In part, I appreciate the pragmatism of Briet's approach. It would certainly make a cataloger's life easier to view documents in this way and, on its surface, it makes a tremendous amount of "sense".

However, I can't help but feel this view is a little too limited. Certainly, it seems to me, the antelope itself would be a source of information. In one way it is an example of what an "antelope" is, but it is also an individual and, beyond that, an individual at a certain snapshot in time.

In a very broad view, we can think that nothing is truly permanent as all things are constantly changing. I think it depends so much on how we observe and questions of time scale.

Human beings are not even exactly what we were in the past. We grow (both physically and in other ways), we change (we age, we change our minds, we change our clothes, we get tattoos, we erase tattoos) and eventually we, as an individual, will cease to exist by any observable means (depending on your belief system) other than by the "things" we leave behind.

We also continue to exist, in a sense, in the minds of those who knew us, but their memories cannot be a whole picture of who we were and certainly no one may know truly how we are inside our own heads. Others will certainly bring their own biases or preferences to their memories of us which may or may not be a complete picture of who we were.

Author response:

Reviewer #1 (Public review):

In this important study, the authors develop a suite of machine vision tools to identify and align fluorescent neuronal recording images in space and time according to neuron identity and position. The authors provide compelling evidence for the speed and utility of these tools. While such tools have been developed in the past (including by the authors), the key advancement here is the speed and broad utility of these new tools. While prior approaches based on steepest descent worked, they required hundreds of hours of computational time, while the new approaches outlined here are >600-fold faster. The machine vision tools here should be immediately useful to readers specifically interested in whole-brain C. elegans data, but also for more general readers who may be interested in using BrainAlignNet for tracking fluorescent neuronal recordings from other systems.

I really enjoyed reading this paper. The authors had several ground truth examples to quantify the accuracy of their algorithms and identified several small caveats users should consider when using these tools. These tools were primarily developed for C. elegans, an animal with stereotyped development, but whose neurons can be variably located due to internal motion of the body. The authors provide several examples of how BrainAlignNet reliably tracked these neurons over space and time. Neuron identity is also important to track, and the authors showed how AutoCellLoader can reliably identify neurons based on their fluorescence in the NeuroPAL background. A challenge with NeuroPAL though, is the high expression of several fluorophores, which compromises behavioral fidelity. The authors provide some possible avenues where this problem can be addressed by expressing fewer fluorophores. While using all four channels provided the best performance, only using the tagRFP and CyOFP channels was sufficient for performance that was close to full performance using all 4 NeuroPAL channels. This result indicates that the development of future lines with less fluorophore expression could be sufficient for reliable neuronal identification, which would decrease the genetic load on the animal, but also open other fluorescent channels that could be used for tracking other fluorescent tools/markers. Even though these tools were developed for C. elegans specifically, they showed BrainAlignNet can be applied to other organisms as well (in their case, the cnidarian C. hemisphaerica), which broadens the utility of their tools.

Strengths:

(1) The authors have a wealth of ground-truth training data to compare their algorithms against, and provide a variety of metrics to assess how well their new tools perform against hand annotation and/or prior algorithms.

(2) For BrainAlignNet, the authors show how this tool can be applied to other organisms besides C. elegans.

(3) The tools are publicly available on GitHub, which includes useful README files and installation guidance.

We thank the reviewer for noting these strengths of our study.

Weaknesses:

(1) Most of the utility of these algorithms is for C. elegans specifically. Testing their algorithms (specifically BrainAlignNet) on more challenging problems, such as whole-brain zebrafish, would have been interesting. This is a very, very minor weakness, though.

We appreciate the reviewer’s point that expanding to additional animal models would be valuable. In the study, we have so far tested our approaches on C. elegans and Jellyfish. Given that this is considered a ‘very, very minor weakness’ and that it does not directly affect the results or analyses in the paper, we think this might be better to address in future work.

(2) The tools are benchmarked against their own prior pipeline, but not against other algorithms written for the same purpose.

We agree that it would be valuable to benchmark other labs’ software pipelines on our datasets. We note that most papers in this area, which describe those pipelines, provide the same performance metrics that we do (accuracy of neuron identification, tracking accuracy, etc), so a crude, first-order comparison can be obtained by comparing the numbers in the papers. But, we agree that a rigorous head-to-head comparison would require applying these different pipelines to a common dataset. We considered performing these analyses, but we were concerned that using other labs’ software ‘off the shelf’ on our data might not represent those pipelines in their best light when compared to our pipeline that was developed with our data in mind. Data from different microscopy platforms can be surprisingly different and we wouldn’t want to perform an analysis that had this bias. Therefore, we feel that this comparison would be best pursued by all of these labs collaboratively (so that they can each provide input on how to run their software optimally). Indeed, this is an important area for future study. In this spirit, we have been sharing our eat-4::GFP datasets (that permit quantification of tracking accuracy) with other labs looking for additional ways to benchmark their tracking software.

We also note that there are not really any pipelines to directly compare against CellDiscoveryNet, as we are not aware of any other fully unsupervised approach for neuron identification in C. elegans.

(3) Considerable pre-processing was done before implementation. Expanding upon this would improve accessibility of these tools to a wider audience.

Indeed, some pre-processing was performed on images before registration and neuron identification -- understanding these nuances can be important. The pre-processing steps are described in the Results section and detailed in the Methods. They are also all available in our open-source software. For BrainAlignNet, the key steps were: (1) selecting image registration problems, (2) cropping, and (3) Euler alignment. Steps (1) and (3) were critically important and are extensively discussed in the Results and Discussion sections of our study (lines 142-144, 218-234, 318-323, 704-712). Step (2) is standard in image processing. For AutoCellLabeler and CellDiscoveryNet, the pre-processing was primarily to align the 4 NeuroPAL color channels to each other (i.e. make sure the blue/red/orange/etc channels for an animal are perfectly aligned). This is also just a standard image processing step to ensure channel alignment. Thus, the more “custom” pre-processing steps were extensively discussed in the study and the more “common” steps are still described in the Methods. The implementation of all steps is available in our open-source software.

Reviewer #2 (Public review):

Summary:

The paper introduced the pipeline to analyze brain imaging of freely moving animals: registering deforming tissues and maintaining consistent cell identities over time. The pipeline consists of three neural networks that are built upon existing models: BrainAlignNet for non-rigid registration, AutoCellLabeler for supervised annotation of over 100 neuronal types, and CellDiscoveryNet for unsupervised discovery of cell identities. The ambition of the work is to enable high-throughput and largely automated pipelines for neuron tracking and labeling in deforming nervous systems.

Strengths:

(1) The paper tackles a timely and difficult problem, offering an end-to-end system rather than isolated modules.

(2) The authors report high performance within their dataset, including single-pixel registration accuracy, nearly complete neuron linking over time, and annotation accuracy that exceeds individual human labelers.

(3) Demonstrations across two organisms suggest the methods could be transferable, and the integration of supervised and unsupervised modules is of practical utility.

We thank the reviewer for noting these strengths of our study.

Weaknesses:

(1) Lack of solid evaluation. Despite strong results on their own data, the work is not benchmarked against existing methods on community datasets, making it hard to evaluate relative performance or generality.

We agree that it would be valuable to benchmark many labs’ software pipelines on some common datasets, ideally from several different research labs. We note that most papers in this area, which describe the other pipelines that have been developed, provide the same performance metrics that we do (accuracy of neuron identification, tracking accuracy, etc), so a crude, first-order comparison can be obtained by comparing the numbers in the papers. But, we agree that a rigorous head-to-head comparison would require applying these different pipelines to a common dataset. We considered performing these analyses, but we were concerned that using other labs’ software ‘off the shelf’ and comparing the results to our pipeline (where we have extensive expertise) might bias the performance metrics in favor of our software. Therefore, we feel that this comparison would be best pursued by all of these labs collaboratively (so that they can each provide input on how to run their software optimally). Indeed, this is an important area for future study. In this spirit, we have been sharing our eat-4::GFP datasets (that permit quantification of tracking accuracy) with other labs looking for additional ways to benchmark their tracking software.

We also note that there are not really any pipelines to directly compare against CellDiscoveryNet, as we are not aware of any other fully unsupervised approach for neuron identification in C. elegans.

(2) Lack of novelty. All three models do not incorporate state-of-the-art advances from the respective fields. BrainAlignNet does not learn from the latest optical flow literature, relying instead on relatively conventional architectures. AutoCellLabeler does not utilize the advanced medNeXt3D architectures for supervised semantic segmentation. CellDiscoveryNet is presented as unsupervised discovery but relies on standard clustering approaches, with limited evaluation on only a small test set.

We appreciate that the machine learning field moves fast. Our goal was not to invent entirely novel machine learning tools, but rather to apply and optimize tools for a set of challenging, unsolved biological problems. We began with the somewhat simpler architectures described in our study and were largely satisfied with their performance. It is conceivable that newer approaches would perhaps lead to even greater accuracy, flexibility, and/or speed. But, oftentimes, simple or classical solutions can adequately resolve specific challenges in biological image processing.

Regarding CellDiscoveryNet, our claim of unsupervised training is precise: CellDiscoveryNet is trained end-to-end only on raw images, with no human annotations, pseudo-labels, external classifiers, or metadata used for training, model selection, or early stopping. The loss is defined entirely from the input data (no label signal). By standard usage in machine learning, this constitutes unsupervised (often termed “self-supervised”) representation learning. Downstream clustering is likewise unsupervised, consuming only image pairs registered by CellDiscoveryNet and neuron segmentations produced by our previously-trained SegmentationNet (which provides no label information).

(3) Lack of robustness. BrainAlignNet requires dataset-specific training and pre-alignment strategies, limiting its plug-and-play use. AutoCellLabeler depends heavily on raw intensity patterns of neurons, making it brittle to pose changes. By contrast, current state-of-the-art methods incorporate spatial deformation atlases or relative spatial relationships, which provide robustness across poses and imaging conditions. More broadly, the ANTSUN 2.0 system depends on numerous manually tuned weights and thresholds, which reduces reproducibility and generalizability beyond curated conditions.

Regarding BrainAlignNet: we agree that we trained on each species’ own data (worm, jellyfish) and we would suggest other labs working on new organisms to do the same based on our current state of knowledge. It would be fantastic if there was an alignment approach that generalized to all possible cases of non-rigid-registration in all animals – an important area for future study. We also agree that pre-alignment was critical in worms and jellyfish, which we discuss extensively in our study (lines 142-144, 318-321, 704-712).

Regarding AutoCellLabeler: the animals were not recorded in any standardized pose and were not aligned to each other beforehand – they were basically in a haphazard mix of poses and we used image augmentation to allow the network to generalize to other poses, as described in our study. It is still possible that AutoCellLabeler is somehow brittle to pose changes (e.g. perhaps extremely curved worms) – while we did not detect this in our analyses, we did not systematically evaluate performance across all possible poses. However, we do note that this network was able to label images taken from freely-moving worms, which by definition exhibit many poses (Figure 5D, lines 500-525); aggregating the network’s performance across freely-moving data points allowed it to nearly match its performance on high-SNR immobilized data. This suggests a degree of robustness of the AutoCellLabeler network to pose changes.

Regarding ANTSUN 2.0: we agree that there are some hyperparameters (described in our study) that affect ANTSUN performance. We agree that it would be worthwhile to fully automate setting these in future iterations of the software.

Evaluation:

To make the evaluation more solid, it would be great for the authors to (1) apply the new method on existing datasets and (2) apply baseline methods on their own datasets. Otherwise, without comparison, it is unclear if the proposed method is better or not. The following papers have public challenging tracking data: https://elifesciences.org/articles/66410, https://elifesciences.org/articles/59187, https://www.nature.com/articles/s41592-023-02096-3.

Please see our response to your point (1) under Weaknesses above.

Methodology:

(1) The model innovations appear incrementally novel relative to existing work. The authors should articulate what is fundamentally different (architectural choices, training objectives, inductive biases) and why those differences matter empirically. Ablations isolating each design choice would help.

There are other efforts in the literature to solve the neuron tracking and neuron identification problems in C. elegans (please see paragraphs 4 and 5 of our Introduction, which are devoted to describing these). However, they are quite different in the approaches that they use, compared to our study. For example, for neuron tracking they use t->t+1 methods, or model neurons as point clouds, etc (a variety of approaches have been tried). For neuron identification, they work on extracted features from images, or use statistical approaches rather than deep neural networks, etc (a variety of approaches have been tried). Our assessment is that each of these diverse approaches has strengths and drawbacks; we agree that a meta-analysis of the design choices used across studies could be valuable.

We also note that there are not really any pipelines to directly compare against CellDiscoveryNet, as we are not aware of any other fully unsupervised approach for neuron identification in C. elegans.

(2) The pipeline currently depends on numerous manually set hyperparameters and dataset-specific preprocessing. Please provide principled guidelines (e.g., ranges, default settings, heuristics) and a robustness analysis (sweeps, sensitivity curves) to show how performance varies with these choices across datasets; wherever possible, learn weights from data or replace fixed thresholds with data-driven criteria.

We agree that there are some ANTSUN 2.0 hyperparameters (described in our Methods section) that could affect the quality of neuron tracking. It would be worthwhile to fully automate setting these in future iterations of the software, ensuring that the hyperparameter settings are robust to variation in data/experiments.

Appraisal:

The authors partially achieve their aims. Within the scope of their dataset, the pipeline demonstrates impressive performance and clear practical value. However, the absence of comparisons with state-of-the-art algorithms such as ZephIR, fDNC, or WormID, combined with small-scale evaluation (e.g., ten test volumes), makes the strength of evidence incomplete. The results support the conclusion that the approach is useful for their lab's workflow, but they do not establish broader robustness or superiority over existing methods.

We wish to remind the reviewer that we developed BrainAlignNet for use in worms and jellyfish. These two animals have different distributions of neurons and radically different anatomy and movement patterns. Data from the two organisms was collected in different labs (Flavell lab, Weissbourd lab) on different types of microscopes (spinning disk, epifluorescence). We believe that this is a good initial demonstration that the approach has robustness across different settings.

Regarding comparisons to other labs’ C. elegans data processing pipelines, we agree that it will be extremely valuable to compare performance on common datasets, ideally collected in multiple different research labs. But we believe this should be performed collaboratively so that all software can be utilized in their best light with input from each lab, as described above. We agree that such a comparison would be very valuable.

Impact:

Even though the authors have released code, the pipeline requires heavy pre- and post-processing with numerous manually tuned hyperparameters, which limits its practical applicability to new datasets. Indeed, even within the paper, BrainAlignNet had to be adapted with additional preprocessing to handle the jellyfish data. The broader impact of the work will depend on systematic benchmarking against community datasets and comparison with established methods. As such, readers should view the results as a promising proof of concept rather than a definitive standard for imaging in deformable nervous systems.

Regarding worms vs jellyfish pre-processing: we actually had the exact opposite reaction to that of the reviewer. We were surprised at how similar the pre-processing was for these two very different organisms. In both cases, it was essential to (1) select appropriate registration problems to be solved; and (2) perform initialization with Euler alignment. Provided that these two challenges were solved, BrainAlignNet mostly took care of the rest. This suggests a clear path for researchers who wish to use this approach in another animal. Nevertheless, we also agree with the reviewer’s caution that a totally different use case could require some re-thinking or re-strategizing. For example, the strategy of how to select good registration problems could depend on the form of the animal’s movement.

Reviewer #3 (Public review):

Context:

Tracking cell trajectories in deformable organs, such as the head neurons of freely moving C. elegans, is a challenging task due to rapid, non-rigid cellular motion. Similarly, identifying neuron types in the worm brain is difficult because of high inter-individual variability in cell positions.

Summary:

In this study, the authors developed a deep learning-based approach for cell tracking and identification in deformable neuronal images. Several different CNN models were trained to: (1) register image pairs without severe deformation, and then track cells across continuous image sequences using multiple registration results combined with clustering strategies; (2) predict neuron IDs from multicolor-labeled images; and (3) perform clustering across multiple multicolor images to automatically generate neuron IDs.

Strengths:

Directly using raw images for registration and identification simplifies the analysis pipeline, but it is also a challenging task since CNN architectures often struggle to capture spatial relationships between distant cells. Surprisingly, the authors report very high accuracy across all tasks. For example, the tracking of head neurons in freely moving worms reportedly reached 99.6% accuracy, neuron identification achieved 98%, and automatic classification achieved 93% compared to human annotations.

We thank the reviewer for noting these strengths of our study.

Weaknesses:

(1) The deep networks proposed in this study for registration and neuron identification require dataset-specific training, due to variations in imaging conditions across different laboratories. This, in turn, demands a large amount of manually or semi-manually annotated training data, including cell centroid correspondences and cell identity labels, which reduces the overall practicality and scalability of the method.

We performed dataset-specific training for image registration and neuron identification, and we would encourage new users to do the same based on our current state of knowledge. This highlights how standardization of whole-brain imaging data across labs is an important issue for our field to address and that, without it, variations in imaging conditions could impact software utility. We refer the reviewer to an excellent study by Sprague et al. (2025) on this topic, which is cited in our study.

However, at the same time, we wish to note that it was actually reasonably straightforward to take the BrainAlignNet approach that we initially developed in C. elegans and apply it to jellyfish. Some of the key lessons that we learned in C. elegans generalized: in both cases, it was critical to select the right registration problems to solve and to preprocess with Euler registration for good initialization. Provided that those problems were solved, BrainAlignNet could be applied to obtain high-quality registration and trace extraction. Thus, our study provides clear suggestions on how to use these tools across multiple contexts.

(2) The cell tracking accuracy was not rigorously validated, but rather estimated using a biased and coarse approach. Specifically, the accuracy was assessed based on the stability of GFP signals in the eat-4-labeled channel. A tracking error was assumed to occur when the GFP signal switched between eat-4-negative and eat-4-positive at a given time point. However, this estimation is imprecise and only captures a small subset of all potential errors. Although the authors introduced a correction factor to approximate the true error rate, the validity of this correction relies on the assumption that eat-4 neurons are uniformly distributed across the brain - a condition that is unlikely to hold.

We respectfully disagree with this critique. We considered the alternative suggested by the reviewer (in their private comments to the authors) of comparing against a manually annotated dataset. But this annotation would require manually linking ~150 neurons across ~1600 timepoints, which would require humans to manually link neurons across timepoints >200,000 times for a single dataset. These datasets consist of densely packed neurons rapidly deforming over time in all 3 dimensions. Moreover, a single error in linking would propagate across timepoints, so the error tolerance of such annotation would be extremely low. Any such manually labeled dataset would be fraught with errors and should not be trusted. Instead, our approach relies on a simple, accurate assumption: GFP expression in a neuron should be roughly constant over a 16min recording (after bleach correction) and the levels will be different in different neurons when it is sparsely expressed. Because all image alignment is done in the red channel, the pipeline never “peeks” at the GFP until it is finished with neuron alignment and tracking. The eat-4 promoter was chosen for GFP expression because (a) the nuclei labeled by it are scattered across the neuropil in a roughly salt-and-pepper fashion – a mixture of eat-4-positive and eat-4-negative neurons are found throughout the head; and (b) it is in roughly 40% of the neurons, giving very good overall coverage. Our view is that this approach of labeling subsets of neurons with GFP should become the standard in the field for assessing tracking accuracy – it has a simple, accurate premise; is not susceptible to human labeling error; is straightforward to implement; and, since it does not require manual labeling, is easy to scale to multiple datasets. We do note that it could be further strengthened by using multiple strains each with different ‘salt-and-pepper’ GFP expression patterns.

(3) Figure S1F demonstrates that the registration network, BrainAlignNet, alone is insufficient to accurately align arbitrary pairs of C. elegans head images. The high tracking accuracy reported is largely due to the use of a carefully designed registration sequence, matching only images with similar postures, and an effective clustering algorithm. Although the authors address this point in the Discussion section, the abstract may give the misleading impression that the network itself is solely responsible for the observed accuracy.

Our tracking accuracy requires (a) a careful selection of registration problems, (b) highly accurate registration of the selected registration problems, and (c) effective clustering. We extensively discussed the importance of the choosing of the registration problems in the Results section (lines 218-234 and 318-321), Discussion section (lines 704-708), and Methods section (955-970 and 1246-1250) of our paper. We also discussed the clustering aspect in the Results section (lines 247-259), Discussion section (lines 708-712), and Methods section (lines 1162-1206). In addition, our abstract states that the BrainAlignNet needs to be “incorporated into an image analysis pipeline,” to inform readers that other aspects of image analysis need to occur (beyond BrainAlignNet) to perform tracking.

(4) The reported accuracy for neuron identification and automatic classification may be misleading, as it was assessed only on a subset of neurons labeled as "high-confidence" by human annotators. Although the authors did not disclose the exact proportion, various descriptions (such as Figure 4f) imply that this subset comprises approximately 60% of all neurons. While excluding uncertain labels is justifiable, the authors highlight the high accuracy achieved on this subset without clearly clarifying that the reported performance pertains only to neurons that are relatively easy to identify. Furthermore, they do not report what fraction of the total neuron population can be accurately identified using their methods-an omission of critical importance for prospective users.

The reviewer raises two points here: (1) whether AutoCellLabeler accuracy is impacted by ease of human labeling; and (2) what fraction of total neurons are identified. We address them one at a time.

Regarding (1), we believe that the reviewer overlooked an important analysis in our study. Indeed, to assess its performance, one can only compare AutoCellLabeler’s output against accurate human labels – there is simply no way around it. However, we noted that AutoCellLabeler was identifying some neurons with high confidence even when humans had low confidence or had not even tried to label the neurons (Fig. 4F). To test whether these were in fact accurate labels, we asked additional human labelers to spend extra time trying to label a random subset of these neurons (they were of course blinded to the AutoCellLabeler label). We then assessed the accuracy of AutoCellLabeler against these new human labels and found that they were highly accurate (Fig. 4H). This suggests that AutoCellLabeler has strong performance even when some human labelers find it challenging to label a neuron. However, we agree that we have not yet been able to quantify AutoCellLabeler performance on the small set of neuron classes that humans are unable to identify across datasets.

Regarding (2), we agree that knowing how many neurons are labeled by AutoCellLabeler is critical. For example, labeling only 3 neurons per animal with 100% accuracy isn’t very helpful. We wish to emphasize that we did not omit this information: we reported the number of neurons labeled for every network that we characterized in the study, alongside the accuracy of those labels (please see Figures 4I, 5A, and 6G; Figure 4I also shows the number of human labels per dataset, which the reviewer requested). We also showed curves depicting the tradeoff between accuracy and number of neurons labeled, which fully captures how we balanced accuracy and number of neurons labeled (Figures 5D and S4A). It sounds like the reviewer also wanted to know the total number of recorded neurons. The typical number of recorded neurons per dataset can also be found in the paper in Fig. 2E.

Reviewer #1 (Public review):

Summary:

This study focuses on characterizing the EEG correlates of item-specific proportion congruency effects. In particular, two types of learned associations are characterized. One being associations between stimulus features and control states (SC), and the other being stimulus features and responses (SR). Decoding methods are used to identify SC and SR correlates and to determine whether they have similar topographies and dynamics.

The results suggest SC and SR associations are simultaneously coactivated and have shared topographies, with the inference being that these associations may share a common generator.

Strengths:

Fearless, creative use of EEG decoding to test tricky hypotheses regarding latent associations.

Nice idea to orthogonalize the ISPC condition (MC/MI) from stimulus features.

Weaknesses:

(1) I'm relatively concerned that these results may be spurious. I hope to be proven wrong, but I would suggest taking another look at a few things.

While a nice idea in principle, the ISPC manipulation seems to be quite confounded with the trial number. E.g., color-red is MI only during phase 2, and is MC primarily only during Phase 3 (since phase 1 is so sparsely represented). In my experience, EEG noise is highly structured across a session and easily exploited by decoders. Plus, behavior seems quite different between Phase 2 and Phase 3. So, it seems likely that the classes you are asking the decoder to separate are highly confounded with temporally structured noise.

I suggest thinking of how to handle this concern in a rigorous way. A compelling way to address this would be to perform "cross-phase" decoding, however I am not sure if that is possible given the design.

The time courses also seem concerning. What are we to make of the SR and SC timecourses, which have aggregate decoding dynamics that look to be <1Hz?

Some sanity checks would be one place to start. Time courses were baselined, but this is often not necessary with decoding; it can cause bias (10.1016/j.jneumeth.2021.109080), and can mask deeper issues. What do things look like when not baselined? Can variables be decoded when they should not be decoded? What does cross-temporal decoding look like - everything stable across all times, etc.?

(2) The nature of the shared features between SR and SC subspaces is unclear.

The simulation is framed in terms of the amount of overlap, revealing the number of shared dimensions between subspaces. In reality, it seems like it's closer to 'proportion of volume shared', i.e., a small number of dominant dimensions could drive a large degree of alignment between subspaces.

What features drive the similarity? What features drive the distinctions between SR and SC? Aside from the temporal confounds I mentioned above, is it possible that some low-dimensional feature, like EEG congruency effect (e.g., low-D ERPs associated with conflict), or RT dynamics, drives discriminability among these classes? It seems plausible to me - all one would need is non-homogeneity in the size of the congruency effect across different items (subject-level idiosyncracies could contribute: 10.1016/j.neuroimage.2013.03.039).

(3) The time-resolved within-trial correlation of RSA betas is a cool idea, but I am concerned it is biased. Estimating correlations among different coefficients from the same GLM design matrix is, in general, biased, i.e., when the regressors are non-orthogonal. This bias comes from the expected covariance of the betas and is discussed in detail here (10.1371/journal.pcbi.1006299). In short, correlations could be inflated due to a combination of the design matrix and the structure of the noise. The most established solution, to cross-validate across different GLM estimations, is unfortunately not available here. I would suggest that the authors think of ways to handle this issue.

(4) Are results robust to running response-locked analyses? Especially the EEG-behavior correlation. Could this be driven by different RTs across trials & trial-types? I.e., at 400 ms post-stim onset, some trials would be near or at RT/action execution, while others may not be nearly as close, and so EEG features would differ & "predict" RT.

(5) I suggest providing more explanation about the logic of the subspace decoding method - what trialtypes exactly constitute the different classes, why we would expect this method to capture something useful regarding ISPC, & what this something might be. I felt that the first paragraph of the results breezes by a lot of important logic.

In general, this paper does not seem to be written for readers who are unfamiliar with this particular topic area. If authors think this is undesirable, I would suggest altering the text.

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

1. General Statements

We thank the reviewers for providing thoughtful and constructive feedback, which will help us improve the clarity and rigor of the paper. On balance, the reviews were positive. Reviewer 1 mentioned that “This is a strong manuscript with few problems and all important findings well justified, indeed this is a nicely polished…..high-quality manuscript,” and that “this paper makes a major breakthrough, showing that cell autonomous defects in hTSCs are very likely at the heart of the pathology observed in GIN-prone murine mutants.” Reviewer 3 stated that “The study is well designed, and the manuscript is very well written. The conclusions are supported by the evidence presented.” Reviewer 2 was less enthusiastic, with main concerns being that “The paper is mostly descriptive and often quite confusing leaving one not much closer to understanding the mechanistic basis for the interesting sex-biased semi-lethal phenotype.” and felt that figure titles/section headers overstated the results, and finally recommended to improve some technical aspects and tempering conclusions. The proposed edits we think address most issues raised by the reviewers either with re-writing or adding data as described below.

In response to reviewer #1 comments:

Major comments:

• I am confused as to the basis of the sex-skewing phenomenon? Is the problem that lack of maternally loaded WT Mcm4 worsens the phenotype, or is the issue that Mcm4C3/C3 dams are less able to retain pregnancies, perhaps being a more inflammatory environment? Also, while there quite consistent evidence for reduced viability of Mcm4C3/C3McmGt/+ progeny, especially for female progeny, how confident can we be that the genotype of the dam vs. sire is important? Notably on a Ddx58 background, the progeny of the Mcm4C3/C3 sire included seven live male Mcm4C3/C3McmGt/+ but no female.

Regarding the first point (sex skewing only when female is C3/C3), we also suspected either: 1) the maternal uterine environment, or 2) reduced oocyte quality. Although not reported in this manuscript, we tested #1 by performing embryo transfer experiments. Transferring 2-cell stage embryos from sex-skewing mating to WT females did not rescue the sex-bias. We then examined oocytes from C3/C3 females. We found evidence for compromised mitochondria and transcriptome disruption. However, we are not sure why this happens (poor follicle support? Oocyte intrinsic phenomenon?). We are reserving these results and additional experiments for another paper, especially since this one mainly deals with GIN and placenta development. If the reviewers feel strongly that the embryo transfer data is crucial, we can include it.

Regarding how confident we are that the genotype of the dam vs. sire is important, this stems from our previous paper by McNairn et al 2019 (the percentage of female C3/C3 M2/+ from sex-skewing mating is 20% compared to 60% from the reciprocal mating), which was quite dramatic. Consistent with this, MCM levels were significantly reduced in the placentae only when the dam was C3/C3 and the sire C3/+ M2/+, but not in the reciprocal cross. The reviewer makes a good observation about the Ddx58 cross; we can only hypothesize that the mutation somehow sensitizes females in this scenario and will make mention of it in the revision. We also realize that we neglected to write in Methods that the Ddx58 allele was coisogenic in the C3H background.

• I'm not sure what Supplementary Figure 6 is showing (faster differentiation of C3 but less TGC?). Regardless, it's hard to draw too much conclusion from one not-very-pretty Western blot. This figure requires both additional replicates and a better explanation of how it fits with the other conclusions of the paper..

We hypothesized that the JZ defect observed in the semi-lethal genotype placentas could arise either from impaired maintenance of the progenitor pool or from reduced capacity of mutant trophoblast progenitors to differentiate into the JZ lineage. The blot in Supplementary Figure 6 was intended as a qualitative demonstration that mutant trophoblast stem cells can differentiate into JZ lineages. We recognize that the figure is not definitive and will revise the text to clarify its purpose. A replicate(s) of the Western will be performed as suggested.

• Supplementary Figure 7F-G is puzzling. Half of the mESCs have gamma-H2AX at all times, including most in S or G2 phase? In Figure S7E, do the quadrants correspond to being negative or positive for gamma-H2AX? At very least, IF images showing clear gamma-H2AX foci would be much more convincing.

The gates for γH2AX FACS analysis were established using negative controls lacking primary antibody. As reported previously, embryonic stem cells display high basal levels of γH2AX staining (Chuykin et al., Cell Cycle 2008; Turinetto et al., Stem Cells 2012; Ahuja et al., Nat Comm 2016), which likely explains the broad signal observed across cell cycle phases. Regardless, we will provide immunofluorescence staining of γH2Ax and foci count in our revision.

• The methods section is well detailed, but it would be ideal to clarify how many replicates each Western Blot or flow cytometry experiment is representative of.

Thanks for the suggestion. We will update this for Fig4 and Fig5.

Minor comments:

• Is it possible that cGAS-STING and RIG pathways act redundantly to cause inflammation and lethality, or that other innate immune components are involved? I don't expect the authors to make compound mutants to test this but at least this possibility should be discussed textually.

We appreciate the reviewer’s point, and had the same suspicion. Supporting this, we will add new RNA-seq analysis of Tmem173 KO placentas revealed elevated inflammatory gene expression compared to C3/C3 M2/+ controls, consistent with potential redundancy or feedback regulation. We will update in supplementary figures to reflect this.

In response to reviewer #2 comments:

Major comments:

A major concern throughout the paper is that conclusions are often overstating their data. The title of figure 2 is "placentae with replication stress have smaller junctional and labyrinth zones". However, there is no measure of replication stress in this figure, just a histological evaluation of the placentae from the different mutants. The title of figure 3 is "Impact of GIN on LZ is less than JZ," but there is no measure of GIN, but instead measurement of number of cells in cell cycle and some bulk RNA-seq analysis. Title of figure 4 is "TSCs with increased genomic instability exhibit abnormal phenotypes." Again there is no measure of GIN, but instead staining of derived TSCs for proliferation, cell death, and a TSC marker. Title of figure 5 is "DNA damage responses and G2/M checkpoint activation drive premature TSC differentiation." However, there does not appear to be a difference in gH2AX between the two mutant genotypes. Checkpoint proteins might be up, but need quantification and reproduction. > 4C is the only marker of differentiation. Importantly, all the analyses here are associations, not connections, so cannot use the word "drive". Similar issues can be raised with a number of the supplementary figures.

The Chaos3 (chromosome aberrations occurring spontaneously 3) model is a well-established system of intrinsic chronic replication stress and GIN. It is characterized by ~20 fold elevation of blood micronuclei (Shima et al., Nature 2007), a hallmark of GIN (Soxena et al., Mol Cell 2022); a destabilized MCM2-7 helicase prone to replication fork collapse (Bai et al., PLoS Genet 2016); and increased mitotic chromosome abnormalities and decreased dormant origins (Kawabata et al., Mol Cell 2011; Chuang et al., Nucleic Acid Res 2012) that are known to cause GIN and replication stress (Ibarra et al., PNAS 2008 ). Also, in our previous work (McNairn et al Nature 2019), we showed that placentae from C3/C3 dams exhibit significantly elevated γH2Ax as well as reduced MCM2 and MCM4 protein levels. In our current study, we also observe elevated γH2Ax in mutant TSCs (C3/C3 and C3/C3 M2/+), consistent with genomic instability. Nevertheless, we acknowledge that in TSCs, we did not formally demonstrate replications stress(RS), so where appropriate, we will advise figure titles, for example to say that “cells/placentae with a GIN or RS genotype.”

We acknowledge the reviewers concern regarding western blots. We will provide quantification and statistics in our revision.

1) A deeper analysis of the cell lines is likely to be the most fruitful path to reveal interesting mechanisms. It is very surprising that there is no phenotype in ESCs. Authors should check for increased apoptosis. Maybe the phenotypic cells are lost. Or do ESCs use different MCMs/mechanisms of DNA replication or are they better able to handle replication stress and GIN? How many passages were the TSCs and ESCs cultured for? Does GIN (i.e. aneuploidy, CNVs) develop in TSCs and ESCs with passaging? How do the MCM mutations impact the molecular identity of the ESC and TSC cells including their heterogeneity in the population.

We assessed apoptosis using cleaved caspase 3 flow cytometry in mutant ESCs and observed no difference compared to controls (we will add this data as Supplementary Fig. 7).

We believe there are intrinsic differences in TSCs and ESCs in their ability to respond to and counteract replication stress and DNA damage. ESCs are known to license more replication origins than somatic cells at a higher rate, which protects them from short G1-induced replication stress (Ahuja et al., Nat Comm 2016; Ge et al., Stem Cell Rep 2015; Matson et al., eLife 2017). Human placental cells physiologically exhibit high levels of mutation rate and chromosomal instability in vivo (Coorens et al., Nature 2021). Supporting this, Wang, D., et al (Nat Comm 2025) reported that several cell cycle and DDR regulators are differentially expressed in human TSCs vs human pluripotent stem cells. Whether such transcriptional differences directly contribute to functional outcomes remains to be determined.

All experiments in this study were conducted using early-passage ESCs and TSCs (i.e. Finally, we showed that close to 90% mutant ESCs are KLF4+ (a naive pluripotency marker) whereas EOMES+ cells were significantly reduced in TSCs carrying the GIN genotype (Fig. 4E–F and Supplementary Fig. 7), highlighting lineage-specific differences.

Minor Comments:

1) There is a lack of quantification and repeats for all Westerns. At minimum there should be three repeats for each experiment, quantification including normalization to a reference protein, and stats confirming any proposed differences between conditions.

We will update our revision with quantification and statistics for western blots.

2) I would recommend moving the results in supp table 1 to figure 1. While negative, they are the newer results. The results shown in current figure 1 are essentially a reproduction of their previous work.

The placental observations presented in Fig.1 are new. In particular, the placental and embryonic weight measurements graphed in Fig1B and C have not been published by our group. Fig1A reproduces our previous observation on embryo viability in GIN mutants (McNairn et al., Nature 2019), while the schematic was provided for better flow and readability given the complex mating schemes. We are agnostic on the Suppl Table 1. It could be changed to a new Table 1 in the main section depending on the journal.

In response to reviewer #3 comments:

Major Comments

While the inclusion of bulk RNAseq data of whole placental tissue is appreciated, the interpretation of the results is somewhat problematic, as it is acknowledged that the cell type composition of the placentas is drastically different between groups. Making conclusions based upon GSEA analysis of two different groups with drastically different cell type composition is somewhat misleading, as based on the results, it is a direct reflection of the cell types present. It would be more helpful to perform cell type deconvolution of the RNAseq data to estimate the proportion of each cell type within the bulk samples and compare that to what is seen histologically and not dive too deeply into the pathways since the results could just be a reflection of the cell types e.g. angiogenesis pathways from more endothelial cells. Additionally, the RNAseq data can be leveraged to look at expression of inflammatory genes by sex, which may show interesting patterns based on the other results.

We agree that the representation of cell types in the placenta is problematic especially for underrepresented genes. We propose to use the BayesPrism tool (Chu et al., Nat Cancer 2022) to deconvolute bulk RNA-seq for better representation of transcriptional changes in the placenta.

Section: GIN impairs trophoblast stem cell establishment and maintenance. To support the assertion in the first paragraph, beyond measuring apoptosis, it would be helpful at this stage to look at RNA expression levels indicative of the activation of DNA damage checkpoint genes

We have performed RNA-seq on mutant ESC and TSCs and are in the process of data analysis. We will update these results in the revision.

Please include additional methodological details in the methods section on the statistical analysis done for differential expression analysis. Specifically, what type of normalization was used, if lowly expressed genes were filtered out and at what cutoff, what statistical model was used (did you include covariates?), what comparisons were made? Did you stratify by sex? What cutoff was used for statistical significance? Did you perform multiple testing correction?

We will update RNA-Seq data analysis methods in our full revision.

2. Description of the revisions that have already been incorporated in the transferred manuscript

Reviewer #1 comments:

• Supplementary Table 1. would be enhanced greatly showing comparable tables for Mcm4C3/C3 x Mcm4C3/+McmGt/+ in mice without the Tmem173 or Ddx58 mutations. It is fine to recycle data from McNairn 2019 here, as long as the source is indicated, but a comparison is needed.

Thanks for pointing this out. We have updated this suggestion in Supp table 1.

• In Figure S3E-F, is the box above each graph supposed to show the genotype of the dam?

Yes. Thanks for pointing this out. We have added a description in the figure legend to make it clear.

• "Indeed, the placenta and embryo weights of E13.5 Mcm4C3/C3 Mcm2Gt/+ Mcm3Gt/+ animals were significantly improved vs. Mcm4C3/C3 Mcm2Gt/+ animals, rendering them similar to Mcm4C3/C3 littermates (Fig. 6A-C). The JZ (but not LZ) area in Mcm4C3/C3 Mcm2Gt/+ Mcm3Gt/+ placentae also increased to the level of Mcm4C3/C3 littermates (Fig. 6D-H)." There are two problems here. First, the figure calls are wrong. Second, the description of the data is not quite right, it looks like the C3/C3 and C3/C3 M2/+ M3/+ LZs are a similar size to each and are statistically indistinguishable.

Thanks for catching this. We have updated these in the main text.

*Reviewer #2 comments: *

Minor comment

• Need to review citations to figures. For example, no citations are made to figure 4a and 4c.

Thanks for catching this. We have updated the text.

Reviewer #3 comments:

Define the first use of >4C DNA content to help readers understand this potentially unfamiliar term.

We have edited this part to indicate cells with more than 4C DNA content for better clarity.

iDEP tool - please include citation to manuscript instead of link

We have updated this citation.

Check citations. Some citations to BioRxiv that are now published e.g. 13.

We have updated this citation.

3. Description of analyses that authors prefer not to carry out

Reviewer 2

2) Along similar lines, most of the in vivo phenotypic analyses are performed at E13.5, long after defects are likely beginning to express themselves especially given that they see phenotypes in the TSCs, which represent the polar TE of a E4.5. To understand the primary defects of the in vivo phenotype, they should be looking much earlier. Supplemental figure 5 is a start but represents a rather superficial analysis.

The peri-implantation period, namely E4.5, represents a “black box” of embryonic development given that this is a critical stage for implantation. Aside from being an extremely difficult stage to analyze technically, we don’t think it is essential to the conclusions (or doable in a timely manner), especially given the use of TSCs. If we complete EdU studies on E6.5 embryos, we will include them.

3) Fig. 6 would benefit from evidence that MCM3 mutant is rescuing MCM4 levels in the chromatin fraction of cells and the DNA damage phenotype.

The genetic evidence presented is strong, and although we didn’t do the suggested experiment, we feel that our previous studies (McNairn et al., Nature 2019 and Chuang et al., PLoS Genet 2010) on the effects of MCM3 as a nuclear export factor (as it is in yeast (Liku et al., Mol Biol Cell 2005)) are a reasonable basis for not repeating such experiments. Furthermore, we are no longer maintaining the Mcm3 line and it would take over a year to reconstitute and rebreed triple mutants.

Reviewer #3 (Public review):

Summary:

Lmx1a is an orthologue of apterous in flies, which is important for dorsal-ventral border formation in the wing disc. Previously, this research group has described the importance of the chicken Lmx1b in establishing the boundary between sensory and non-sensory domains in the chicken inner ear. Here, the authors described a series of cellular changes during border formation in the chicken inner ear, including alignment of cells at the apical border and concomitant constriction basally. The authors extended these observations to the mouse inner ear and showed that these morphological changes occurred at the border of Lmx1a positive and negative regions, and these changes failed to develop in Lmx1a mutants. Furthermore, the authors demonstrated that the ROCK-dependent actomyosin contractility is important for this border formation and blocking ROCK function affected epithelial basal constriction and border formation in both in vitro and in vivo systems.

Strengths:

The morphological changes described during border formation in the developing inner ear are interesting. Linking these changes to the function of Lmx1a and ROCK dependent actomyosin contractile function are provocative.

Weaknesses:

There are several outstanding issues that need to be clarified before one can pin the morphological changes observed being causal to border formation and that Lmx1a and ROCK are involved.

Comments on the latest version:

The revised manuscript has provided clarity of their results on some levels, but unfortunately, the basal restriction during border formation remains unclear and the study did not advance the understanding of role of Lmx1a in boundary formation. Overall comments are indicated below:

(1) The authors states in the rebuttal, "we do not think that ROCK activity is required for the formation or maintenance of the basal constriction at the interface of Lmx1a-expressing and non-expressing cells"<br /> If the above is the sentiment of the authors, then the manuscript is not written to support this sentiment clearly, starting with this misleading sentence in the Abstract, "The boundary domain is absent in Lmx1a-deficient mice, which exhibit defects in sensory organ segregation, and is disrupted by the inhibition of ROCK-dependent actomyosin contractility."

(2) As acknowledged by the authors, the data as they currently stand could be explained by Lmx1a functioning in specifying the non-sensory fate and may not function directly in boundary formation. With this caveat in mind, the role of Lmx1a in boundary formation remains unclear.

(3) I feel like the word "orchestrate" in the title is an overstatement.

Author response:

The following is the authors’ response to the original reviews

Public Reviews:

Reviewer #1 (Public Review):

Summary:

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

Strengths:

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

Weaknesses:

The methodology, although standard, lacks quantification. This includes the mass spectrometry data , along with the cytology. The work would also benefit from clarifying the role of the DSB machinery on the X chromosome versus the autosomes.

• We have uploaded the MS data and added a summary table with the number of peptides and coverage.

• We have added statistics to the comparisons of DAPI body counts.

• We have provided additional images of the change in HIM-5 localization

• We have quantified the overlap (or lack thereof) between XND-1 and HIM-17 and the DNA axis

Reviewer #2 (Public Review):

Summary:

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

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

Weaknesses:

This work relies heavily on Y2H, which is notorious for having high rates of false positives and false negatives. Although the interactions between HIM-17 and XND-1 and between DSB-1 and HIM-5 were validated by co-IP, the significance of these interactions was not tested, and cataloging Y2H interactions does not yield much more insight.

We appreciate that the reviewer recognized the value of our IP data, but we beg to differ that we rely too heavily on the Y2H. We also provide genetic analysis on bivalent formation to support the physical interaction data. We do acknowledge that there are caveats with Y2H, however, including that a subset of the interactions can only be examined with proteins in one orientation due to auto-activation. While we acknowledge that it would be nice to have IP data for all of the proteins using CRISPR-tagged, functional alleles, these strains are not all feasible (e.g. no functional rec-1 tag has been made) and are beyond the scope of the current work.

Moreover, most experiments lack rigor, which raises serious concerns about whether the data convincingly supports the conclusions of this paper. For instance, the XND-1 antibody appears to detect a band in the control IP; however, there was no mention of the specificity of this antibody.

We previously showed the specificity of this antibody in its original publication showing lack of staining in the xnd-1 mutant by IF (Wagner et al., 2010). To further address this, however, we have now included a new supplementary figure (Figure S1) demonstrating the specificity of the XND-1 antibody by Western blot. The antibody detects a distinct band in extracts from wild-type (N2) worms, but this band is absent in two independent xnd-1 mutant strains. This confirms that the antibody specifically recognizes XND-1, supporting the validity of the IP results shown in the main figures.

Additionally, epistasis analysis of various genetic mutants is based on the quantification of DAPI bodies in diakinesis oocytes, but the comparisons were made without statistical analyses.

We have added statistical analysis to all datasets where quantification was possible, strengthening the rigor and interpretation of our findings.

For cytological data, a single representative nucleus was shown without quantification and rigorous analysis. The rationale for some experiments is also questionable (e.g. the rescue by dsb-2 mutants by him-5 transgenes in Figure 2), making the interpretation of the data unclear. Overall, while this paper claims to present "the first comprehensive model of DSB regulation in a metazoan", cataloging Y2H and genetic interactions did not yield any new insights into DSB formation without rigorous testing of their significance in vivo. The model proposed in Figure 4 is also highly speculative.

Regarding the cytology, we provide new images and quantification of HIM-17 and XND-1 overlap with the DNA axes. We also added full germ line images showing HIM-5 localization in wild type and dsb-1 mutants, to provide a more complete and representative view of the observed phenotype. To further support our findings, we’ve also included images demonstrating that this phenotype is consistently observed with both in live worm with the the him-5::GFP transgene and in fixed worms with an endogenously tagged version of HIM-5.

Reviewer #3 (Public Review):

During meiosis in sexually reproducing organisms, double-strand breaks are induced by a topoisomerase-related enzyme, Spo11, which is essential for homologous recombination, which in turn is required for accurate chromosome segregation. Additional factors control the number and genome-wide distribution of breaks, but the mechanisms that determine both the frequency and preferred location of meiotic DSBs remain only partially understood in any organism.

The manuscript presents a variety of different analyses that include variable subsets of putative DSB factors. It would be much easier to follow if the analyses had been more systematically applied. It is perplexing that several factors known to be essential for DSB formation (e.g., cohesins, HORMA proteins) are excluded from this analysis, while it includes several others that probably do not directly contribute to DSB formation (XND-1, HIM-17, CEP-1, and PARG-1).

We respectfully disagree with the reviewer’s statement regarding the selection of factors included in our analysis. In this work, our focus was specifically on SPO-11 accessory factors — proteins that directly interact with or regulate SPO-11 activity during doublestrand break formation. Cohesins and chromosome axis proteins (such as the HORMA domain proteins) are essential for establishing the correct chromosome architecture that supports DSB formation, but there is no evidence that they are direct accessory factors of SPO-11. Therefore, they were intentionally excluded from this study to maintain a clear and focused scope on proteins that more directly modulate SPO-11 function.

Conversely, XND-1, HIM-17, CEP-1, and PARG-1 have all been implicated in regulating aspects of SPO-11-mediated DSB formation or its immediate environment. Although their contributions mayinvolve broader chromatin or DNA damage response regulation, prior literature supports their inclusion as relevant modulators of SPO-11 activity, justifying their analysis within the context of this work.

The strongest claims seem to be that "HIM-5 is the determinant of X-chromosome-specific crossovers" and "HIM-5 coordinates the actions of the different accessory factors subgroups." Prior work had already shown that mutations in him-5 preferentially reduce meiotic DSBs on the X chromosome. While it is possible that HIM-5 plays a direct role in DSB induction on the X chromosome, the evidence presented here does not strongly support this conclusion. It is also difficult to reconcile this idea with evidence from prior studies that him-5 mutations predominantly prevent DSB formation on the sex chromosomes, while the protein localizes to autosomes.

HIM-5 is not the only protein that is autosomally enriched but preferentially affects the X chromosome: MES-4 and MRG-1 are both autosomally-enriched but influence silencing of the X chromosome. While HIM-5 appears autosomally-enriched, it does not appear to be autosomal-exclusive. While we would ideally perform ChIP to determine its localization on chromatin, this method for assaying DSB sites is likely insufficient to identify DSB sites which differ in each nucleus and for which there are no known hotspots in the worm.

him-5 mutants confer an ~50% reduction in total number of breaks and a very profound change in break dynamics (seen by RAD-51 foci (Meneely et al., 2012)). Since the autosomes receives sufficient breaks in this context to attain a crossover in >98% of nuclei, this indicates that the autosomes are much less profoundly impacted by loss of DSB functions than is the X chromosome. Indeed, prior data from co-author, Monica Colaiacovo, showed that fewer breaks occur on the X (Gao, 2015) likely resulting from differences in the chromatin composition of the X and autosome resulting from X chromosome silencing.

The conclusion that HIM-5 must be required for breaks on the X comes from the examination of DSB levels and their localization in different mutants that impair but do not completely abrogate breaks. In any situation where HIM-5 protein expression is affected (xnd-1, him-17, and him-5 null alleles), breaks on the X are reduced/ eliminated. By contrast, in dsb-2 mutants, where HIM-5 expression is unaffected, both X and autosomal breaks are impacted equally. As discussed above, in the absence of HIM-5 function, there are ~15 breaks/ nucleus. The Ppie1::him-5 transgene is expressed to lower levels than Phim-5::him-5, but in the best case, the ectopic expression of this protein should give a maximum of ~15 breaks (the total # of breaks is thought to be ~30/nucleus). By these estimates, Ppie-1::him-5; him-17 and him-5 null mutants have the same number of breaks. Yet, in the former case, breaks occur on the X; whereas in the latter they do not. The best explanation for this discrepancy is that HIM-5 is sufficient to recruits the DSB machinery to the X chromosome.

The one experiment that seems to elicit the conclusion that HIM-5 expression is sufficient for breaks on the X chromosome is flawed (see below). The conclusion that HIM-5 "coordinates the activities of the different accessory sub-groups" is not supported by data presented here or elsewhere.

We have reorganized the discussion to more directly address the reviewers’ concerns. We raise the possibility that HIM-5 has an important role in bringing together the SPO-11 and its interacting components (DSB-1/2/3) with the other DSB inducing factors, including those factors that regulating DSB timing (XND-1), coordination with the cell cycle (REC-1), association with the chromosome axis (PARG-1, MRE-11), and coupling to downstream resection and repair (MRE-11, CEP-1).  

This raises a natural question: if HIM-5 has such a central role, why are the phenotypes of HIM-5 so mild? We propose that while the loss of DSBs on the X appears mild, more profound effects are seen in the total number, timing, and placement of the DSBs across the genome- all of which are diminished or altered in the absence of HIM-5. The phenotypes of him-5 loss reminiscent of those observed in Prdm9-/- in mice where breaks are relocated to transcriptional start sites and show significant delay in formation. As with PRDM9, the comparatively subtle phenotypes of HIM-5 loss do not diminish its critical role in promoting proper DSB formation in most mammals.

Like most other studies that have examined DSB formation in C. elegans, this work relies on indirect assays, here limited to the cytological appearance of RAD-51 foci and bivalent chromosomes, as evidence of break formation or lack thereof. Unfortunately, neither of these assays has the power to reveal the genome-wide distribution or number of breaks. These assays have additional caveats, due to the fact that RAD-51 association with recombination intermediates and successful crossover formation both require multiple steps downstream of DSB induction, some of which are likely impaired in some of the mutants analyzed here. This severely limits the conclusions that can be drawn. Given that the goal of the work is to understand the effects of individual factors on DSB induction, direct physical assays for DSBs should be applied; many such assays have been developed and used successfully in other organisms.

We appreciate the reviewer’s thoughtful comments. We agree that RAD-51 foci are an indirect readout of DSB formation and that their dynamics can be influenced by defects in downstream repair processes. However, in C. elegans, the available methods for directly detecting DSBs are limited. Unlike other organisms, C. elegans lacks γH2AX, eliminating the possibility of using γH2AX as a DSB marker. TUNEL assays, while conceptually appealing, have proven unreliable and poorly reproducible in the germline context. Similarly, RPA foci do not consistently correlate with the number of DSBs and are influenced by additional processing steps.

Given these limitations, RAD-51 foci remain the most widely accepted surrogate for monitoring DSB formation in C. elegans. While we fully acknowledge the caveats associated with this approach — particularly the potential effects of downstream repair defects — RAD-51 analysis continues to provide valuable insight into DSB dynamics and regulation, especially when interpreted in combination with other phenotypic assessments.

Throughout the manuscript, the writing conflates the roles played by different factors that affect DSB formation in very different ways. XND-1 and HIM-17 have previously been shown to be transcription factors that promote the expression of many germline genes, including genes encoding proteins that directly promote DSBs. Mutations in either xnd-1 or him-17 result in dysregulation of germline gene expression and pleiotropic defects in meiosis and fertility, including changes in chromatin structure, dysregulation of meiotic progression, and (for xnd-1) progressive loss of germline immortality. It is thus misleading to refer to HIM-17 and XND-1 as DSB "accessory factors" or to lump their activities with those of other proteins that are likely to play more direct roles in DSB induction.

It is clear that we will not reach agreement about the direct vs indirect roles here of chromatin remodelers/transcription factors in break formation. In yeast, there is a precedent for SPP1 and in mouse for Prdm9, both of which could be described as transcription factors as well, as having roles in break formation by creating an open chromatin environment for the break machinery. We envision that these proteins function in the same fashion. The changes in histone acetylation in the xnd-1 mutants supports such a claim.

We do not know what the reviewer is referring to in statement that “XND-1 and HIM-17 have previously been shown to be transcription factors that promote the expression of many germline genes.” While the Carelli et al paper indeed shows a role for HIM-17 in expression of many germline genes, there is only one reference to XND-1 in this manuscript (Figure S3A) which shows that half of XND-1 binding sites overlap with the co-opted germline promoters. There is no transcriptional data at all on xnd-1 mutants, save our studies (referenced herein) that XND-1 regulates him-5 expression.

For example, statements such as the following sentence in the Introduction should be omitted or explained more clearly: "xnd-1 is also unique among the accessory factors in influencing the timing of DSBs; in the absence of xnd-1, there is precocious and rapid accumulation of DSBs as monitored by the accumulation of the HR strand-exchange protein RAD-51.

We are not sure what is confusing here. The distribution of RAD-51 foci is significantly altered in xnd-1 mutants and peak levels of breaks are achieved as nuclei leave the transition zone (Wagner et al., 2010; McClendon et al., 2016). There is no other mutation that causes this type of change in RAD-51 distribution.

"The evidence that HIM-17 promotes the expression of him-5 presented here corroborates data from other publications, notably the recent work of Carelli et al. (2022), but this conclusion should not be presented as novel here.

We have clarified this in the text. We note that this paper showed alterations in him-5 levels by RNA-Seq but they did not validate these results with quantitative RT-PCR. Thus, our studies do provide an important validation of their prior results.

The other factors also fall into several different functional classes, some of which are relatively well understood, based largely on studies in other organisms. The roles of RAD50 and MRE-11 in DSB induction have been investigated in yeast and other organisms as well as in several prior studies in C. elegans. DSB-1, DSB-2, and DSB-3 are homologs of relatively well-studied meiotic proteins in other organisms (Rec114 and Mei4) that directly promote the activity of Spo11, although the mechanism by which they do so is still unclear.

Whilst we agree that we understand some of the functions of the homologs, there are clearly examples in other processes of conserved proteins adopting unique regulatory function. We should not presume evolutionary conservation until proven. Indeed the comparison between the Mer2 proteins becomes particularly relevant here. For example, the RMM complex in plants does not contain PRD3, although this protein is thought to have function in DSB formation and repair (Lambing et al, 2022; Vrielynck et al., 2021; Thangavel et al., 2023). In Sordaria, as well, the Mer2 homolog has distinct functions (Tesse et al., 2017).  

Mutations in PARG-1 (a Poly-ADP ribose glycohydrolase) likely affect the regulation of polyADP-ribose addition and removal at sites of DSBs, which in turn are thought to regulate chromatin structure and recruitment of repair factors; however, there is no convincing evidence that PARG-1 directly affects break formation.

Our prior collaborative studies on PARG-1 showed that is has a non-catalytic function that promote DSBs that is independent of accumulation of PAR (Janisiw et al., 2020; Trivedi et al., 2022)

CEP-1 is a homolog of p53 and is involved in the DNA damage response in the germline, but again is unlikely to directly contribute to DSB induction.

We respectfully disagree with the reviewer’s statement. While CEP-1 is indeed a homolog of p53 and plays a major role in the DNA damage response, prior work from Brent Derry’s lab and from our group (Mateo et al., 2016) demonstrated that specific cep-1 separationof-function alleles affect DSB induction and/or repair pathway choice independently of canonical DNA damage checkpoint activation. In particular, defects in DSB formation observed in certain cep-1 mutants can be rescued by exogenous irradiation, supporting a direct or closely linked role in promoting DSB formation rather than merely responding to damage. Thus, based on these functional data, we considered CEP-1 a relevant factor to include in our analysis. We have now clarified this rationale in the revised manuscript.

HIM-5 and REC-1 do not have apparent homologs in other organisms and play poorly understood roles in promoting DSB induction. A mechanistic understanding of their functions would be of value to the field, but the current work does not shed light on this. A previous paper (Chung et al. G&D 2015) concluded that HIM-5 and REC-1 are paralogs arising from a recent gene duplication, based on genetic evidence for a partially overlapping role in DSB induction, as well as an argument based on the genomic location of these genes in different species; however, these proteins lack any detectable sequence homology and their predicted structures are also dissimilar (both are largely unstructured but REC-1 contains a predicted helical bundle lacking in HIM-5). Moreover, the data presented here do not reveal overlapping sets of genetic or physical interactions for the two genes/proteins. Thus, this earlier conclusion was likely incorrect, and this idea should not be restated uncritically here or used as a basis to interpret phenotypes.

Actually, there is quite good bioinformatic analysis that the rec-1 and him-5 loci evolved from a gene duplication and that each share features of the ancestral protein (Chung et al., 2015). We are sorry if the reviewer casts aspersions on the prior literature and analyses. The homology between these genes with the ancestral protein is near the same degree as dsb-1, dsb-2, or dsb-3 to their ancestral homologs (<17%).

DSB-1 was previously reported to be strictly required for all DSB and CO formation in C. elegans. Here the authors test whether the expression of HIM-5 from the pie-1 promoter can rescue DSB formation in dsb-1 mutants, and claim to see some rescue, based on an increase in the number of nuclei with one apparent bivalent (Figure 2C). This result seems to be the basis for the claim that HIM-5 coordinates the activities of other DSB proteins. However, this assay is not informative, and the conclusion is almost certainly incorrect. Notably, a substantial number of nuclei in the dsb-1 mutant (without Ppie-1::him-5) are reported as displaying a single bivalent (11 DAPI staining bodies) despite prior evidence that DSBs are absent in dsb-1 mutants; this suggests that the way the assay was performed resulted in false positives (bivalents that are not actually bivalents), likely due to inclusion of nuclei in which univalents could not be unambiguously resolved in the microscope. A slightly higher level of nuclei with a single unresolved pair of chromosomes in the dsb-1; Ppie-1::him-5 strain is thus not convincing evidence for rescue of DSBs/CO formation, and no evidence is presented that these putative COs are X-specific. The authors should provide additional experimental evidence - e.g., detection of RAD-51 and/or COSA-1 foci or genetic evidence of recombination - or remove this claim. The evidence that expression of Ppie-1::him-5 may partially rescue DSB abundance in dsb-2 mutants is hard to interpret since it is currently unknown why C. elegans expresses 2 paralogs of Rec114 (DSB-1 and DSB-2), and the age-dependent reduction of DSBs in dsb-2 mutants is not understood.

We have removed this claim in part because we have been unable to create the triple mutants strains to analyze COSA-1 foci.

To the point about 11 vs 12 DAPI bodies: the literature is actually replete with examples of 11 DAPI bodies vs 12 in mutants with no breaks:

Hinman al., 2021: null allele of dsb-3 has an average of 11.6 +/- 0.6 breaks;

Stamper et al, 2013, show just over 60% of dsb-1 nuclei with 12 DAPI bodies and 5-10% with 10 DAPI bodies. (Figure 1);

In addition, we also previously showed (Machovina et al., 2016) that a subset of meiotic nuclei have a single RAD-51 focus and can achieve a crossover. RAD-51 foci in spo-11 were also reported in Colaiacovo et al., 2003.

Several of the factors analyzed here, including XND-1, HIM-17, HIM-5, DSB-1, DSB-2, and DSB-3, have been shown to localize broadly to chromatin in meiotic cells. Coimmunoprecipitation of pairs of these factors, even following benzonase digestion, is not strong evidence to support a direct physical interaction between proteins.

Similarly, the super-resolution analysis of XND-1 and HIM-17 (Figure 1EF) does not reveal whether these proteins physically interact with each other, and does not add to our understanding of these proteins functions, since they are already known to bind to many of the same promoters. Promoters are also likely to be located in chromatin loops away from the chromosome axis, so in this respect, the localization data are also confirmatory rather than novel.

While the binding to promoters would be expected to be on DNA loops, that has not been definitively shown in the worm germ line. The supplemental data of the Carelli paper suggests that there are ~250 binding sites for each protein at these coopted promoters. This could not account for crossover map seen in C. elegans.

The reviewer states correct that we do not reveal that these proteins interact, but we have shown that the two proteins co-IP and have a Y2H interaction. This interaction is supporedt by a recent publication (Blazickova et al., 2025) corroborating this conclusion and identifies XND-1 in HIM-17 co-IPs also in the presence of benzonase. We do now show, however, by immuno-localization that the two proteins appear to be adjacent, but nonoverlapping. As now described in the text, AlphaFold 3 modeling and structural analysis suggests that the two proteins do interact directly and that the tagged 5’ end of HIM-17 used in our studies is likely to be at least 200nm from the putative XND-1 binding interface, a distance that is consistent with our confocal images showing frequent juxtaposition of the two proteins.

The phenotypic analysis of double mutant combinations does not seem informative. A major problem is that these different strains were only assayed for bivalent formation, which (as mentioned above) requires several steps downstream of DSB induction. Additionally, the basis for many of the single mutant phenotypes is not well understood, making it particularly challenging to interpret the effects of double mutants. Further, some of the interactions described as "synergistic" appear to be additive, not synergistic. While additive effects can be used as evidence that two genes work in different pathways, this can also be very misleading, especially when the function of individual proteins is unknown. I find that the classification of genes into "epistastasis groups" based on this analysis does not shed light on their functions and indeed seems in some cases to contradict what is known about their functions. ‘

As described above, each of the proteins analyzed is thought to have a direct role in regulating meiotic DSB formation and single mutant phenotypes are consistent with this interpretation. In almost all-if not all- of these cases, IR induced breaks suppress univalent phenotypes (or uncover a downstream repair defect (e.g. in mre-11)) supporting this conclusion. We have changed the terminology from “epistasis groups” since this is not strict epistasis, but rather, “functional groups”.  

The yeast two-hybrid (Y2H) data are only presented as a single colony. While it is understandable to use a 'representative' colony, it is ideal to include a dilution series for the various interactions, which is how Y2H data are typically shown.

The Y2H data are presented as spots on a plate and are from three to four individual transformants per interaction tested, and are not individual colonies. The experiment was repeated in triplicate from different transformations. We have now made this clearer in the materials and methods section. This approach has been successfully used to examine protein interactions in our prior manuscripts of yeast and human proteins [Gaines et al (2015) Nat. Comms 6:7834; Kondrashova et al (2017) Cancer Discovery 7:984; Garcin et al (2019) PLoS Genetics 15:e1008355; Bonilla et al (2021) eLife 1: e68080) Prakash et al (2022) PNAS 119: e2202727119, etc]

Additional (relatively minor) concerns about these data:

(1) Several interactions reported here seem to be detected in only one direction - e.g., MRE-11-AD/HIM-5-BD, REC-1-AD/XND-1-BD, and XND-1-AD/HIM-17-BD - while no interactions are seen with the reciprocal pairs of fusion proteins. I'm not sure if some of this is due to pasting "positive" colony images into the wrong position in the grid, but this should be addressed.

The asymmetry in the interactions observed is due to the well-known phenomenon in yeast two-hybrid (Y2H) assays where certain plasmids exhibit self-activation when fused in one orientation, making interpretation of reciprocal interactions challenging. In our experiment, some of the plasmids indeed showed self-activation in one direction, which likely accounts for the lack of interaction seen with the reciprocal pairs of fusion proteins. We have clarified this point in the Methods.

(2) DSB-3 was only assayed in pairwise combinations with a subset of other proteins; this should be explained; it is also unclear why the interaction grids are not symmetrical about the diagonal.

We have now completed the analysis by adding the interactions of DSB-3 with the remaining proteins that were missing from the initial set.

(3) I don't understand why the graphic summaries of Y2H data are split among 3 different figures (1, 2, and 3).

We chose to split the graphic summaries of the Y2H data across Figures 1, 2, and 3 because we felt this organization better aligns with the flow of the results presented in each figure. Each set of interactions is shown in the context of the specific experiments and findings discussed in those sections, which we believe helps provide a clearer and more logical presentation of the data.

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

Figure 1: B) The IP is difficult to interpret - there is a band of the corresponding size to XND-1 in the control lane calling into question the specificity of the IP/Western.

We added a supplemental figure with the specificity of the antibody showing that there is a background non-specific band.

C) More information about the mass spectrometry should be included. No indication of the number of times a peptide was identified, or the overall coverage of the identified proteins.

Done

This is important as in the results section (line 114) the authors indicate that there was "strong" interaction yet there is no way to assess this.

D) Why wasn't hatching measured in the him-5p::him-5; him-17(ok424) strain?

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

E) Quantification of the cytology should be included.

We have now quantified overlap between XND-1 and HIM-17

Figure 2: C) Statistics should be included.

Done

E) Quantification should be included for the cytology. I recommend changing the eals15 to HIM-5.

We included better images showing whole gonads instead of one or two nuclei. We were not sure what the reviewers want us to quantify here since the relocalization of the protein to the cytoplasm is very clear.

I have a general issue with the use of the term epistasis - this is used to order gene function based on different mutant phenotypes, usually with null alleles. While I think the authors have valid points with how they group the different SPO-11 accessory proteins, I do not think they should use the word epistasis, but rather genetic interactions.

We appreciate the reviewers thoughts on this matter and have removed the term epistasis and use functional groups or genetic interactions throughout the text.

Figure 4 and the nature of the X chromosome: First, I think it would help the non-C. elegans reader to include a little more information on the X chromosome with respect to its differences compared to the autosomes. I also think that, if possible, it would be beneficial to include a model of the X in Figure 4.

We have added more about X/autosome differences in the intro and during the discussion of HIM-5 function and have added a figure showing difference in the behavior of the X/autosomes during DSB/crossover formation.

Minor points:

Abstract: Given the findings of Silva and Smolikove on SPO-11 breaks, I recommend removing "early" from line 28 in the Abstract.

Done

Introduction (line 93): I think "biochemical studies" is a stretch here - I recommend "interaction studies".

Done

Results: (lines 160-161): mutations are not required for breaks. Line 172, there is a problem with the sentence.

Corrected

Reviewer #2 (Recommendations For The Authors):

Major comments:

(1) Figure 1B- The signal for XND-1 seems to appear both in the control and him-17::HA IP. Do the authors have tested the specificity of the XND-1 antibody?

We included a supplementary figure demonstrating the specificity of the XND-1 antibody by Western blot. This was also previously published (Wagner et al., 2010)

(2) Figure 1D - can the authors provide an explanation why the him-5p::him-5 transgene that drives a higher expression than pie-1p::him-5 fails to suppress the Him phenotype seen in him-17? What are the HIM-5 levels like in these two strains compared to N2 and him-17 null mutants? Can this information provide explanation for the differential effect of the him-5 transgenes?

We previously reported that him-5p::him-5 drives higher expression than pie-1p::him-5 (McClendon et al, 2016).

The reason that him-5p::him-5 does not rescue, despite higher wild type expression is that HIM-17 directly regulates expression of him-5. Since HIM-17 does not regulate the pie-1 promoter, the pie-1p::him-5 construct can at least partially suppress the him-17 mutation.

We have (hopefully) explained this better in the text.  

(3) Line 102- the subheading "HIM-5 is the essential factor for meiotic breaks in the Xchromosome" may not be appropriate for this section. This is what has previously been known. However, the results in Figure 1 demonstrate that a him-5 transgene can partially rescue the him-17 and ¬xnd-1 phenotype, but not that it is essential for meiotic DSB formation on X chromosomes.

We think some of the concern here is sematic and have changed the phraseology to say that HIM-5 is SUFFICIENT for DSBs on the X… which had not previously been shown.

Vis-à-vis the X chromosome, in all genetic backgrounds examined, the absence of HIM-5 consistently results in a complete lack of DSBs on the X. For instance, in dsb-2 mutants— where HIM-5 is still expressed—DSBs are reduced genome-wide, but the X chromosome occasionally retains breaks. In contrast, even a weak allele of him-17 results specifically in the loss of X chromosome breaks, underscoring a unique requirement for HIM-5 in promoting DSBs on the X. While Figure 1 shows that a him-5 transgene can partially rescue him-17 and xnd-1 phenotypes, the consistent observation that X breaks are absent without HIM-5 supports its classification as sufficient for DSB formation on the X chromosome.

(4) Figure 1E - please consider enlarging the images and showing multiple examples.

Done.

I also suggest that the authors perform a more rigorous analysis to support the conclusion that XND-1 and HIM-17 localize away from the axis by quantifying multiple images and doing line-scan analysis.

Provided. New images are provided in both, the main and supplemental figures, and quantification is included. There is no detectable overlap of the two protein with one another or the DNA axes (see quantification of overlap in Fig. 1).

(5) Line 162 - This is the first mention of DSB-1, DSB-2, and DSB-3 in the paper. DSB-1 and DSB-2 are Rec114 homologs in C. elegans (Tesse et al., 2017), while DSB-3 is a homolog of Mei4 (Hinman et al., 2021). These proteins should be properly introduced in the introduction with appropriate citations.

Done. We appreciate the reviewer pointing out that this was the first reference to these genes.

(6) Line 169 - the rationale for this experiment is unclear. Why did the Y2H interaction between HIM-5 and DSB-1 prompt the authors to test the rescue of dsb-1 or dsb-2 phenotypes by the ectopic expression of him-5? Do the authors have evidence that HIM-5 level is reduced in dsb-1 or dsb-2 mutants?

We have reorganized this section to better explain the motivation for looking at these interactions. We did see a difference in the localization in HIM-5 in the dsb-1 mutant animals and we did have a sense that HIM-5 was critical for breaks on the X. We reasoned that it could have independent functions in promoting breaks that were not yet appreciated so wanted to do this experiment.

(7) Line 172 - "very slightly reduced". This claim requires statistical analysis.

We added statistical analysis, but we also removed this claim.

(8) Figures 2C and 2D - Can the authors provide an explanation why the pie-1p::him-5 transgene fails to suppress the phenotypes in dsb-1, while the him-5p::him-5 trasgene can? Again, the rationale for these experiments is unclear. Because of this, the interpretation is also unclear.

The difference in rescue between the pie-1p::him-5 and him-5p::him-5 transgenes likely reflects differences in expression levels. As previously shown (McClendon et al., 2016), the him-5p::him-5 construct results in significantly higher expression of HIM-5 protein compared to pie-1p::him-5. This elevated expression likely explains its ability to partially rescue the dsb-1 phenotype. In contrast, the lower expression driven by the pie-1 promoter is insufficient to compensate for the absence of dsb-1 function. We have clarified the rationale and interpretation of these experiments in the revised manuscript to better reflect this point.

(9) Lines 184-185 - the data for endogenously tagged HIM-5::3xHA are not shown anywhere in the paper. This must be shown.

We have added this in the supplemental figures.

(10) Figure 2D and 2E - what does the localization of pie-1p::him-5::GFP (eaIs15) and him5p::him-5::GFP (eaIs4) look like in wild-type and dsb-1 mutants? Are the cytoplasmic aggregates caused by increased levels of HIM-5 expression? Can the differential behavior of him-5 transgenes provide explanation for differential rescues?

We now show both live and fixed images of Phim-5::him-5::gfp transgenes, as well as the localization of the endogenously HA-tagged HIM-5 locus (Figure 2 and S3). In all cases, the protein is initially nuclear and then absent from meiotic nuclei with similar timing. The Ppie1::him-5 transgene was very difficult to image due to low expression (even in wild type) so it not shown here. We presume it is the slightly elevated level of expression of the Phim5::him-5::gfp that can explain the differential rescue.

(11) Lines 221-222, where are the results shown? Please refer to Figure S3.

Done

(12) Figure S3 - these need statistical analyses.

Done

(13) Lines 230-231 - what about the rec-1; parg-1; cep-1 triple mutant?

This is an excellent suggestion and not one we have not yet pursued. Given the lack of strong phenotypes in all combination of double mutants, we prioritized other experiments . However, we agree that examining the rec-1; parg-1; cep-1 triple mutant would provide a valuable test of whether these factors act in the same pathway, and we appreciate the reviewer highlighting this potential future direction.

(14) Line 298 - I suggest the authors take a look at the Alphafold prediction of DSB-1/DSB-2/DSB-3 and the comparison to human and budding yeast Rec114/Mei4 complex in Guo et al., 2022 eLife, which could provide insights into the Y2H results.

We thank the reviewer for these comments and have indeed used these interactions and predicted homologies to zero in a region of interaction between these proteins that resembles what is seen in humans and yeast with a dimer of REC114 like proteins wraps stabilizing a central Mei4 helix . This is now shown in Figure 3H, I. Satisfyingly, this modeling predicts that a trimer comprised of 2 DSB-1 proteins with DSB-3 is more stable than a DSB1-DSB-2-DSB-3 trimer. This might explain why DSB-2 is not required in young adults and only becomes essential as DSB-1 levels drop in older animals (Rosu et al., 2013)

(15) Can the authors introduce mutations within the DSB-1 interfaces that disrupt the interaction to either SPO-11 or DSB-2?

We have begun to address this question by introducing targeted mutations within DSB-1. As shown in Figure 3E and 3F, mutations in the C-terminal region of DSB-1—which includes a core of four α-helices—disrupt its interaction with DSB-2 and DSB-3, but not with SPO-11. These findings suggest that the C-terminus mediates interactions specifically with DSB2 and DSB-3

(16) Line 323 - The him-5 phenotypes are too weak to support the idea that it serves as the linchpin for the whole DSB complex. Do the authors have an explanation for why him-5 mutants exhibit X-chromosome-specific DSB defects?

In response to the reviewer, above, and in the text, we have included a more detailed explanation of why we think HIM-5 has a key role in coordinating meiotic break formation. Although, identified for its role on the X, the phenotypes associated with DSB formation in the mutant are really quite pleiotropic and severe.

(17) Line 436 - C. elegans lacks DSB hotspots.

Removed

Minor comments:

(1) Figure 1A - please show the raw data for the yeast two-hybrid.

We show representative yeast colonies in Figure S3.

(2) It looks like the labeling for Figure 1B and 1C are switched.

Fixed.

(3) Figure 1B - what does the red box indicate? Please explain it in the legend.

It indicates the XND-1 band. We added that information in the legend.

(4) Figure 1C - in the legend, it was noted that the results are from GFP pulldowns of HIM17::GFP. However, the method for Figure 1B and the method section noted that HIM-17 was tagged with 3xHA, and the pull-down was performed using anti-HA affinity matrix. Please reconcile this discrepancy.

That’s because they were done in two different sets of experiments. For the IPs we used a HIM-17::HA strain and for the MS, a HIM-17::GFP strain.

(5) Also in Figure 1C - please call Table S2 in the main text when discussing the mass spec results. Also, it is not clear what HIM-17 and GFP indicate in the table. What makes CKU80 different from the other proteins listed under GFP? Please explain more clearly in the legend.

We have move the table to supplemental data where we have included all of the peptide counts and gene coverage. We have included in the revised method rationale for inclusion in this table which explains why CKU-80 differs.

(6) Line 527 - it is unclear what experiment was done for HIM-17. Please revise it to indicate that this is for "HIM-17 immunoprecipitation". Also please indicate the strain used for HIM17 pull-down (AV280?).

(7) Line 113- please be specific about how the HIM-17 IP was performed. Which epitope and strains are used for pull-downs?

This indeed was AV280. This has been added to the text and methods.

(8) Figure 1D- What does ND mean? In the text, it was stated that there was only a minor suppression of hatching rates. The hatching rate for him-5p::him-5; him-17 must have been measured, and the data must be presented.

ND does mean not determined. We have removed the statement about “minor suppression”. We only tested the overall population dynamics in the Phim-5::him-5;him17(ok424) and the DAPI body counts. The failure to suppress the latter suggests there would be no enect on hatching rates, although we did not test this directly. Since we had done this for the Ppie-1::him-5;him-17 strain, we provided this information to further support the claims of genetic rescue by ectopic expression.

(9) Line 151 - please specify that STED was used.

We have removed the STED images, and just show the confocal images with Lightning Processing.

(10) Figure 1E- the authors suggested that HIM-17 and XND-1 mainly localize to autosomes but not the X chromosome. However, there is not enough evidence that the chromosome excluded from HIM-17 staining is indeed an X chromosome.

(11) Figure 1E (Line 154) - what are the active chromatin markers examined? Where are the data?

We have previously shown that the chromosome lacking XND-1 staining is the X (Wagner et al., 2010). The X is heterochromatic and chromatin marks associated with active transcription, including H3K4me3 and HTZ-1 (a variant H2A), preferentially localize to autosomes, effectively anti-marking the X chromosome. As shown in the new Figure 1E, a single chromosome has very little XND-1 and HIM-17 associated proteins. This is the X chromosome.

(12) Line 172 - It should be a comma instead of the period after "In dsb-1 mutants".

Fixed

(13) Figure S3H-K - I suggest the authors indicate the alleles of mre-11 (null vs. iow1) on the graph, similarly to him-5(e1490) to avoid confusion.

Done

(14) Lines 294 and 600 - Guo et al. 2022 is now published in eLife. The authors must cite the published paper, not the preprint.

Fixed

(15) Line 407 - the reference Carelli et al., 2022 is missing.

Added

(16) Line 766 - please remove "is" before nuclear.

Done

Reviewer #3 (Recommendations For The Authors):

Major issues:

In my view, the most interesting mechanistic finding in the paper is the evidence that HIM-5 may not bind to chromatin in the absence of DSB-1. If validated, this would suggest that HIM-5 is likely to be directly involved in a process that promotes break formation, in contrast to factors such as HIM-17 and XND-1. It does not, however, support the idea that HIM-5 is at the top of a hierarchy of DSB factors, as it is interpreted here. More importantly, the data supporting this claim are unconvincing; only a single image of an unfixed gonad from an animal expressing HIM-5::GFP is shown. Immunofluorescence should be performed and the results must be quantified.

We have provided additional images of the HIM-5 relocalization to show that we observed this in both fixed and live worms with two different tagged strains. The exclusion from the nucleus is seen in all scenarios. Whether the protein now accumulates exclusively in the cytoplasm/ is destabilized is challenging to address with the fixed images due to the arbitrariness of defining “background” staining.

More generally, this type of analysis, looking at the interdependence of different factors for their association with chromosomes, is much more informative than the genetic interaction data presented in the paper, which does not seem to provide any mechanistic insights into the functions of the factors analyzed. The paper could potentially be greatly improved through a more extensive, systematic analysis of the interdependence of DSBpromoting factors for their localization to chromosomes.

We have at least added this for XND-1 and HIM-17 and show they are not interdependent for chromosome association. We also provide for the first time data on the localization of HIM-5 in the dsb-1 mutant. Many of the other interactions have already been shown in the literature and/or were not warranted base on the lack of genetic interaction we present here.

Minor issues:

The title is vague and inconclusive. A more concrete title summarizing the major findings would help readers to assess whether the work is of interest.

We have discussed the title extensively with all authors and all would like to keep the current title.

The authors claim that the expression of HIM-5 from a different promoter (Ppie-1::him-5) but not its endogenous promoter (Phim-5::him-5) can partially rescue the DSB defect in him-17 mutants. To support this claim, they should really quantify the germline expression of HIM-5 in wild-type, him-17, him-17; Ppie-1::him-5, and Phim-5::him-5; him-17.

We had previously reported the expression in the N2 background of both transgenes (McClendon et al., 2016)

Panel O appears to be missing from Figure S3.

Fixed

The evidence for chromosome fusions in cep-1; mre-11 mutants shown in S4D is not convincing and the claim should be removed unless stronger evidence can be obtained.

A clearer image has been added

The basis of the following statement is unclear: "Furthermore, rec-1;him-5 double mutants give an age-dependent severe loss of DSBs (like dsb-2 mutants) suggesting that the ancestral function of the protein may have a more profound effect on break formation." The manuscript does not seem to include data regarding age-dependent loss of DSBs and no other publication is cited to support this claim. The interpretation is also perplexing; I think that it may be predicated on the idea that REC-1 and HIM-5 are paralogs, but as stated above, this claim is not well supported and is likely specious.

We have added the reference. This was shown in Chung et al., 2013 – the paper that presented the cloning of the rec-1 locus.

Author response:

Joint Public Review

This manuscript puts forward the provocative idea that a posttranslational feedback loop regulates daily and ultradian rhythms in neuronal excitability. The authors used in vivo long-term tip recordings of the long trichoid sensilla of male hawkmoths to analyze spontaneous spiking activity indicative of the ORNs' endogenous membrane potential oscillations. This firing pattern was disrupted by pharmacological blockade of the Orco receptor. They then use these recordings together with computational modeling to predict that Orco receptor neuron (ORN) activity is required for circadian, not ultradian, firing patterns. Orco did not show a circadian expression pattern in a qPCR experiment, and its conductance was proposed to be regulated by cyclic nucleotide levels. This evidence led the authors to conclude that a post-translational feedback loop (PTFL) clockwork, associated with the ORN plasma membrane, allows for temporal control of pheromone detection via the generation of multi-scale endogenous membrane potential oscillations. The findings will interest researchers in neurophysiology, circadian rhythms, and sensory biology. However, the manuscript has limited experimental evidence to support its central hypothesis and is undermined by several questionable assumptions that underlie their data analysis and model builds, as well as insufficient biological data, including critical controls to validate and/or fully justify the model the authors are proposing.

We thank the reviewers for their thorough and thoughtful comments and believe that the manuscript will be much stronger once we incorporate the requested changes.

Please note that we used ORN as acronym for “olfactory receptor neuron” throughout the manuscript. ORNs contain odorant receptors (ORs), and in insects these ORs have to associate with the olfactory receptor co-receptor (Orco) in the cilium of the neuron to form functional OR-Orco complexes for odorant detection. Besides this chaperone function, Orco can form homomers with the potential to act as ionic pacemaker channels; a role which we explore in this study.

Strengths:

The study is notable for its combination of long-term in vivo tip recordings with computational modeling, which is technically challenging and adds weight to the authors' claims. The link between Orco, cyclic nucleotides, and circadian regulation is potentially important for sensory neuroscience, and the modeling framework itself - a stochastic Hodgkin-Huxley formulation that explicitly incorporates channel noise - is a solid and forward-looking contribution. Together, these elements make the study conceptually bold and of clear interest to circadian and olfactory biologists.

Major weaknesses:

At the same time, several limitations temper the conclusions. The pharmacological evidence relies on a single antagonist and concentration, without key controls. The circadian analysis is based on relatively small numbers of neurons, with rhythms detected only in subsets, and the alignment procedure used in constant darkness raises concerns of bias. The molecular evidence is sparse, with only three qPCR timepoints, and the model, while creative, rests on assumptions that are not yet fully supported by in vivo data.

Please see our responses to the detailed comments.

Detailed comments are provided below:

(1) The role for Orco proposed in the authors' model largely stems from the effects seen following the administration of (a single dose) of the Orco antagonist, OLC15. However, this hypothesis is undercut by the lack of adequate pharmacological controls, including a basic multipoint OLC15 dose-response series in addition to the administration of blockers for the other channels that are embedded in their model, but which were ruled out as being involved in the modulation of biological rhythms. In addition, these studies would (ideally) also benefit from the inclusion of the same concentration (series) of an inactive OLC15 analog to better control for off-target effects.

The Orco agonist VUAA1 (Jones et al., 2011) binds directly to Orco and increases the channel open time probability. In M. sexta hawkmoths, we have already published that VUAA 1 increases the low spontaneous activity of ORNs in a dose-dependent fashion (Nolte et al., 2016). Chen and Luetje (2012) systematically varied the chemical structure of VUAA1 to identify new Orco ligands and discovered 22 Orco Ligand Candidates (OLC) that either activated or inhibited Orco. In their heterologous expression system, Orco was most sensitive to inhibition by OLC15. Based on these results, we published a dose-response curve of OLC15 inhibition (1-100 µM) using in vivo tip recordings of pheromone-sensitive long trichoid sensilla of M. sexta (Nolte et al., 2016). In that study, we could also demonstrate that OLC15 antagonizes the VUAA1 activation of Orco.

Furthermore, we tested other published Orco antagonists in in vivo assays in intact hawkmoths, focusing on amiloride-derived antagonists, because we previously identified an amiloride-sensitive cation channel in hawkmoth ORNs. We found that, in contrast to OLC15, the amilorides HMA and MIA were not Orco-specific but instead affected different targets depending on time-of-day (Nolte et al., 2016). Based on those experiments and the dose-response curves we determined that the Orco agonist VUAA1 (Jones et al., 2011) and the Orco antagonist OLC15 (Chen and Luetje, 2012) worked best in hawkmoth ORNs to target Orco pharmacologically. Based on comparative tests with other published Orco antagonists we settled since then in all further experiments on a dose of 50 µM OLC15.

We will clarify the Methods section accordingly.

(2) The expression pattern of Orco was assessed using qPCR at only three timepoints. Rhythmic transcripts can easily be missed with such sparse sampling (Hughes et al., 2017). A minimum of six evenly spaced timepoints across a 24-hour cycle would be required to confidently rule out circadian transcriptional regulation. In addition, the use of the timeless mRNA control from another study is not acceptable. Furthermore, qPCR analysis measures transcript abundance, not transcription, as the authors repeatedly state. Transcriptional studies would require nuclear run-off or, more recently, can be done with snRNAseq analysis. Taken together, these concerns undermine the authors' desire to rule out TTFL-based control that directly led them to implicate a PTTF-based model.

We agree with the referees that more time points and a direct comparison between timeless and Orco mRNA levels should be included in this manuscript. We will include these additional qPCR experiments and edit the manuscript to make clear that we measure transcript abundance, but we will not perform snRNAseq analysis due to time- and financial constraints. We are currently working on the transcriptional control of Orco, both during ontogeny and throughout the day but this work in progress is beyond the scope of this manuscript.

(3) The modelling presented is based on Orco as a ZT-dependent conductance tied to the cAMP oscillations that were reported by this group in the cockroach and from the presence and functionality in Manduca of homomeric Orco complexes that are devoid of tuning ORs. While these complexes have been generated in cell culture and other heterologous expression systems, as well as presumably exist in vivo in the Drosophila empty neuron and other tuning OR mutants, there is no evidence that these complexes exist in wild-type Manduca ORNs. While this doesn't necessarily undermine every aspect of their models, the authors should note the presence of Orco/OR complexes rather than Orco homomeric complexes.

Our ELISAs found circadian oscillations in cAMP levels not only in antennae of the Madeira cockroach (Schendzielorz et al., 2014, 2012), but also in hawkmoth antennae (Schendzielorz et al., 2015). We will add the 2015 citation to the Modeling chapter in the Methods section to clarify this.

We agree with the referees that we cannot distinguish between Orco homo- and heteromers in the different compartments of our hawkmoth ORNs. Thus, as the referee suggests, we will add text regarding the presence and localization of OR-Orco heteromers. However, we have indications that Orco homomers could indeed be present in the hawkmoth ORNs. In a heterologous expression system, MsexOrco expression alone was sufficient to increase intracellular Ca²⁺ levels in response to VUAA1 application (Nolte et al., 2013). In differentiating primary cell cultures of hawkmoth antennae, Orco expression started during a developmental time window where ORNs did not yet express pheromone receptors, and Orco affected spontaneous activity (Nolte et al., 2016). Thus, Orco homomers are present in developing hawkmoth ORNs during a time window where ORNs already express spontaneous activity but cannot heteromerize with pheromone receptors. However, we do not know whether and in what ratio homo- and heteromers of Orco and ORs are present in the respective sensillum compartments of adult hawkmoths (Nolte et al., 2013; Stengl, 1994; Stengl and Hildebrand, 1990).

We will clarify our manuscript accordingly.

(4) Some aspects of the authors' models, most notably the decision to phase align/optimize their DD and OLC15 recordings, are likely to bias their interpretations.

It is consensus that insects display daily and circadian rhythms in pheromone-dependent mating, odor-gated feeding, and egg-laying behavior that phase-locks to environmental rhythms, corresponding with daily/circadian rhythms of sensory neuron physiology (e.g., Merlin et al., 2007; Rymer et al., 2007; Schendzielorz et al., 2015, 2012). However, circadian rhythms can be easily masked by stress, like the disturbances during a very challenging long-term recording experiment over several days. In addition, we observed in our animal raising facility that in LD 17:7 light-dark cycles the originally nocturnal hawkmoths M. sexta distribute their activity patterns over the course of the day, finding nocturnal as well as diurnal hawkmoths. Thus, light-dark cycles were not enough to ensure phase-synchronized behavioral rhythms, and it is very likely that the nocturnal hawkmoths rely heavily on pheromone/odor dependent synchronization as also found in other moth species (Ghosh et al., 2024). Here, we used isolated males that were never exposed to the female pheromones so that their circadian activity patterns readily disperse. Therefore, it became necessary in free-running conditions to first determine the respective behavioral rhythm for each animal, and then to phase-align their activity patterns to allow for statistical analysis. Otherwise, circadian differences would average out in a free-running population. As requested by the referees in point (7), we will use additional tests for rhythmicity in each of our recordings and revise the manuscript accordingly.

Assuming that hawkmoths need pheromone presence as additional Zeitgeber, we are currently working on a new set of experiments where we attempt to improve synchronization by exposure to LD cycles and pheromone before DD and OLC15 recordings. We will add these experiments to the manuscript.

(5) The tip recordings from long trichoid sensilla are critical aspects of this study. These recordings were carried out on upper sensillar tips located on the distal-most second annulus. Since there are approximately 80 annuli on the Manduca antennae, it is unclear whether the recordings are representative of the antennal response.

We think the reviewers might have misinterpreted our description of the recording site. In the Methods, we state that we clip off the 20 most distal annuli (leaving a stump of about 60 annuli) and insert the reference electrode into the flagellum up to the second annulus from the cut end, i.e., the recording site is located at 2/3 – 3/4 of the antenna length as seen from the head of the animal. We will make this more clear in the Methods section.

In addition, our lab did show with antibody stainings against Orco that apparently all ORNs that innervate long and short trichoid sensilla along the whole flagellum express the same staining pattern (Nolte et al., 2016). Furthermore, our patch clamp recordings of primary cell cultures of whole male antennae found largely overlapping ion channel populations across ORNs. This would indicate that all ORNs, whether they express pheromone- or general odorant receptors, could potentially share the same Orco-dependent spontaneous activity rhythms. In our lab, different experimenters from different years that recorded from long trichoid sensilla on different annuli did not detect obvious differences in neither the spontaneous activity nor the pheromone responses (c.f., Dolzer et al., 2003; Gawalek and Stengl, 2018; Schneider et al., 2025). Thus, it is very likely that we are reporting a general encoding mechanism that is not locally restricted along the antennal flagellum.

(5.1) The authors do not provide any data in support of their cAMP/cGMP-based Orco gating…

There are publications supporting cyclic nucleotide gating of Orco in Drosophila, but only after previous phosphorylation via protein kinase C (PKC; review: (Wicher and Miazzi, 2021)). Since Orco is very conserved among insect species, it is likely that these PKC and cGMP/cAMP-dependent regulations are present in other insect species. We are currently running thorough tip-recording experiments on the regulation of Orco gating, which are beyond the scope of this manuscript. However, we will add a set of experiments to this manuscript that demonstrates cAMP gating of Orco.

(5.2)… and the PTTF model proposed is somewhat disappointing.

For a detailed introduction of our PTFL membrane clock hypothesis please see our opinion paper (Stengl and Schneider, 2024).

(5.3) The model seems to be influenced by their long-held proposal that insect olfactory signaling has a critical metabotropic component involving cyclic nucleotides, PKC, etc, a view that may be influenced by the use of Orco homomeric complexes generated in HEK cells.

Indeed, we propose a metabotropic pheromone-transduction cascade, which in moths and cockroaches is based on G-protein-mediated activation of phospholipase C but not on adenylyl cyclase activation. Our hypothesis is not influenced by HEK cell heterologous expression studies of Orco but is supported by our own work comparing in vivo tip recordings of intact hawkmoths with patch clamp experiments on hawkmoth primary cell cultures of olfactory receptor neurons, which are able to respond to their species-specific pheromones in vitro ((Schneider et al., 2025; Stengl, 2010; Stengl and Funk, 2013; Wicher and Miazzi, 2021). In addition, a multitude of publications by other laboratories with in vivo and in vitro studies using physiological, genetic, and immunocytochemical assays all support a metabotropic signal transduction cascade in insect olfaction (reviews: Stengl, 2010; Stengl and Funk, 2013; Wicher and Miazzi, 2021). In contrast, the hypothesis suggesting a solely ionotropic pheromone- and general odor-dependent transduction cascade for all insect species is based on very sparse experimental evidence, based primarily on heterologous expression studies such as HEK cells that lack the insect’s WT molecular surroundings, and thus, cannot predict OR-Orco function in vivo. Furthermore, the ionotropic hypothesis is heavily based upon the argument that an inverse 7TM receptor cannot couple to G-proteins, which lacks careful backup via biochemical and structural studies. In addition, the ionotropic hypothesis lacks support via carefully performed physiological in vivo studies in different insect species that paid attention to analysis of the distinct kinetic components of ORN´s odor/pheromone responses and that employ physiological concentrations and durations of odor/pheromone stimuli (please see our most recent publication by Schneider et al. (2025)).

(5.4) Nevertheless, structural studies on Orco do not support a cyclic nucleotide binding site, although PKC-based phosphorylation has been implicated in the fine-tuning/adaptation of olfactory signaling.

While structural studies did not find evidence for conserved known cyclic nucleotide binding sites on Orco, this does not exclude the presence of so far unknown binding sites, or via sites that fold out only after a specific sequence of previous phosphorylations of the many phosphorylation sites on Orco. Indeed, physiological studies in Drosophila presented evidence for cyclic nucleotide dependence of Orco after previous PKC-dependent phosphorylation (Getahun et al., 2013). Our ongoing in vivo experiments in hawkmoths further corroborate a PKC- and cAMP-dependent modulation of Orco. These studies will be published in a follow-up publication.

(6) Because only 5/11 LD and 7/10 DD animals showed daily rhythms, with averages lacking clear daily modulation, the methods are not sufficiently reliable enough to reveal novel underlying mechanisms of circadian rhythm generation. The reported results are therefore not yet reliable or quantifiable. To quantify their results, the authors should apply tests for circadian rhythmicity using methods such as RAIN, JTK CYCLE, MetaCycle, or Echo. The use of FFT and Wavelet is applauded, but these methods do not have tests of significance for rhythms and can be biased when analyzing data in which there could only be 1-3 circadian cycles. Because the conclusions appear to be based on 11-12 neurons that were recorded for 2-4 days, the reader is concerned that the methods are not yet perfected to provide strong evidence for circadian regulation of spontaneous firing of ORNs. The average data (e.g., Figure 3Bii and 3Cii) highlight the apparent lack of daily rhythms. In summary, the results would be more compelling if more than 50% of the recordings had significant circadian amplitudes and with similar periods and phases.

The long-term tip-recordings of intact hawkmoths are very challenging and take a very long time to accomplish, thus, we are very happy that we succeeded in obtaining so many of them (N=34). Since 5/11 LD recordings and 7/10 DD recordings revealed daily/circadian rhythmicity and since many other physiological recordings at different ZTs of different members of our laboratory all revealed ZT-dependent pheromone-transduction we can be certain that the physiology of hawkmoth antennae is under strict circadian control. Please see also our response to (4) above commenting the phase-dispersal of activity rhythms observed in our experiments, as well as in the behavior of hawkmoth males in the mating cage.

Nevertheless, we will follow the advice of the referees to apply additional tests for significance of rhythms in spontaneous activity, and we are thankful for the tests suggested that we were not aware of.

(7) The statement that circadian patterns of ORN firing are lost with the Orco antagonist (OLC15) is not strongly supported. The manuscript should be revised to quantify how Orco changed circadian amplitude in the 12 recorded neurons. Measures of circadian amplitude can avoid confusing/vague statements like Line 394 “low and high frequency bands appeared to merge during the activity phase around ZT 0 in the animals that showed clear circadian rhythms (N = 5 of 11 in LD)”. The conclusion that Orco blocks circadian firing appears to be contradicted by Figure 6, which indicates that ~6 of these neurons had circadian periods detected by wavelet. The manuscript would be strengthened with details about the specificity and reproducibility of the Orco antagonist. The authors quantify the gradual decrease in firing with the slope of a linear fit to estimate how the “effectiveness [of OLC15] increased over time.” They conclude that the drug “obliterated circadian rhythms and attenuated the spontaneous activity in several, but not all experiments (N = 8 of 12).” The report would be greatly strengthened with corroborating data from additional Orco antagonists and additional doses of OLC15 (the authors use only 50 uM OLC15).

We will revise our data analysis, according to the valuable suggestions of the referees.

However, based upon our previous studies with other Orco antagonists and different doses of OLC15 (Nolte et al., 2016) we found that 50 µM OLC15 is the best Orco antagonist dose in M. sexta to target Orco-dependent modulation of spontaneous action potential activity of hawkmoth olfactory receptor neurons. Please see also our response to (1).

(8) The manuscript includes several statements that are more speculation than conclusion. For example, there is no evidence for tuning or plasticity in this report. Statements like the following should be removed or addressed with experiments that show changes in odor response specificity or sensitivity: "ORN signalosomes are highly plastic endogenous PTFL clocks comprising receptors for circadian and ultradian Zeitgebers that allow to tune into internal physiological and external environmental rhythms as basis for active sensing." (Discussion Line 622). The paper concludes that (line 380) "mean frequency of spontaneous spiking and the frequency of bursting expressed daily modulation, and are both most likely controlled via a circadian clock that targets the leak channel Orco." This is too bold given the available results.

We will revise the discussion accordingly and clarify which statements are supported via published evidence and which are predictions based upon our novel hypothesis published in our opinion paper (Stengl and Schneider, 2024).

(9.1) Because Orco conductance is modulated by cyclic nucleotides, it remains highly plausible that circadian regulation occurs upstream at the level of signaling pathways (e.g., calcium, calcium-binding proteins, GPCRs, cyclases, phosphodiesterases).

We agree with the referees that it is very likely that there are multiple layers of interconnected feedback cycles that control Orco localization and activity. Our novel hypothesis suggests interlocked TTFL and PTFL control of physiological circadian rhythms, not strictly hierarchical TTFL control, which would require a daily turnover of membrane proteins and transcriptional control via the established TTFL clock in insect ORNs. We currently search for TTFL control at all levels of odor/pheromone transduction using ZT-dependent transcriptomics in combination with qPCR and single nuclear transcriptomics, involving also all the molecules suggested by the referees. These studies are ongoing, are very time- and money-consuming, and are beyond the scope of this manuscript.

(9.2) The possibility that circadian oscillations of cyclic nucleotides are generated by the canonical TTFL mechanism has not been excluded. In fact, extensive work in Drosophila has demonstrated that the TTFL-based molecular clock proteins are required for circadian rhythms in olfaction.

Our experiments that test circadian TTFL control at different levels of the cAMP transduction cascade in hawkmoth antennae are on the way and are part of another publication. We will revise our discussion accordingly.

The experiments published for TTFL dependent control of Drosophila olfaction that we are aware of (Krishnan et al., 1999; Tanoue et al., 2004) do not exclude interlinked PTFL and TTFL clocks. Krishnan et al. (1999) demonstrate that the TTFL clock in antennal olfactory receptor neurons correlates with circadian rhythms in odor responses measured in electroantennogram (EAG) recordings, not in single sensillum recordings as in our experiments. EAG recordings comprise not only voltage responses of the olfactory sensory neurons but also voltage changes generated in non-neuronal antennal cells such as trichogen and tormogen cells that built the transepithelial potential gradient via vATPases that generates the high K⁺ concentration in the sensillum lymph (Jain et al., 2024; Klein, 1992; Thurm and Küppers, 1980). In addition, EAG recordings most likely contain responses of afferent neurons originating from somata in the brain that maintain central control of the antennae. Thus, EAG recordings are difficult to interpret.

(11) A defining feature of circadian oscillators is the feedback mechanism that generates a time delay (e.g., PERIOD/TIMELESS repressing their own transcription). While the authors describe how cyclic nucleotides can regulate Orco conductance, they do not provide a convincing explanation of how Orco activity could, in turn, feed back into the proposed PTFL to sustain oscillations. For these reasons, the authors should consider:

a) Providing a broader discussion of non-TTFL models of circadian rhythms (e.g., redox cycles, post-translational modifications).

We will revise the discussion accordingly.

b) Reassessing Orco expression using a higher-resolution temporal sampling ({greater than or equal to}6 timepoints per 24 h).

We will add those experiments to the revised version of the manuscript (see our response to (2)).

c) Clarifying or revising the PTFL model to explicitly address how feedback would be achieved. Alternatively, the data may be more consistent with Orco conductance rhythms being regulated by post-translational mechanisms downstream of the canonical TTFL oscillator, as suggested by the Drosophila olfactory system literature.

We will revise the manuscript accordingly.

Minor weaknesses:

(1) The authors should compare the firing patterns of ORN neurons to the bursts, clusters, and packets of retinal efferent spikes reported in Liu JS and Passaglia CL (2011; JBR). By comparing measures in moths to measures in Limulus, the authors might be able to address the question: Is the daily firing pattern of ORN neurons likely a conserved feature of circadian control of sensory sensitivity?

We will revise the discussion accordingly.

(2) The methods need further details. For example, it is unclear if or how single neuron activity was discriminated and whether the results were compromised by the relatively large environmental fluctuations in temperature (21-27oC), humidity (35-60%), or other cues known to modulate spontaneous firing.

We will clarify the Methods section.

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This work has been peer reviewed in GigaScience (see https://doi.org/10.1093/gigascience/giaf097), which carries out open, named peer-review. These reviews are published under a CC-BY 4.0 license and were as follows:

Reviewer 3: Cristian Canestro

TO THE AUTHORS

In this MS entitled 'First chromosome-level genome assembly of the colonial chordate model Botryllus schlosseri (Tunicata)', Olivier De Thier and colleagues report the first chromosome-scale assembly of this colonial ascidian specie, paying special attention to differences with previous published assemblies and importantly between haplotypes. The MS is very well written, very easy and pleasant to read. This provides data of great quality and very relevant not only for the ascidian/tunicate community, but to the field of genome structural evolution. I firmly recommend it for publication, although I think that the authors could discuss it in deeper detail. Specially, I miss for instance a more elaborate discussion of the results in our understanding of the similarities and differences between clades that have been published in the last years (I have not been able to find some relevant articles in this regard cited in the bibliography). I also feel that a deeper analysis of the differences between haplotypes could be very interesting, unless they are artifactual effects of the assemblies. As mentioned below, unless this is part of a longer story for a different MS beyond the scope of this one, I encourage the authors to validate some of the differences they find between haplotypes, and try to correlate the structural variations, with differences in gene counts between haplotypes, and to explore whether these differences could be correlated with aspects of biological relevance. I miss, for instance, Venn diagrams with gene contents between previous assemblies, and the haplotypes/haploid genome here reported. In any case, I firmly recommend this MS for publications, since most of my suggestions are not intended to interrogate the results of the MS, but to improve it, but I also understand that some may go beyond the scope of this MS.

Minor points: Introduction Page 1: "the basic body plan of adult tunicates is highly conserved across the entire subphylum [3]". This sentence, which could be OK for ascidians, probably provides a highly simplified vision of Tunicate adult morphologies, specially comparing the divergent morphologies of Thaliaceans and Appendicularians. Please, elaborate the sentence.

To understand the comparisons between the data of this MS and previously reported genomes, it seems crucial to understand well the meaning of the "clades and subclades". Please, include in the introduction (or where needed), how are defined those clades, which are their origins and biological/geographical differences, … and all the critical information that will specially help non-tunicate readers to understand the results.

Results: The authors refer to the presence of large-scale genomic palindromes in Bs1 and Bs3. But it is unclear what are these structures. I suggest to please provide some more detailed explanation about the palindromic nature of these regions.

The data of haplotype-resolved assemblies is very interesting. I wonder if it is possible to somehow measure the amount of heterozygosity between haplotype 1 and 2, and those versus the previous versions of the genome, to better understand intra and inter-variation between subclades? The differences of the size of some regions between Colombera and this study, and even between haplotypes 1 and 2, are very interesting. I would find more informative to merge the three graphs of Figure S9 into one single graph, so we can also easily compare the different in sizes of the haplotypes with the haploid. If some of those differences are actually due to deletions, that would deserve further analysis. If this analysis is not part of another ongoing project that will be published somewhere else, I suggest identifying with a dot-plot some of those differences, specially between haplotypes, and validate with long-reads crossing those regions whether some of the deletions are real or artifactual. Please, include the dotplot graph together with the two haplotypes in figure S10. In those cases that could be real, it would be very interesting what genes are gone, and if those are not placed somewhere else in the genome as result of translocations, or those genes are actually gone and could explain some of the differences reported in the gen count between haplotypes.

The authors mentioned the presence of multiple structural variations, although some of which could be artifactual of miss-assemblies. Interestingly, the plot of the synteny blocks between the two haplotypes in figure S11 shows some of those structural variations, including cases of: - deletions: for instance, there are "blank" regions in Bs1A and Bs3A with no lines, which may reflect areas that are not present in the haplotype B. - duplications and translocations within chromosomes or between chromosomes of different haplotypes. Just looking to this plot, I wonder how the distribution of chromosomes between haplotypes is done. For instance, I see that Bs7B shares a duplicated synteny block with chromosomes Bs10B and Bs14B, but not with Bs10A and Bs10B, which means that the duplications are intra-haplotype present in B but not in A. But I wonder if it is possible that Bs10B and Bs14B could be in fact switched to haplotype A, and therefore there would be no duplication nor deletion in one of the haplotypes, just a simple translocation. I may be wrong in the interpretation, but I'm curious to understand the graph. In any case, again, as mentioned above, it would be worthy to validate some of those variations with long reads, which could illuminate the biological relevance between the haplotypes and discard potential artifactual errors of the assemblies.

I notice that in figures 7 and S13, some lines are thicker than others. Is this because many "thin" lines are overlapped, and they look like a "thick" line. Otherwise, the visual effect of different thicknesses could be misleading. Please, clarify.

In the analysis of the Hox cluster the authors say "[…] our new assembly revealed that B. schlosseri's Hox genes are not scattered. Instead, eight of them were clustered on the second largest scaffold (Bs2), whereas two other ones are found on the 15th largest scaffold (Bs15)." Generally, the description of the Hox gene in a cluster refers to the fact they are in the vicinity, with near not many other genes in between Hox genes. Therefore, I would not describe that eight Hox genes are clustered by the simple fact that they are in the same chromosome (maybe even in different arms).

This work has been peer reviewed in GigaScience (see https://doi.org/10.1093/gigascience/giaf105), which carries out open, named peer-review. These reviews are published under a CC-BY 4.0 license and were as follows:

Reviewer 2: Brendan Reid

The authors of this work provide a fantastic addition to the genomic resources currently available for marine turtles with five new, apparently high-quality reference genomes. These new resources enable a number of interesting cross-species analyses in this group, including phylogenetic reconstruction, inference of demographic history, and identification of hotspots of diversity and divergence. I though this paper was quite clearly written and easy to read overall, and I have one major and a few more minor comments/suggestions.

Major comment: there is an extensive literature on hybridization among marine turtle lineages (see Vilaca et al. 2021, https://doi.org/10.1111/mec.16113, for a recent genomic example), with lots of evidence for ancient gene flow after initial lineage divergence as well as recent hybridization. The authors do not really mention this phenomenon at all, and since I think it has a lot of bearing on all of the results it would make sense to re-think your findings in light of the fact that some level of gene flow has occurred. Would extensive synteny/lack of genomic rearrangements potentially enable hybridization? Is overall low divergence among lineages potentially a function of gene flow? Are regions of high divergence the result of selection (as you suggest), or could these regions potentially be resistant to gene flow? I believe that IQtree assumes a strictly bifurcating tree, and gene flow can influence PSMC inferences (see Mazet et al. 2016, https://doi.org/10.1038/hdy.2015.104) - how would gene flow among lineages affect your inference of divergence dates and demographic histories?

MInor commentsL [note - line numbers would have been helpful for providing comments on specific items! I will refer to the lower-left page numbers and paragraph instead]:

page 3, paragraph 2: Some of the applications you refer to here don't seem terribly germane to the relevance of "genomic resources" in management and conservation per se, and several are just methods using some kind of genetic data ... e.g., "abundance"/close-kin mark recapture doesn't require full genomes (and the reference you cite used microsat data), and the "community"/eDNA applications don't generally rely on genomes but instead on databases of a few (usually mitochondrial) genes. Either include methods that truly benefit from the development of high-quality reference genomes or broaden this to something like "growth in molecular ecology techniques".

page 4, paragraph 2: last sentence is a bit of a run-on, could break this up a bit.

page 10, paragraph 3: for me, the ROH methods need some additional explanation and interpretation. The more detailed methods indicate that the ROH were identified on the basis of lower-than-average heterozygosity rather than true homozygosity - I can understand why this might have been done (since the baseline level of heterozygosity varies across species) but it still seems a bit arbitrary and could risk mistaking stretches with simply low variation for IBD tracts. I wonder if a ROH-detection method like ROHan that explicitly incorporates baseline genomic heterozygosity into its model would be more appropriate for comparing results across species and could give different results. I also question a bit the interpretation of these low-diversity tracts as evidence of inbreeding per se. The authors do not comment much on the length distributions of these ROH - given that many of them are quite short I would expect that if there was mating between close kin it probably happened far back in the past and the IBD tracts have been broken up by recombination.

page 11, paragraph 2: for PSMC analyses it is important to note the method assumes that differences in coalescence time/Ne across the genome result from demography alone. If portions of the genome are under balancing/diversifying selection (such as the areas of high diversity that you detect in this study), the local Ne for inferred these regions would be expected to be larger than the rest of the genome, which could lead to the spurious detection of population expansion or contraction (more likely a contraction for balancing selection). See Boitard et al. 2022 (https://doi.org/10.1093/genetics/iyac008) for a more detailed treatement. I would try excluding the regions putatively under diversifying selection and re-run PSMC to see if your inferences change.

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Reviewer 2: Ellen Visscher

The paper introduces a python package for imputation, filtering, segmentation, feature extraction and visualisation of CNA profiles. It explains some of the elements of the package, and then demonstrates how data from multiple cohorts can be processed and combined using the package preprocessing pipeline. The authors then use processed data from 3 different cohorts to perform cancer type prediction using a CNN. From this, they get an interesting result to find a biomarker that differentiates two different lung cancers. Throughout, they show visualisations using their package. The package itself seems well documented and designed to be used. There is some clarification required in the methods section specifically around the CNN training and the models therein. There is also one major question of whether all the preprocessing steps are actually required for the downstream CNN analysis. Overall, however, this is a well written manuscript, providing a useful software tool for further analysis of CNA data.

Major comments: - CNN section- how are the segments decided- is it based on all the training data, or just data in a batch? - Throughout the results pertaining to figure 3A-C, you call it test accuracy- to be clear is this is based on your CV hold outs? This should be reworded everywhere to reflect this. As cross validation indicates, this is not a test set and is a validation set- which is also the way you use it. - Regarding the above, you have a comment saying: "the best test accuracy without cross-validation was 92.34%". Could you please clarify what you mean by this. Only in the CNN section do you describe your training approach, which does not mention a test or separate validation set. - It reads slightly unclearly- you have a section called "model transfer", but are you training 3 different models- one per dataset? You only have one figure for training results which suggests one dataset, but then you have this section called model transfer? - Re all the above, please dedicate a small subsection in methods making this clearer. Are there dedicated test sets? If your main results are for aggregated data, then what are you testing on to ensure generalisability? What is the point of training the 3 different models on 3 different datasets? Perhaps it would make more sense to hold one dataset out as your test set. In some ways, that is what the model transfer is showing, but it would be less confusing to clarify that aim instead of suddenly introducing 3 models. - If the CNN architecture is essentially the same as in Attique et. al., the performance is basically the same and they use only CNs a gene locations- how does this demonstrate that the preprocessing from CNSistent is necessary or advantageous for this task? Maybe having a result which combines CN calls naively over gene locations and comparing to this across the aggregate datasets would be a good way of comparing? I.e showing that preproccessing does offer an advantage when combining different datasets together? Also because this is what you argue in your abstract. For this analysis you would have to make sure you also compare across the same samples to differentiate between filtering/other preprocessing steps. - In Figure 3I, you say "notice the similarity of chromosome 3 pattern for the correctly classified LUSC samples (red) and the misclassified ones (orange)". This is confusing because the orange and red are not similar. In fact for this whole section, it seems that figure 3I does not align with what you are saying?

Minor comments/errors: - Clarification on why CNSistent needs a reference genome if it's dealing with segments? How is this information used- is it just for the known gaps? - Your caption of Supplementary Figure 1 has a typo about a breakpoint at 16 instead of 14. - You do not explain how you use the knee pt to filter (i.e is it samples above/below the knee pt.) - Your CNN graphic is difficult to interpret and non-standard. - CNN section should clarify at the beginning what the input is and what the output is (i.e a prediction that a sample belongs to a particular cancer type) before explaining the architectural details. - Even though you control for class imbalance, some cancer types are so poorly represented it is unlikely a CNN could learn that, you do kind of mention this in the discussion, but maybe some sort of minimum threshold for inclusion would make sense. - For Fig2D you refer to it as GND, but the axes/title says hemizygosity-are these things equivalent? E.g could have 3-3, low hemizygosity but not diploid? Or if it's aggregated across the whole genome its assumed equivalent? - There is a grammatical error "Runtimes decreased in a near-linearly with the number of compute cores" - You make a comment that "We therefore suspect some TCGA lung cancers might be cases of co-occurring adeno and squamous carcinomas." This is a possibility but given pleiotropy of many phenotypes- it may also be that the biomarker is not always unique to squamous carcinomas.

Suggestions/Nice to haves: - Maybe make it clearer inside the paper what visualisations come with CNSistent. Looking at the software documentation, there's obviously a lot of useful visualisations that come with that- and some of them you have used in Figure 3 for e.g. - Given there are more total CN callers, maybe good to mention somewhere how CNSistent would work for total CNs only. - You remove profiles that you say are uninformative, could you not include this and then just show how accuracy correlates with no. of break-pts (for e.g). In some ways one might think that there could be useful information in few alteration profiles- because those alterations might be more upstream/causal. - The aggregation step could maybe affect downstream analysis. I.e taking the average could introduce CNs that were never called. Even using min/max- this implies a constant copy number in that region, which may lose information- e.g if it is a functional region having two diff CNs across gene might imply non-functionality. Did you explore the effect of aggregation step? Perhaps taking a small enough resolution of segment types would account for this anyway.

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Reviewer 1: Christoph Dieterich

In this manuscript, the authors present a benchmark to assess the performance of different tools designed for estimation of polyA tail length from Nanopore direct RNA-sequencing data. These tools include tailfindr, nanopolish, Dorado and Boost Nano. Benchmarks on tools and algorithms to analyze Nanopore data, both third party tools and official ONT releases, are of utmost importance for the field. The use of synthetic constructs with known ground truth is recommended as well. Consequently, this study has the potential to provide a significant contribution to the field.

In the current form, I can however not recommend it for publication in GigaScience. My major concerns are: a) Use of only RNA002 data. This chemistry is outdated and thus the Benchmark is only relevant for old, possibly already published data. A comprehensive Benchmark should also include RNA004 and available tools there (at least Dorado). b) The current data set only contains two polyA tail length, which are relatively short and do not cover longer polyA tails that are common e.g. in mammalian cells. A proper Benchmark should show the performance of the analyzed tools over a range of polyA tail lengths.

Minor comments: 1) Abstract: "All four tools generate mean tail-length estimates which lie within 13% of the correct value." The value of 13% is given in the Abstract from the submission system, wherease the abstract in the Main text says 12%. Which value is correct? 2) Background, first paragraph: the role of the polyA tail in RNA circularization, which is required for efficient translation of cellular mRNAs is not mentioned. Reference is missing for "is increasingly recognised as a dynamic process which influences timing and degree of protein production." 3) Background, second paragraph: Chiron seems to be a relatively old basecaller (no models for new chemistries). It should be mentioned here that it is required for BoostNano. 4) Mis-priming of internal polyA sites may an important confounding (and currently overlooked) source of errors in Nanopore sequencing. This should be quantified properly and analyzed in more detail (length of these stretches, influence of other nucleotides within the A-rich stretch, etc.). Should be done as well on whole transcriptome data with more possible mispriming sites. 5) Why do the authors think that the poly(T) stretch of the RTA might be truncated? This is composed of DNA oligos, which should be quite stable 6) What are the parameters for filtering used by Dorado and BoostNano? Can the authors explain, why the filtered reads differ? 7) Dorado seems to systematically underestimate polyA tail length. Is this true also for data generated with RNA004 chemistry and longer polyA tails?

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Reviewer 1: Finlay Maguire

In this paper the authors train a ResNet-based model to predict whether individual 10,000 sample chunks of nanopore signal data originate from live or killed bacterial isolate cultures. From live and UV-killed (at exponential phase) E. coli K-12 cultures DNA was extracted and sequenced using separate R10.4.1 flowcells on a MinION. Signal data from each read in the live and dead extractions were then processed by discarding the first 1,500 samples and dividing the remaining signals into 10,000 sample chunks. These were then split into a balanced 60:20:20 train, test, and validation datasets with the constraint that no two chunks from the same read would end up in the same dataset (e.g., chunk 1 and chunk 2 of 1st read in the killed culture would hypothetically be separated into train and test). During this they also explored/compared the impact of chunk size, model architecture, and performance of a sequence based model using the E. coli data. With a nicely performed class-activation map and masking approach they then identified the signal regions most strongly associated with dead-predictions (such as twisting/kinking/pore blockage of DNA around pyrimidine dimers). Finally, they applied their trained model to a live and heat-killed Chlamydia abortus culture and compared their results to stained microscopy and propidium monoazide PCR measures of viability. They found equivalent performance on the C. abortus data to their E. coli data (despite a different killing-method and taxa).

The manuscript is well written and the methods are clearly described (including well documented code and deposited data). The authors explainability methodology is excellent although it would have been nice to see a bit more in-depth interpretation of those results. The authors have also presented a convincing case that nanopore signal data does contain information that can be used to distinguish signal chunks from live and dead bacterial monocultures. This methods has the potential to be useful in clinical and environmental genomics if it can be extended to more heterogeneous metagenomic samples. However, despite the title and framing of this manuscript (i.e., "metagenomics"), their analyses do not involve any metagenomic data and their results so far do not demonstrate if this is fesible. Currently, the overall framing (and title) of the manuscript is not appropriate given the work performed at this point. Similarly, given that both E. coli and C. abortus "dead" cultures resulted in median read length less than half the live cultures, the authors do not fully make the case that the signal and ResNet approach is actually required relative to simpler baseline models. Finally, although they did evaluate performance on a complete separate dataset, the authors should at least explore/quantify the correlation of live/dead prediction across chunks of the same read given the default expectation of non-independence of signal chunks from the same read.

Major - Although the title and framing of the paper suggest that the authors are classifying live and dead bacteria in metagenomic datasets, the actual experiments and method developed are entirely based around sequencing of cultured clonal bacterial isolates. Metagenomic datasets are going to have considerably more heterogeneity in viability, species composition, and DNA signal characteristics. Given this, the paper's title, introduction, and parts of the discussion are a bit of an oversell and inappropriate. This manuscript should be revised to more clearly reflect the work actually performed.

• This paper doesn't establish whether a ResNet + Signal approach actually outperforms a much simpler baseline. For example, given there is a clear extraction and median read-length differences between live and dead samples, it is possible that a much simpler logistic model using basic features such as read length and/or translocation could perform equivalently.

• Although the C. abortus analysis demonstrates limited impact of leakage, I'm still a bit concerned that the potential non-independence of chunks from the same read (i.e., chunk 1 and chunk 3 of the same read are more likely to share similar live/dead signal characteristics than Chunk 1 and 3 of different reads). By not having multiple chunks of the same read in the training, validation, or test datasets the authors may have avoided issues with longer-reads being more represented in their datasets. However, this has the potential to introduce data leakage between train and test set (which may impact generalisability when they attempt to extend this method to metagenomics). I think this paper would be improved by some exploration of the correlation of live/dead prediction across chunks of the same read. How often do different chunks of the same read disagree? How does this impact the overall performance of the model? Does taking the average prediction across chunks of the same read improve or degrade performance? Would this problem be better suited to a multiple instance learning approach (i.e., a live/dead label applied to all chunks from a single read) especially in more heterogeneous datasets? To what degree do longer reads with more chunks contribute disproportionately to the overall performance in the C. abortus dataset?

Minor

• SRA records don't seem to be live yet (https://www.ncbi.nlm.nih.gov/sra?linkname=bioproject_sra_all&from_uid=1123127)

• Are the actual pod5 files available?

• Read-level performance should be analysed and reported.

• Figure 1B: the test subplot numbers are almost too small to read - they may benefit from being its own panel.

• Plot axes labels are not always clear (e.g., Figure 3) percentage of what? Chunks? or Reads? It would be nice to see consistent capitalisation of labels and legends.

• Predictions on viable E. coli and viable C. abortus seems surprisingly similar (91.44% vs 91.34% viable and 8.56% vs 8.66% dead) despite different taxa, potentially underlying viable cell proportion, and output probability densities. This would benefit from further discussion/analysis - do misclassified chunks have any common characteristics? Would you expect the E. coli to have similar microscopy/PCR measured viability percentage as the C. abortus.

• Would be good to see a bit more discussion/exploration of impact of mixed live/dead cells given ~37.6% viability measure in the C. abortus sample (e.g., how well do models perform with different ratios of live/dead reads) - could potentially be achieved using in-silico spike ins).

I like the phrase "antidote to the uncritical acceptance" quite a lot. At first, you may think that an "uncritical acceptance" isn't necessarily a bad thing. However, thinking about it more, do you really want to just blindly accept the world around you? Looking critically at yourself and the world allows you to make changes and work to improve the lives of yourself and others, among many other things, simply because you dared to question.

This is a very interesting way to think about justice. The author introduces this method to imagine a fair society with no bias. The reason this works so well is because not knowing what ur position in society will be, allows you to genuinely try ur best to make society as fair and enjoyable as possible for every individual

I think this is one of the most important reasons why we need to study philosophy. When we repeat our daily routines and become accustomed to them, we tend to overlook the injustices within them or we may not even recognize them as injustices. Philosophy enables us to think more critically about the society we live in, its institutions, and the impact they have on us.

By asking so many bizarre questions that one normally does not consider on a day-to-day basis, it pushes us outside of our comfort zone and forces us to take a step into the unknown. This encourages our brains to work in different ways that it may normally not think, ask questions beyond our general scope of thinking, and create new connects and ideas that we may normally have not considered. I think this kind of emphasizes the importance of philosophy because it teaches us how to react when we are pushed outside of our comfort zone and how to think beyond our normal flow of consciousness.

We are so used to the life we live that we in ways we become comfortable in it. When imagining a different reality, one in which they may be less high up/wealthy, it becomes difficult for some to acknowledge just the amount of privilege they once had. The "Theory of Justice" gives people a different perspective on life and how different each and every person's life is from one another.

Though it was a little difficult for me to picture this in real life as it is not realistic that society is completely unaware of ones capabilities before choosing their position in the social hierarchy, I think that this is fascinating to imagine. We often forget that we may not be as secure in our social status or career as we think we are so it is important to be aware of those of lower status around you and not take your position for granted.

I think this is a very interesting start to this article! It puts us into the shoes of someone in a difficult position, in which they must tirelessly work away to simply have a shot at a decent, livable lifestyle. I feel that this scenario they painted for us so vividly is really powerful when leading into this question, because I think people in the current climate of the world tend to underestimate the importance of philosophy, or don't really think about it at all. While maybe a lot of us don't completely relate to the situation of the young mother, a lot of us DO have our own struggles and might find ourselves lost in the grueling work that may come with everyday life. And when simply going through with our daily lives is hard enough, why should we bother with philosophy? Personally, I don't really think about the idea of philosophy at all, and I never really thought it would be relevant to me based on what I want to do in life. And when people don't think something is relevant, why bother with it, right? Life is busy enough as it is. But really, it probably has a lot more relevancy in my life than I think, and I believe that this idea is somewhat being conveyed in this part. That's just how I saw this paragraph, but I thought it was a strong opening!

This is a brilliant way to describe others lived experiences and how what might not affect you, could affect someone else. Using philosophical teachings can reveal the privileges of some and the shortcomings of others and hopefully create a better understanding of everyones blindspots in day to day life. Truly a very powerful and humbling exercise that can help create common ground and allow others to empathize with eachother and hopefully create a more just society.

This idea that we must get rid of the idea of "safety" within our lives and experiences can be imagined as a vision of the future that we as people, don't want to imagine. Being a "poor mother" or a "garbage truck driver" can be thought of as a disappointing fate to many who attend college, it can even be a fate so poor in the minds of students, that it serves as motivation in their eyes ; to not be like "them" , its a phrase that sticks with many who hold themselves to a high idea of success. But I believe and resonate with this idea of harnessing imagination as it broadness our perspective on education and life, because no matter how safe we feel behind a wall of education or wealth, there can always be a force of society that challenges our goals.

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Reviewer 4: Wai Yee Low

Review of "A comprehensive water buffalo pangenome reveals extensive structural variation linked to population specific signatures of selection". This is an impressive work at the frontier of buffalo genomics. I truly enjoy reading the work and my questions/comments are aimed at improving it further. My detailed comments are below: Line 30: I think it is better you include the actual number of publicly available assemblies used to create the pangenome graph. Line 71: There is now a swamp buffalo reference genome with annotation too (NCBI accession: PCC_UOA_SB_1v2). Perhaps consider to cite the swamp buffalo ref https://academic.oup.com/gigascience/article/doi/10.1093/gigascience/giae053/7753516 and rewrite the sentence to say a pangenome can be used for both swamp and river, but a single linear ref from either subspecies for read mapping is not good enough. Line 79: "highlighted" Line 82: What do you mean by "higher quality"? The assemblies have been discussed in this review: https://www.frontiersin.org/journals/genetics/articles/10.3389/fgene.2021.629861/full Line 105: Technically, the graph method for bovine species, which includes water buffalo, is being investigated by the Bovine Pangenome Consortium (BPC). However, nothing useful has been published on the buffalo graph but perhaps consider citing the BPC since your paper overlaps with it (https://genomebiology.biomedcentral.com/articles/10.1186/s13059-023-02975-0). Line 165: It will be good if you add a bit more context of the PanGenie method here as the researchers in buffalo community are not used to this. Additionally, it will be great if all code is made available on GitHub or as Supplementary Info. Line 170: To produce phase pangenome graph, don't you need all input assemblies to be phased? All are input assemblies phased? The UOA_WB_1 is locally phased, not phased throughout the genome. Line 235: "a list of 403 unrelated individuals." What does this translate to in terms that geneticists can understand? Do you mean siblings have been removed? Or individuals sharing the same grandparents were removed? Line 246: Can you please explain how did you get the coordinates to match between the GATK and PanGenie method? You'll need matching coordinates for concordance analysis. As I understand it, the GATK was based on UOA_WB_1? Line 254: Why these 3 chromosomes? Line 257: If you had not filtered for relatedness, how will it impact the selective sweep work? I think including some context will help the readers. Line 259: do you mean at least six samples per group? If yes, is 6 samples enough? Line 261: genotype quality less than 25 according to bcftools? Since you only used biallelic variants, please provide the breakdown between biallelic and multiallelic. Line 281: "… we first PacBio HiFi sequenced one female" Please rewrite this. Line 282: How common are these two breeds in percentage? Line 291: Is this already known? Perhaps cite the literature to show the agreement with previous studies? Fig 1D: This is a bit too small to see especially the SV distribution at the bottom. I can hardly see the median? Line 310: Why did you choose UOA_WB_1 as the reference? Line 311: the ~32.8 mil variants are comprised of SNPs as well? Fig 2: This is probably a panel of a figure but should not be the entire figure. The size of the circle indicates sample size but there should be a legend on the plot for this to say the sizes, right? Darker colour should be used to highlight the countries with samples instead of white? Maybe this could be a Supp figure too. Line 356: S Figure 4 and 5 should be main figures? You will need to annotate the abbreviation of sample-country in the legend of S Figure 5. Line 360: "To enable reuse we have made this dataset available …" The dataset should be made available to reviewers? Line 368: "76% of SNVs were called by both callers" 76% seem low. Also, called does not mean concordant. What is the concordance among called SNVs in both? Did the pangenome approach called most of the variants found in GATK? If not, what might be the reasons? Fig 3B: It is not immediately clear what the difference is, between non repetitive and repetitive regions. The overlapping text in the x-axes makes it hard to read. Line 390: "Analyses such as the study of selective sweeps or genome-wide association studies where low frequency variants are often filtered out will benefit less from the advantages of GATK, particularly given its longer run time." From here on, in this paragraph, it's Discussion, not Results. Line 418: Why human? Could you use cattle? Line 427: I tried the browser and not sure what I can learn from it. It will be helpful if there is a README with some examples on what can be explored. Line 450: How large before you considered it as larger variant? Is this ability to study larger variants still hold despite using only ~10 assemblies in the graph? The use of short reads for selective sweep study will still benefit from being able to incorporate these larger variants? As I understand it, the larger variants were found only from graph, not from the short reads. As such, the selective sweep may not be associated with any larger variants? Line 470: Fig S8 should be a main figure? Line 513: Instead of uniprot link, perhaps consider including this as Supplementary info or text. The info in the link may change in the future. Line 551: However, without scaffolding, the assemblies of Pakistani river buffalo may not be good enough to function as reference genomes for river buffalo? Line 552: When considering new bases, did you do this for each assembly independently or the new bases were discovered cumulatively? Line 581: Some of my questions at Line 450 can be discussed here. Line 586: Perhaps consider discussing the limitations of the small number of assemblies used to create the graph. As such, many SVs are likely still missing and we are still unable to properly assess allele frequency of these larger SVs. Additionally, while some SVs may not be considered as large in this work, it does not mean they have no impact.

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Reviewer 1:Will Dampier

The manuscript presented by Nguyen et al. is well written, well researched, and well executed. The use of this new "wavelet style" neural network shows both an increased training efficiency and improved accuracy at detecting influenza subtypes for surveillance. However, I think their comparison to a 'plain' Transformer model does not take advantage of the improvements in pre-training and transfer-learning that have become standard practice in deep-learning. I have also included some stylistic suggestions to improve the figures as presented. After addressing these comments, I believe that this will become a very strong manuscript.

Major Comments:

The authors present a comparison between their new wavelet architecture and a standard transformer architecture using a one-hot encoded vector of amino-acids. I believe that this is the correct 'null model' to compare your wavelet architecture to, however, it does not represent the 'state of the art' in utilizing transformers for sequence analysis. As I'm sure the authors are aware, the disadvantage of transformers is that they take an extensive amount of training (they note the transformer only models take 2-4X more training epochs to converge). However, the advantage they bring is that they can be extensively trained for one task and then transfer that learning to another related task. A number of models have been pre-trained on giant collections of proteins Asgari et al, https://doi.org/10.1371/journal.pone.0141287 and Rives et al https://doi.org/10.1073/pnas.2016239118 which then allow one to transfer that knowledge to different domains with fewer examples such as demonstrated in Dampier et al https://doi.org/10.3389/fviro.2022.880618. It would be interesting to see whether your wavelet model defeats these pre-trained models with transfer learning. If you showed that, you could argue that there is no need for the extensive expense of 'foundational models'.

The authors discuss that there is a significant imbalance in the training set and they used up-sampling and limiting to balance out the class representation. Since the classes are not equally represented, the model may not be equally able to predict each class. And the high metrics may only be a representation of its ability to predict the popular classes correctly. The authors should include an additional set of figures (supplemental is fine) that show the metrics broken out by Subtype. It would also be interesting to see a graph of the class-size (before up-sampling) vs F1-score (or another metric) on that class. This could provide lower-bounds for how many samples are needed to train the model.

Minor Comments:

Figures 3, 4, and 5: These would benefit from a linked y-axis. It is hard to compare across A/B/C/D when the axes have different y-limits.

Author response:

We thank both reviewers for their valuable comments. We have prepared a point-by-point response below.

Reviewer #1 (Public review):

Weaknesses:

(1) The conclusions regarding the links between neural and behavioral mechanisms are mostly well supported by the data. However, what is less convincing is the authors' argument that their study offers evidence of 'priming'. An important hallmark of priming, at least as is commonly understood by cognitive scientists, is that it is stimulus specific: i.e., a repeated stimulus facilitates response times (repetition priming), or a repeated but previously ignored stimulus increases response times (negative priming). That is, it is an effect on a subsequent repeated stimulus, not ANY subsequent stimulus. Because (prime or target) stimuli are not repeated in the current experiments, the conditions necessary for demonstrating priming effects are not present. Instead, a different phenomenon seems to be demonstrated here, and one that might be more akin to approach/avoidance behavior to a novel or salient stimulus following an appetitive/aversive stimulus, respectively.

(2) On a similar note, the authors' claim that 'priming' per se has not been well studied in non-human animals is not quite correct and would need to be revised. Priming effects have been demonstrated in several animal types, although perhaps not always described as such. For example, the neural underpinnings of priming effects on behavior have been very well characterized in human and non-human primates, in studies more commonly described as investigations of 'response suppression'.

We thank the reviewer for these critical comments. After careful consideration of both reviews, we agree that “priming” may not be the most accurate term to describe the behavioral phenomenon. We plan to revise our terminology throughout the manuscript accordingly to better capture the generalized nature of the effect we observe.

(3) The outcome measure - i.e., difference scores between the two odors or odor and non-odor (i.e., the number of flies choosing to approach the novel odor versus the number approaching the non-odor (air)) - appears to be reasonable to account for a natural preference for odors in the mock-trained group. However, it does not provide sufficient clarification of the results. The findings would be more convincing if these relative scores were unpacked - that is, instead of analyzing difference scores, the results of the interaction between group and odor preference (e.g., novel or air) (or even within the pre- and post-training conditions with the same animals) would provide greater clarity. This more detailed account may also better support the argument that the results are not due to conditioning of the US with pure air.

We use the PI score as a standard metric to quantify all the odor preference in behavioral assays because it allows for robust comparison across different genetic or treatment groups under the same experimental setting. In T-maze, real time tracking of fly trajectories is technically difficult. With olfactory arenas, we showed some examples of fly distribution in quadrants over the entire odor choice test period (Figure 2—figure supplement 2) for both pre-trained and post-trained groups and discussed the trajectories in Discussion. We will ensure this point is clarified in the revised text.                       

Reviewer #2 (Public review):

[…] They finally recorded from different mushroom body output neurons, including the one (MBON-γ4γ5) likely affected by the increased activity of the corresponding γ4 reward dopaminergic neurons after shock preexposure. They recorded odour-evoked responses from these neurons before and after shock preexposure, but did not find any plasticity, while they found a logical effect during spaced cycles of aversive training.

We thank the reviewer for the summary. We would like to clarify that we did, in fact, observe plasticity in MBON-γ4γ5 following shock exposure, as shown in Figure 4B.

Overall, the study is very interesting with a substantial amount of behavioural analysis and in vivo 2-photon calcium imaging data, but some major (and some minor) issues have to be resolved to strengthen their conclusions.

(1) According to neuropsychological work (Henson, Encyclopedia of Neuroscience (2009), vol. 7, pp. 1055-1063), « Priming refers to a change in behavioral response to a stimulus, following prior exposure to the same, or a related, stimulus. Examples include faster reaction times to make a decision about the stimulus, a bias to produce that stimulus when generating responses, or the more accurate identification of a degraded version of the stimulus". Or "Repetition priming refers to a change in behavioural response to a stimulus following re-exposure" (PMID: 18328508). I therefore do not think that the effects observed by the authors are really the investigation of the neural mechanisms of priming. To me, the effect they observed seems more related to sensitisation, especially for the activation of sweet-sensing neurons. For the shock effect, it could be a safety phenomenon, as in Jacob and Waddell, 2020, involving (as for sugar reward) different subsets for short-term and long-term safety.

As noted in our response to Reviewer #1, we plan to revise our use of the term “priming” in the manuscript to more accurately interpret the behavioral phenomenon.

(2) The author missed the paper from Thomas Preat, The Journal of Neuroscience, October 15, 1998, 18(20):8534-8538 (Decreased Odor Avoidance after Electric Shock in Drosophila Mutants Biases Learning and Memory Tests). In this paper, one of the effects observed by the authors has already been described, and the molecular requirement of memory-related genes is investigated. This paper should be mentioned and discussed.

We thank the reviewer for bringing this important reference to our attention. We will cite the Preat (1998) paper and discuss its relevant findings in relation to our own in the revised manuscript.

(3) Overall, the bidirectional effect they observed is interesting; however, their results are not always clear, and the use of a delta PI is sometimes misleading. The authors have mentioned that shocks induced attraction to the novel odour, while they should stick to the increase or decrease in preference/avoidance.

The ΔPI is calculated either as (trained PI – mock PI) for different animals or as (post PI – pre PI) for the same animals, with the specific calculation clarified in each figure legend. A positive ΔPI signifies an increase in preference for the odor, which is equivalent to a relative attraction or a decrease in avoidance.

As not all experiments are done in parallel logic, it is not always easy to understand which protocol the authors are using. For example, only optogenetics is used in the appetitive preexposure. Does exposing flies to sugar or activating reward dopaminergic neurons also increase odour avoidance? The observed increased odour avoidance after optogenetic activation of sweet-sensing neurons involve reward (e.g., decreased response) and/or punishment (e.g., increased response) to increase odour avoidance?  

We used different behavioral assays (T-maze or arena), stimuli (real shock or optogenetics), and protocols (different or same animal groups) to robustly demonstrate the phenomenon across platforms. We explained each protocol in the figures or texts, and we’ll make them clearer to follow in the revised version. We focused on activating a clean set of sugar sensing neurons because this optogenetic stimulus is an effective and efficient substitute to real sugar. We agree that testing reward dopaminergic neuron activation is a logical extension and will consider adding these experiments in the revised work.

The author should always statistically test the fly behavioural performances against 0 to have an idea of random choice or a clear preference toward an odour.

Our primary focus is on the change in preference induced by training, rather than the innate odor preference itself, which can be highly variable due to physiological and environmental factors. Statistical testing against 0 for innate preference scores is not standard practice in this specific paradigm, as the critical question is whether a treatment alters behavior relative to a control.

On the appetitive side, the internal hunger state would play an important role. The author should test it or at least discuss it.

For appetitive experiments, we always starve the flies on 1% agar for two days prior to behavioral tests to standardize their hunger state. We will consider adding fed flies as control groups in the revised work.

(4) The authors found a discrepancy between genetic backgrounds; sometimes the same odour can be attractive or aversive.

We observed minor discrepancies in innate odor preferences across genetic backgrounds, which is a known and common occurrence. Different genotypes and temperatures can result in different baseline PI scores. However, the key finding is that the relative change in odor preference following an aversive stimulus is consistent: it increases the relative preference for an odor compared to air. This sometimes reverses valence (aversion to attraction) and other times simply reduces aversion. Our analysis focuses on this consistent, relative change.

Different effects between the T-maze and the olfactory arena are found. The authors proposed that: "Punishment priming effect was still not detected, probably due to the insensitivity of the optogenetic arena". This is unclear to me, considering all prior work using this arena. The author should discuss it more clearly.

The punishment effect with CS+ present was reliably detected in the T-maze (Figure 1A) but was not significant in the olfactory arena (Figure 2—figure supplement 1B-C). We hypothesize that the olfactory arena assay is less sensitive than the T-maze for detecting such subtle behavioral changes. This is evidenced by the fact that even classical odor-shock conditioning yields lower PI in the arena (typically ~0.4) than in the T-maze (~0.8), likely due to the greater distance flies must explore and travel. The higher variance in the arena may therefore mask more modest effects. Here the effect under investigation was induced by optogenetically activating only a small subset of aversive dopaminergic neurons, a stimulus that is likely weaker than full electric shock. This reduced stimulus strength may have contributed to the challenge of detecting a significant effect in the less sensitive arena paradigm.

They mentioned that flies could not be conditioned with air and electric shock. However, flies could be conditioned with the context + shock, which is changing in the T-maze and not in the optogenetic area.

While flies can be conditioned to context, during the optogenetic stimulation period in the arena, the light is delivered uniformly across all four quadrants. Therefore, any potential context conditioning would be equivalent across the entire chamber and should not bias the final distribution of flies between the odor and air quadrants during the test, nor affect the calculated PI score.

Author response:

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

Reviewer #1 (Public review): 

Summary: 

The authors revealed the cellular heterogeneity of companion cells (CCs) and demonstrated that the florigen gene FT is highly expressed in a specific subpopulation of these CCs in Arabidopsis. Through a thorough characterization of this subpopulation, they further identified NITRATE-INDUCIBLE GARP-TYPE TRANSCRIPTIONAL REPRESSOR 1 (NIGT1)-like transcription factors as potential new regulators of FT. Overall, these findings are intriguing and valuable, contributing significantly to our understanding of florigen and the photoperiodic flowering pathway. However, there is still room for improvement in the quality of the data and the depth of the analysis. I have several comments that may be beneficial for the authors. 

Strengths: 

The usage of snRNA-seq to characterize the FT-expressing companion cells (CCs) is very interesting and important. Two findings are novel: 1) Expression of FT in CCs is not uniform. Only a subcluster of CCs exhibits high expression level of FT. 2) Based on consensus binding motifs enriched in this subcluster, they further identify NITRATE-INDUCIBLE GARP-TYPE TRANSCRIPTIONAL REPRESSOR 1 (NIGT1)-like transcription factors as potential new regulators of FT. 

We are pleased to hear that reviewer 1 noted the novelty and importance of our work. As reviewer 1 mentioned, we are also excited about the identification of a subcluster of companion cells with very high FT expression. We believe that this work is an initial step to describe the molecular characteristics of these FT-expressing cells. We are also excited to share our new findings on NIGT1s as potential FT regulators. We believe this finding will attract a broader audience, as the molecular factor coordinating plant nutrition status with flowering time remains largely unknown despite its well-known phenomenon.

Weaknesses: 

(1) Title: "A florigen-expressing subpopulation of companion cells". It is a bit misleading. The conclusion here is that only a subset of companion cells exhibit high expression of FT, but this does not imply that other companion cells do not express it at all. 

We agree with this comment, as it was not our intention to sound like that FT is not produced in other companion cells than the subpopulation we identified. We revised the title to more accurately reflect the point. The new title is “Companion cells with high florigen production express other small proteins and reveal a nitrogen-sensitive FT repressor.”

(2) Data quality: Authors opted for fluorescence-activated nuclei sorting (FANS) instead of traditional cell sorting method. What is the rationale behind this decision? Readers may wonder, especially given that RNA abundance in single nuclei is generally lower than that in single cells. This concern also applies to snRNA-seq data. Specifically, the number of genes captured was quite low, with a median of only 149 genes per nucleus. Additionally, the total number of nuclei analyzed was limited (1,173 for the pFT:NTF and 3,650 for the pSUC2:NTF). These factors suggest that the quality of the snRNA-seq data presented in this study is quite low. In this context, it becomes challenging for the reviewer to accurately assess whether this will impact the subsequent conclusions of the paper. Would it be possible to repeat this experiment and get more nuclei?

We appreciate this comment; we noticed that we did not clearly explain the rationale for using single-nucleus RNA sequencing (snRNA-seq) instead of single-cell RNA-seq (scRNA-seq). As reviewer 1 mentioned, RNA abundance in scRNA-seq is higher than in snRNA-seq. To conduct scRNA-seq using plant cells, protoplasting is the necessary step. However, in our study, protoplasting has many drawbacks in isolating our target cells from the phloem. First, it is technically challenging to efficiently isolate protoplasts from highly embedded phloem companion cells from plant tissues. Typically, at least several hours of enzymatic incubation are required to obtain protoplasts from companion cells (often using semi-isolated vasculatures), and the efficiency of protoplasting vasculature cells remains low. Secondly, for our analysis, restoring the time information within a day is also crucial. Therefore, we employed a more rapid isolation method. In the revision, we will explain our rationale for choosing snRNA-seq due to the technical limitations. In the revised manuscripts, we added four new sentences in the Introduction section to clearly explain these points.

Reviewer 1 also raised a concern about the quality of our snRNA-seq data, referring to the relatively low readcounts per nucleus. Although we believe that shallow reads do not necessarily indicate low quality and are confident in the accuracy of our snRNA-seq data, as supported by the detailed follow-up experiments (e.g., imaging analysis in Fig. 4B), we agree that it is important to address this point in the revision and alleviate readers’ concerns regarding the data quality. 

We believe the primary reason for the low readcounts per cell is the small amount of RNA present in each Arabidopsis vascular cell nucleus that we isolated. For bulk nuclei RNAseq, we collected 15,000 nuclei. However, the total RNA amount was approximately 3 ng. It indicates that each nucleus isolated contains a very limited amount of RNA (by the simple calculation, 3,000 pg / 15,000 nuclei = 0.2 pg/nucleus). It appears that the size of cells and nuclei was still small in 2-week-old seedlings; thus, each nucleus may contain lower levels of RNA. During the optimization process, we also tried to fix the tissues that we hoped to restore nuclear retained RNA, but unfortunately, in our hands, we encountered the technical issue of nuclei aggregation that hindered the sorting process, which is not suitable for single-nucleus RNA-seq.

Reviewer 1 suggested that we repeat the same snRNA-seq experiment. We agree that having more cells increases the reliability of data. However, to our knowledge, higher cell numbers enhance the confidence of clustering, but not readcounts per cell. In our snRNAseq data, our target, FT-expressing cells, were observed in cluster 7, which projected at an obvious distance from other cell clusters. Therefore, we think that having more nuclei does not significantly help in separating high FT-expressing cluster 7 cells and different types of cells, although we may obtain more DEGs from the cluster 7 cells. Considering the costs and time required for additional snRNA-seq experiments, we think that adding more followup molecular biology experiment data would be more practical. We clearly stated the limitations of our approach in the Discussion section. “A drawback of our snRNA-seq analysis was shallow reads per nucleus. It appears mainly due to the low abundance of mRNA in nuclei from 2-week-old leaves. Based on our calculation, the average mRNA level per nucleus is approximately 0.2 pg (3,000 pg mRNA from 15,000 sorted nuclei). Future technological advance is needed to improve the data quality“

In this revised version of the manuscript, we silenced FT gene expression using an amiRNA against FT driven by tissue-specific promoters [pROXY10, cluster 7; pSUC2, companion cells; pPIP2.6, cluster 4 (for the spatial expression pattern of PIP2.6, please see the new data shown in Fig. S8F); pGC1, guard cells]. Given that both FT and ROXY10 were highly expressed in cluster 7 of our snRNA-seq dataset, we anticipated the late flowering phenotype of pROXY10:amiRNA-ft. As we expected, pROXY10:amiR-ft but not pPIP2.6:amiR-ft lines showed delayed flowering phenotypes (Fig. S14A), supporting the validity of our snRNA-seq approach. We are also now more confident in the resolution of our snRNA-seq analysis, since cluster 4-specific PIP2.6 did not cause late flowering despite its higher basal expression than ROXY10 (Fig. S14B).

(3) Another disappointment is that the authors did not utilize reporter genes to identify the specific locations of the FT-high expressing cells (cluster 7 cells) within the CC population in vivo. Are there any discernible patterns that can be observed? 

In the original manuscript, as we showed only limited spatial images of overlap between FT and other cluster 7 genes in Fig. 4B, this comment is totally understandable. To respond to it, we added whole leaf images showing the spatial expression of FT and other cluster 7 genes (Fig. S12). These data indicate that cluster 7 genes including FT are expressed highly in minor veins in the distal part of the leaf but weakly in the main vein. We also added enlarged images of spatial expression of FT and cluster 7 genes (FLP1 and ROXY10) to note that those genes do not overlap completely (Fig. S13).

In contrast to cluster 7 genes, genes highly expressed in cluster 4, such as LTP1 and MLP28, are reportedly highly expressed in the main leaf vein. To further confirm it, we established a transgenic line that expresses a GFP-fusion protein controlled by the promoter of a cluster 4-specific gene PIP2.6 (Fig. S8F). It also showed strong GFP signals in the main vein, consistent with previous observations of LTP1 and MLP28.   In summary, FT-expressing cells (cluster 7 cells) are enriched in companion cells in the minor vein, and their expression patterns show a clear distinction from genes expressed in the main vein (e.g., cluster 4-specific genes). 

(4) The final disappointment is that the authors only compared FT expression between the nigtQ mutants and the wild type. Does this imply that the mutant does not have a flowering time defect particularly under high nitrogen conditions? 

We agree with reviewer 1 that more experiments are required to conclude the role of NIGT1 on FT regulation, in addition to our Y1H data, flowering time data of NIGT1 overexpressors, and FT expression in NIGT1 overexpressors and nigtQ mutant.

First, to test the direct regulation of NIGT1s on FT transcription, we conducted a transient luciferase (LUC) assay in tobacco leaves using effectors (p35S:NIGT1.2, p35S:NIGT1.4, and p35S:GFP) and reporters [pFT:LUC (FT promoter fused with LUC) and pFTm:LUC (the same FT promoter with mutations in NIGT1-binding sites fused with LUC)]. Our result showed that NIGT1.2 and NIGT1.4, but not GFP, decreased the activity of pFT:LUC but not pFTm:LUC (Fig. 5C). This indicates that NIGT1s directly repress the FT gene.

Second, to address reviewer 1’s suggestion about the effect of of nigtQ mutation on flowering time, we have grown WT and nigtQ plants on 20 mM and 2 mM NH₄NO₃. Under 20 mM NH₄NO₃, the nigtQ line bolted at earlier days than WT; under 2 mM NH₄NO₃, nigtQ and WT bolted at almost same timing (Fig. S17D and E). This result suggests that the nigtQ mutation affects flowering timing depending on nitrogen nutrient status. However, leaf numbers of bolted plants were not different between WT and nigtQ lines (Fig. S17E). Therefore, it appears that nigtQ mutation also accelerated overall growth of plants rather than flowering promotion. We also have measured flowering time by counting leaf numbers of the nigtQ and WT plants at bolting on nitrogen-rich soil. The mutant generated slightly more leaves than WT when they flowered (Fig. S17G). These results suggest that the NIGT-derived fine-tuning of FT regulation is conditional on higher nitrogen conditions. 

Minor: 

(1) Abstract: "Our bulk nuclei RNA-seq demonstrated that FT-expressing cells in cotyledons and in true leaves differed transcriptionally.". This sentence is not informative. What exactly is the difference in FT-expressing cells between cotyledons and true leaves? 

We modified the sentence to clarify the differences between cotyledons and true leaves. “Our bulk nuclei RNA-seq demonstrated that FT-expressing cells in cotyledons and true leaves showed differences especially in FT repressor genes.”

(2) As a standard practice, to support the direct regulation of FT by NIGT1, the authors should provide EMSA and ChIP-seq data. Ideally, they should also generate promoter constructs with deletions or mutations in the NIGT1 binding sites. 

To test direct interaction of NIGT1 to the FT promoter sequences, we performed the transient reporter assay using FT promoter driven luciferase reporter (Fig. 5C). NIGT1.2 and NIGT1.4 repressed the FT promoter activity; however, with NIGT1 binding site mutations, this repression was not observed, indicating that NIGT1 binds to the ciselements in the FT promoter to repress its transcription.

(3) Sorting: Did the authors fix the samples before preparing the nuclei suspension? If not, could this be the reason the authors observed the JA-responsive clusters (Fig. 2J)? Please provide more details related to nuclei sorting in the Methods section. 

We added a new subsection in the Materials and Methods section to explain a detail of the nuclei sorting procedure. We did not include a sample fixation step. We have tried formaldehyde fixation; however, it clumped nuclei, which was not suitable for snRNA-seq. Moreover, fixation steps generally reduce readcounts of single-cell RNA-seq according to the 10X Genomics’ guideline.

We agree that JA responses were triggered during the FANS nuclei isolation. Therefore, we added the following sentence. “Since our FANS protocol did not include a sample fixation step to avoid clumping, these cells likely triggered wounding responses during the chopping and sorting process (Fig. S1B).  

Reviewer #2 (Public review): 

This manuscript submitted by Takagi et al. details the molecular characterization of the FTexpressing cell at a single-cell level. The authors examined what genes are expressed specifically in FT-expressing cells and other phloem companion cells by exploiting bulk nuclei and single-nuclei RNA-seq and transgenic analysis. The authors found the unique expression profile of FT-expressing cells at a single-cell level and identified new transcriptional repressors of FT such as NIGT1.2 and NIGT1.4. 

Although previous researchers have known that FT is expressed in phloem companion cells, they have tended to neglect the molecular characterization of the FT-expressing phloem companion cells. To understand how FT, which is expressed in tiny amounts in phloem companion cells that make up a very small portion of the leaf, can be a key molecule in the regulation of the critical developmental step of floral transition, it is important to understand the molecular features of FT-expressing cells in detail. In this regard, this manuscript provides insight into the understanding of detailed molecular characteristics of the FT-expressing cell. This endeavor will contribute to the research field of flowering time. 

We are grateful that reviewer 2 recognizes the importance of transcriptome profiling of FTexpressing cells at the single-cell level.

Here are my comments on how to improve this manuscript. 

(1) The most noble finding of this manuscript is the identification of NTGI1.2 as the upstream regulator of FT-expressing cluster 7 gene expression. The flowering phenotypes of the nigtQ mutant and the transgenic plants in which NIGT1.2 was expressed under the SUC2 gene promoter support that NIGT1.2 functions as a floral repressor upstream of the FT gene. Nevertheless, the expression patterns of NIGT1.2 genes do not appear to have much overlap with those of NIGT1.2-downstream genes in the cluster 7 (Figs S14 and F3). An explanation for this should be provided in the discussion section. 

We agree with reviewer 2 that the spatial expression patterns of NIGT1.2 and cluster 7 genes do not overlap much, and some discussion should be provided in the manuscript. Although we do not have a concrete answer for this phenomenon, we obtained the new data showing that NIGT1.2 and NIGT1.4 directly repress the FT gene in planta (Fig. 5C).  As NIGT1.2/1.4 are negative regulators of FT, it is plausible that NIGT1.2/1.4 may suppress FT gene expression in non-cluster 7 cells to prevent the misexpression of FT. We added this point in the Results section.

(2) To investigate gene expression in the nuclei of specific cell populations, the authors generated transgenic plants expressing a fusion gene encoding a Nuclear Targeting Fusion protein (NTF) under the control of various cell type-specific promoters. Since the public audience would not know about NTF without reading reference 16, some explanation of NTF is necessary in the manuscript. Please provide a schematic of constructs the authors used to make the transformants.

As reviewer 2 pointed out, we lacked a clear explanation of why we used NTF in this study. NTF is the fusion protein that consists of a nuclear envelope targeting WPP domain, GFP, and a biotin acceptor peptide. It was initially designed for the INTACT (isolation of nuclei tagged in specific cell types) method, which enables us to isolate bulk nuclei from specific tissues. Although our original intention was to profile the bulk transcriptome of mRNAs that exist in nuclei of the FT-expressing cells using INTACT, we utilized our NTF transgenic lines for snRNA-seq analysis. To explain what NTF is to readers, we included a schematic diagram of NTF (Fig. S1A) and more explanation about NTF in the Results section.

Again, we appreciate all reviewers’ careful and constructive comments. With these changes, we hope our revised manuscript is now satisfactory.

Author response:

The following is the authors’ response to the previous reviews

Reviewer #1 (Public review): 

Summary: 

The study by Klug et al. investigated the pathway specificity of corticostriatal projections, focusing on two cortical regions. Using a G-deleted rabies system in D1-Cre and A2a-Cre mice to retrogradely deliver channelrhodopsin to cortical inputs, the authors found that M1 and MCC inputs to direct and indirect pathway spiny projection neurons (SPNs) are both partially segregated and asymmetrically overlapping. In general, corticostriatal inputs that target indirect pathway SPNs are likely to also target direct pathway SPNs, while inputs targeting direct pathway SPNs are less likely to also target indirect pathway SPNs. Such asymmetric overlap of corticostriatal inputs has important implications for how the cortex itself may determine striatal output. Indeed, the authors provide behavioral evidence that optogenetic activation of M1 or MCC cortical neurons that send axons to either direct or indirect pathway SPNs can have opposite effects on locomotion and different effects on action sequence execution. The conclusions of this study add to our understanding of how cortical activity may influence striatal output and offer important new clues about basal ganglia function. 

The conceptual conclusions of the manuscript are supported by the data, but the details of the magnitude of afferent overlap and causal role of asymmetric corticostriatal inputs on some behavioral outcomes may be a bit overstated given technical limitations of the experiments. 

For example, after virally labeling either direct pathway (D1) or indirect pathway (D2) SPNs to optogenetically tag pathway-specific cortical inputs, the authors report that a much larger number of "non-starter" D2-SPNs from D2-SPN labeled mice responded to optogenetic stimulation in slices than "non-starter" D1 SPNs from D1-SPN labeled mice did. Without knowing the relative number of D1 or D2 SPN starters used to label cortical inputs, it is difficult to interpret the exact meaning of the lower number of responsive D2-SPNs in D1 labeled mice (where only ~63% of D1-SPNs themselves respond) compared to the relatively higher number of responsive D1-SPNs (and D2-SPNs) in D2 labeled mice. While relative differences in connectivity certainly suggest that some amount of asymmetric overlap of inputs exists, differences in infection efficiency and ensuing differences in detection sensitivity in slice experiments make determining the degree of asymmetry problematic. 

It is also unclear if retrograde labeling of D1-SPN- vs D2-SPN- targeting afferents labels the same densities of cortical neurons. This gets to the point of specificity in some of the behavioral experiments. If the target-based labeling strategies used to introduce channelrhodopsin into specific SPN afferents label significantly different numbers of cortical neurons, might the difference in the relative numbers of optogenetically activated cortical neurons itself lead to behavioral differences? 

We thank the reviewer for the comments and for raising additional interpretations of our results. We agree that determining the relative number of D1- versus D2-SPN starter cells would allow a more accurate estimate of connectivity. However, due to current technical limitations, achieving this level of precision remains challenging. As the reviewer also noted, differences in the number of cortical neurons targeting D1- versus D2-SPNs could introduce additional complexity to the functional effects observed in the behavioral experiments. Moreover, functional heterogeneity is likely to exist not only among cortical neurons projecting to striatal D1- or D2-SPNs, but also within the striatal D1- and D2-SPN populations themselves. Addressing these questions at the single-neuron level will require more refined viral tools in combination with improved recording and manipulation techniques. Despite these limitations, our results suggest that a subpopulation of cortical neurons selectively targets striatal D1-SPNs, supporting a functional dichotomy of pathway-specific corticostriatal subcircuits in the control of behavior.   

Reviewer #2 (Public review): 

Summary: 

Klug et al. use monosynaptic rabies tracing of inputs to D1- vs D2-SPNs in the striatum to study how separate populations of cortical neurons project to D1- and D2-SPNs. They use rabies to express ChR2, then patch D1-or D2-SPNs to measure synaptic input. They report that cortical neurons labeled as D1-SPN-projecting preferentially project to D1-SPNs over D2-SPNs. In contrast, cortical neurons labeled as D2-SPN-projecting project equally to D1- and D2-SPNs. They go on to conduct pathway-specific behavioral stimulation experiments. They compare direct optogenetic stimulation of D1- or D2-SPNs to stimulation of MCC inputs to DMS and M1 inputs to DLS. In three different behavioral assays (open field, intra-cranial self-stimulation, and a fixed ratio 8 task), they show that stimulating MCC or M1 cortical inputs to D1-SPNs is similar to D1-SPN stimulation, but that stimulating MCC or M1 cortical inputs to D2-SPNs does not recapitulate the effects of D2-SPN stimulation (presumably because both D1- and D2-SPNs are being activated by these cortical inputs). 

Strengths: 

Showing these same effects in three distinct behaviors is strong. Overall, the functional verification of the consequences of the anatomy is very nice to see. It is a good choice to patch only from mCherry-negative non-starter cells in the striatum. This study adds to our understanding of the logic of corticostriatal connections, suggesting a previously unappreciated structure. 

Weaknesses: 

One limitation is that all inputs to SPNs are expressing ChR2, so they cannot distinguish between different cortical subregions during patching experiments. Their results could arise because the same innervation patterns are repeated in many cortical subregions or because some subregions have preferential D1-SPN input while others do not. 

Thank you for raising this thoughtful concern. It is indeed not feasible to restrict ChR2 expression to a specific cortical region using the first-generation rabies-ChR2 system alone. A more refined approach would involve injecting Cre-dependent TVA and RG into the striatum of D1- or A2A-Cre mice, followed by rabies-Flp infection. Subsequently, a Flp-dependent ChR2 virus could be injected into the MCC or M1 to selectively label D1- or D2-projecting cortical neurons. This strategy would allow for more precise targeting and address many of the current limitations.

However, a significant challenge lies in the cytotoxicity associated with rabies virus infection. Neuronal health begins to deteriorate substantially around 10 days post-infection, which provides an insufficient window for robust Flp-dependent ChR2 expression. We have tested several new rabies virus variants with extended survival times (Chatterjee et al., 2018; Jin et al., 2024), but unfortunately, they did not perform effectively or suitably in the corticostriatal systems we examined.

In our experimental design, the aim is to delineate the connectivity probabilities to D1 or D2-SPNs from cortical neurons. Our hypothesis considered includes the possibility that similar innervation patterns could occur across multiple cortical subregions, or that some subregions might show preferential input to D1-SPNs while others do not, or a combination of both scenarios. This leads us to perform a series behavior test that using optogenetic activation of the D1- or D2-projecting cortical populations to see which could be the case.

In the cortical areas we examined, MCC and M1, during behavioral testing, there is consistency with our electrophysiological results. Specifically, when we stimulated the D1-projecting cortical neurons either in MCC or in M1, mice exhibited facilitated local motion in open field test, which is the same to the activation of D1 SPNs in the striatum along (MCC: Fig 3C & D vs. I; M1: Fig 3F & G vs. L). Conversely, stimulation of D2-projecting MCC or M1 cortical neurons resulted in behavioral effects that appeared to combine characteristics of both D1- and D2-SPNs activation in the striatum (MCC: Fig 3C & D vs. J; M1: Fig 3F & G vs. M). The similar results were observed in the ICSS test. Our interpretation of these results is that the activation of D1-projecting neurons in the cortex induces behavior changes akin to D1 neuron activation, while activation of D2-projecting neurons in the cortex leads to a combined effect of both D1 and D2 neuron activation. This suggests that at least some cortical regions, the ones we tested, follow the hypothesis we proposed.

There are also some caveats with respect to the efficacy of rabies tracing. Although they only patch non-starter cells in the striatum, only 63% of D1-SPNs receive input from D1-SPN-projecting cortical neurons. It's hard to say whether this is "high" or "low," but one question is how far from the starter cell region they are patching. Without this spatial indication of where the cells that are being patched are relative to the starter population, it is difficult to interpret if the cells being patched are receiving cortical inputs from the same neurons that are projecting to the starter population. The authors indicate they are patching from mCherry-negative neurons within the region of the mCherry-positive neurons, but since the mCherry population will include both true starter cells and monosynaptically connected cells, this is not perfectly precise. Convergence of cortical inputs onto SPNs may vary with distance from the starter cell region quite dramatically, as other mapping studies of corticostriatal inputs have shown specialized local input regions can be defined based on cortical input patterns (Hintiryan et al., Nat Neurosci, 2016, Hunnicutt et al., eLife 2016, Peters et al., Nature, 2021). 

This is a valid concern regarding anatomical studies. Investigating cortico-striatal connectivity at the single-cell level remains technically challenging due to current methodological limitations. At present, we rely on rabies virus-mediated trans-synaptic retrograde tracing to identify D1- or D2-projecting cortical populations. This anatomical approach is coupled with ex vivo slice electrophysiology to assess the functional connectivity between these projection-defined cortical neurons and striatal SPNs. This enables us to quantify connection ratios, for example, the proportion of D1-projecting cortical neurons that functionally synapse onto non-starter D1-SPNs.

To ensure the robustness of our conclusions, it is essential that both the starter cells and the recorded non-starter SPNs receive comparable topographical input from the cortex and other brain regions. Therefore, we carefully designed our experiments so that all recorded cells were located within the injection site, were mCherry-negative (i.e., non-starter cells), and were surrounded by ChR2-mCherry-positive neurons. This configuration ensured that the distance between recorded and starter cells did not exceed 100 µm, maintaining close anatomical proximity and thereby preserving the likelihood of shared cortical innervation within the examined circuitry.

These methodological details are also described in the section on ex vivo brain slice electrophysiology, specifically in the Methods section, lines 453–459:

“D1-SPNs (eGFP-positive in D1-eGFP mice, or eGFP-negative in D2-eGFP mice) or D2-SPNs (eGFP-positive in D2-eGFP mice, or eGFP-negative in D1-eGFP mice) that were ChR2-mCherry-negative, but in the injection site and surrounded by cells expressing ChR2-mCherry were targeted for recording. This configuration ensured that the distance between recorded and starter cells did not exceed 100 µm, maintaining close anatomical proximity and thereby preserving the likelihood of shared cortical innervation within the examined circuitry.”

This experimental strategy was implemented to control for potential spatial biases and to enhance the interpretability of our connectivity measurements.

A caveat for the optogenetic behavioral experiments is that these optogenetic experiments did not include fluorophore-only controls, although a different control (with light delivered in M1) is provided in Supplementary Figure 3. Another point of confusion is that other studies (Cui et al, J Neurosci, 2021) have reported that stimulation of D1-SPNs in DLS inhibits rather than promotes movement. This study may have given different results due to subtly different experimental parameters, including fiber optic placement and NA.

We appreciate the reviewer’s thoughtful evaluation and comments. We have added a short discussion of Cui et al.’s study on optogenetic stimulation of D1-SPNs in the DLS (lines 341-343), which reports findings that contrast with ours and those of other studies.

Reviewer #3 (Public review): 

Review of resubmission: The authors provided a response to the reviews from myself and other reviewers. While some points were made satisfactorily, particularly in clarification of the innervation of cortex to striatum and the effects of input stimulation, many of my points remain unaddressed. In several cases, the authors chose to explain their rationale rather than address the issues at hand. A number of these issues (in fact, the majority) could be addressed simply by toning done the confidence in conclusions, so it was disappointing to see that the authors by and large did not do this. I repeat my concerns below and note whether I find them to have been satisfactorily addressed or not. 

In the manuscript by Klug and colleagues, the investigators use a rabies virus-based methodology to explore potential differences in connectivity from cortical inputs to the dorsal striatum. They report that the connectivity from cortical inputs onto D1 and D2 MSNs differs in terms of their projections onto the opposing cell type, and use these data to infer that there are differences in cross-talk between cortical cells that project to D1 vs. D2 MSNs. Overall, this manuscript adds to the overall body of work indicating that there are differential functions of different striatal pathways which likely arise at least in part by differences in connectivity that have been difficult to resolve due to difficulty in isolating pathways within striatal connectivity, and several interesting and provocative observations were reported. Several different methodologies are used, with partially convergent results, to support their main points. 

However, I have significant technical concerns about the manuscript as presented that make it difficult for me to interpret the results of the experiments. My comments are below. 

Major: 

There is generally a large caveat to the rabies studies performed here, which is that both TVA and the ChR2-expressing rabies virus have the same fluorophore. It is thus essentially impossible to determine how many starter cells there are, what the efficiency of tracing is, and which part of the striatum is being sampled in any given experiment. This is a major caveat given the spatial topography of the cortico-striatal projections. Furthermore, the authors make a point in the introduction about previous studies not having explored absolute numbers of inputs, yet this is not at all controlled in this study. It could be that their rabies virus simply replicates better in D1-MSNs than D2-MSNs. No quantifications are done, and these possibilities do not appear to have been considered. Without a greater standardization of the rabies experiments across conditions, it is difficult to interpret the results. 

This is still an issue. The authors point out why they chose various vectors. I can understand why the authors chose the fluorophores etc. that they did, yet the issues I raised previously are still valid. The discussion should mention that this is a potential issue. It does not necessarily invalidate results, but it is an issue. Furthermore, it is possible (in all systems) that rabies replicates better/more efficiently in some cells than others. This is one possible interpretation that has not really been explored in any study. I don't suggest the authors attempt to do that, but it should be raised as a potential interpretation. If the rabies results could mean several different things, the authors owe it to the readership to state all possible interpretations of data.

We thank the reviewer for the comments and suggestions. Because the same fluorophore (mCherry) was used in both TVA- and ChR2-expressing viruses, it was not possible to distinguish true starter SPNs from TVA-only SPNs or monosynaptically labeled SPNs. This limitation makes it difficult to precisely assess the efficiency of rabies labeling and retrograde tracing in our experimental setup. Moreover, differences in rabies replication efficiency between D1- and D2-SPNs could potentially lead to an apparent lower connection probability from D1-projecting cortical neurons to D2-SPNs than from D2-projecting cortical neurons to D1-SPNs. We have added this clarification to the Discussion (lines 280-297).

The authors claim using a few current clamp optical stimulation experiments that the cortical cells are healthy, but this result was far from comprehensive. For example, membrane resistance, capacitance, general excitability curves, etc are not reported. In Figure S2, some of the conditions look quite different (e.g., S2B, input D2-record D2, the method used yields quite different results that the authors write off as not different). Furthermore, these experiments do not consider the likely sickness and death that occurs in starter cells, as has been reported elsewhere. Health of cells in the circuit is overall a substantial concern that alone could invalidate a large portion, if not all, of the behavioral results. This is a major confound given those neurons are thought to play critical roles in the behaviors being studied. This is a major reason why first-generation rabies viruses have not been used in combination with behavior, but this significant caveat does not appear to have been considered, and controls e.g., uninfected animals, infected with AAV helpers, etc, were not included. 

This issue remains unaddressed. I did not request clarity about experimental design, but rather, raised issues about the potential effects of toxicity. I believe this to be a valid concern that needs to be discussed in the manuscript, especially given what look visually like potential differences in S2. 

We understand and appreciate the reviewer’s concern regarding the potential cytotoxicity of rabies virus infection. Although we performed the in vivo optogenetic behavioral experiments during a period when rabies-infected cells are generally considered relatively healthy, some deficits in starter cells may still occur and could contribute to the observed effects of optogenetic cortical stimulation. We have added this clarification to the Discussion (lines 298-306).

The overall purity (e.g., EnvA pseudotyping efficiency) of the RABV prep is not shown. If there was a virus that was not well EnvA-pseudotyped and thus could directly infect cortical (or other) inputs, it would degrade specificity. This issue has not been addressed. Viral strain is irrelevant. The quality of the specific preparations used is what matters.

While most of the study focuses on the cortical inputs, in slice recordings, inputs from the thalamus are not considered, yet likely contribute to the observed results. Related to this, in in vivo optogenetic experiments, technically, if the thalamic or other inputs to the dorsal striatum project to the cortex, their method will not only target cortical neurons but also terminals of other excitatory inputs. If this cannot be ruled it, stating that the authors are able to selectively activate the cortical inputs to one or the other population should be toned down. 

The authors added text to the discussion to address this point. While it largely does what is intended, based on the one study cited, I disagree with the authors' conclusions that it is "clear" that potential contamination from other sites does not play a role. The simplest interpretation is the one the authors state, and there is some supporting evidence to back up that assertion, but to me that falls short of making the point "clear" that there are no other interpretations. 

The statements about specificity of connectivity are not well founded. It may be that in the specific case where they are assessing outside of the area of injections, their conclusions may hold (e.g., excitatory inputs onto D2s have more inputs onto D1s than vice versa). However, how this relates to the actual site of injection is not clear. At face value, if such a connectivity exists, it would suggest that D1-MSNs receive substantially more overall excitatory inputs than D2s. It is thus possible that this observation would not hold over other spatial intervals. This was not explored and thus the conclusions are over-generalized. e.g., the distance from the area of red cells in the striatum to recordings was not quantified, what constituted a high level of cortical labeling was not quantified, etc. Without more rigorous quantification of what was being done, it is difficult to interpret the results. 

Again, the goal here would be to make a statement about this in the discussion to clarify limitations of the study. I don't expect the authors to re-do all of these experiments, but since they are discussing the corticostriatal circuits, which have multiple subdomains, this remains a relevant point. It has not been addressed. 

The results in Figure 3 are not well controlled. The authors show contrasting effects of optogenetic stimulation of D1-MSNs and D2-MSNs in the DMS and DLS, results which are largely consistent with the canon of basal ganglia function. However, when stimulating cortical inputs, stimulating the inputs from D1-MSNs gives the expected results (increased locomotion) while stimulating putative inputs to D2-MSNs had no effect. This is not the same as showing a decrease in locomotion - showing no effect here is not possible to interpret. 

I think that the caveat of showing no clear effects of inputs to D2 stimulation should be pointed out. Yes, I understand that the viruses appeared to express etc., but again it remains possible that the results are driven by a lack of e.g., sufficient ChR2 expression. Aside from a full quantification of the number of cells expressing ChR2, overlap in fiber placement and ChR2 expression (which I don't suggest), this remains a possibility and should be pointed out, as it remains a possibility. 

In the light of their circuit model, the result showing that inputs to D2-MSNs drive ICSS is confusing. How can the authors account for the fact that these cells are not locomotor-activating, stimulation of their putative downstream cells (D2-MSNs) does not drive ICSS, yet the cortical inputs drive ICSS? Is the idea that these inputs somehow also drive D1s? If this is the case, how do D2s get activated, if all of the cortical inputs tested net activate D1s and not D2s? Same with the results in Figure 4 - the inputs and putative downstream cells do not have the same effects. Given potential caveats of differences in viral efficiency, spatial location of injections, and cellular toxicity, I cannot interpret these experiments. 

The explanation the authors provide in their rebuttal makes sense, however this should be included in the discussion of the manuscript, as it is interesting and relevant. 

We thank the reviewer for the valuable comments and suggestions. In line with the reviewer’s recommendation, we have incorporated these explanations into the Discussion (lines 242–279) to help interpret the complex behavioral outcomes of optogenetic stimulation of cortical neurons projecting to D1- or D2-SPNs.

Reviewer #2 (Recommendations for the authors): 

I appreciate the authors' responses, which helped clarify some experimental choices. I appreciate that the experiment in Fig S3 serves as a reasonable light control for optogenetics experiments. The careful comparison with methods in Cui et al (2021) is useful, although not added to the main manuscript. Some of the other citations here don't really address the controversy, e.g. Kravitz at al is in DMS, but perhaps fully addressing this issue is outside the scope of the current manuscript and awaits further experiments. I also appreciate the clarification for recording locations that "This configuration ensured that the distance between recorded and starter cells did not exceed 100 µm, maintaining close anatomical proximity and thereby preserving the likelihood of shared cortical innervation within the examined circuitry." However, the statement in the reviewer response does not seem to be added to the manuscript's methods, which I think would be helpful. The criteria for choosing recorded cells are still a bit fuzzy without a map of recording locations and histology. There is also a problem that mCherry-positive cells could be starter cells or could be monosynaptically traced cells, so it is hard to know the area of the starter cell population in these experiments for sure. My evaluation of the manuscript remains largely the same as the original. However, I have adjusted my public review a bit to incorporate the authors' responses. I still think this paper has valuable information, suggesting an interesting and previously unappreciated structure of corticostriatal inputs that I hope this group and others will continue to investigate and incorporate into models of basal ganglia function.

We thank the reviewer for the valuable suggestions. We have now included a comparison with Cui et al. in the Discussion. In addition, we have added the criteria for selecting recorded cells to the Methods section: ‘This configuration ensured that the distance between recorded and starter cells did not exceed 100 µm, maintaining close anatomical proximity and thereby preserving the likelihood of shared cortical innervation within the examined circuitry.’

Author Response:

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

Reviewer #1 (Public Review):

Summary: 

This paper applies methods for segmentation, annotation, and visualization of acoustic analysis to zebra finch song. The paper shows that these methods can be used to predict the stage of song development and to quantify acoustic similarity. The methods are solid and are likely to provide a useful tool for scientists aiming to label large datasets of zebra finch vocalizations. The paper has two main parts: 1) establishing a pipeline/ package for analyzing zebra finch birdsong and 2) a method for measuring song imitation. 

Strengths: 

It is useful to see existing methods for syllable segmentation compared to new datasets.

It is useful, but not surprising, that these methods can be used to predict developmental stage, which is strongly associated with syllable temporal structure.

It is useful to confirm that these methods can identify abnormalities in deafened and isolated songs. 

Weaknesses: 

For the first part, the implementation seems to be a wrapper on existing techniques. For instance, the first section talks about syllable segmentation; they made a comparison between whisperseg (Gu et al, 2024), tweetynet (Cohen et al, 2022), and amplitude thresholding. They found that whisperseg performed the best, and they included it in the pipeline. They then used whisperseg to analyze syllable duration distributions and rhythm of birds of different ages and confirmed past findings on this developmental process (e.g. Aronov et al, 2011). Next, based on the segmentation, they assign labels by performing UMAP and HDBScan on the spectrogram (nothing new; that's what people have been doing). Then, based on the labels, they claimed they developed a 'new' visualization - syntax raster ( line 180 ). That was done by Sainburg et. al. 2020 in Figure 12E and also in Cohen et al, 2020 - so the claim to have developed 'a new song syntax visualization' is confusing. The rest of the paper is about analyzing the finch data based on AVN features (which are essentially acoustic features already in the classic literature). 

First, we would like to thank this reviewer for their kind comments and feedback on this manuscript. It is true that many of the components of this song analysis pipeline are not entirely novel in isolation. Our real contribution here is bringing them together in a way that allows other researchers to seamlessly apply automated syllable segmentation, clustering, and downstream analyses to their data. That said, our approach to training TweetyNet for syllable segmentation is novel. We trained TweetyNet to recognize vocalizations vs. silence across multiple birds, such that it can generalize to new individual birds, whereas Tweetynet had only ever been used to annotate song syllables from birds included in its training set previously. Our validation of TweetyNet and WhisperSeg in combination with UMAP and HDBSCAN clustering is also novel, providing valuable information about how these systems interact, and how reliable the completely automatically generated labels are for downstream analysis. We have added a couple sentences to the introduction to emphasize the novelty of this approach and validation.

Our syntax raster visualization does resemble Figure 12E in Sainburg et al. 2020, however it differs in a few important ways, which we believe warrant its consideration as a novel visualization method. First, Sainburg et al. represent the labels across bouts in real time; their position along the x axis reflects the time at which each syllable is produced relative to the start of the bout. By contrast, our visualization considers only the index of syllables within a bout (ie. First syllable vs. second syllable etc) without consideration of the true durations of each syllable or the silent gaps between them. This makes it much easier to detect syntax patterns across bouts, as the added variability of syllable timing is removed. Considering only the sequence of syllables rather than their timing also allows us to more easily align bouts according to the first syllable of a motif, further emphasizing the presence or absence of repeating syllable sequences without interference from the more variable introductory notes at the start of a motif. Finally, instead of plotting all bouts in the order in which they were produced, our visualization orders bouts such that bouts with the same sequence of syllables will be plotted together, which again serves to emphasize the most common syllable sequences that the bird produces. These additional processing steps mean that our syntax raster plot has much starker contrast between birds with stereotyped syntax and birds with more variable syntax, as compared to the more minimally processed visualization in Sainburg et al. 2020. There doesn’t appear to be any similar visualizations in Cohen et al. 2020. 

The second part may be something new, but there are opportunities to improve the benchmarking. It is about the pupil-tutor imitation analysis. They introduce a convolutional neural network that takes triplets as an input (each tripled is essentially 3 images stacked together such that you have (anchor, positive, negative), Anchor is a reference spectrogram from, say finch A; positive means a different spectrogram with the same label as anchor from finch A, and negative means a spectrogram not related to A or different syllable label from A. The network is then trained to produce a low-dimensional embedding by ensuring the embedding distance between anchor and positive is less than anchor and negative by a certain margin. Based on the embedding, they then made use of earth mover distance to quantify the similarity in the syllable distribution among finches. They then compared their approach performance with that of sound analysis pro (SAP) and a variant of SAP. A more natural comparison, which they didn't include, is with the VAE approach by Goffinet et al. In this paper (https://doi.org/10.7554/eLife.67855, Fig 7), they also attempted to perform an analysis on the tutor pupil song.  

We thank the reviewer for this suggestion. We have included a comparison of our triplet loss embedding model to the VAE model proposed in Goffinet et al. 2021. We also included comparisons of similarity scoring using each of these embedding models combined with either earth mover’s distance (EMD) or maximum mean discrepancy (MMD) to calculate the similarity of the embeddings, as was done in Goffinet et al. 2021. As discussed in the updated results section of the paper and shown in the new Figure 6–figure supplement 1, the Triplet loss model with MMD performs best for evaluating song learning on new birds, not included in model training. We’ve updated the main text of the paper to reflect this switch from EMD to MMD for the primary similarity scoring approach.

Reviewer #2 (Public Review):

Summary: 

In this work, the authors present a new Python software package, Avian Vocalization Network (AVN) aimed at facilitating the analysis of birdsong, especially the song of the zebra finch, the most common songbird model in neuroscience. The package handles some of the most common (and some more advanced) song analyses, including segmentation, syllable classification, featurization of song, calculation of tutor-pupil similarity, and age prediction, with a view toward making the entire process friendlier to experimentalists working in the field.

For many years, Sound Analysis Pro has served as a standard in the songbird field, the first package to extensively automate songbird analysis and facilitate the computation of acoustic features that have helped define the field. More recently, the increasing popularity of Python as a language, along with the emergence of new machine learning methods, has resulted in a number of new software tools, including the vocalpy ecosystem for audio processing, TweetyNet (for segmentation), t-SNE and UMAP (for visualization), and autoencoder-based approaches for embedding.

Strengths: 

The AVN package overlaps several of these earlier efforts, albeit with a focus on more traditional featurization that many experimentalists may find more interpretable than deep learning-based approaches. Among the strengths of the paper are its clarity in explaining the several analyses it facilitates, along with high-quality experiments across multiple public datasets collected from different research groups. As a software package, it is open source, installable via the pip Python package manager, and features high-quality documentation, as well as tutorials. For experimentalists who wish to replicate any of the analyses from the paper, the package is likely to be a useful time saver.

Weaknesses: 

I think the potential limitations of the work are predominantly on the software end, with one or two quibbles about the methods.

First, the software: it's important to note that the package is trying to do many things, of which it is likely to do several well and few comprehensively. Rather than a package that presents a number of new analyses or a new analysis framework, it is more a codification of recipes, some of which are reimplementations of existing work (SAP features), some of which are essentially wrappers around other work (interfacing with WhisperSeg segmentations), and some of which are new (similarity scoring). All of this has value, but in my estimation, it has less value as part of a standalone package and potentially much more as part of an ecosystem like vocalpy that is undergoing continuous development and has long-term support. 

We appreciate this reviewer’s comments and concerns about the structure of the AVN package and its long-term maintenance. We have considered incorporating AVN into the VocalPy ecosystem but have chosen not to for a few key reasons. (1) AVN was designed with ease of use for experimenters with limited coding experience top of mind. VocalPy provides excellent resources for researchers with some familiarity with object-oriented programming to manage and analyze their datasets; however, we believe it may be challenging for users without such experience to adopt VocalPy quickly. AVN’s ‘recipe’ approach, as you put it, is very easily accessible to new users, and allows users with intermediate coding experience to easily navigate the source code to gain a deeper understanding of the methodology. AVN also consistently outputs processed data in familiar formats (tables in .csv files which can be opened in excel), in an effort to make it more accessible to new users, something which would be challenging to reconcile with VocalPy’s emphasis on their `dataset`classes. (2) AVN and VocalPy differ in their underlying goals and philosophies when it comes to flexibility vs. standardization of analysis pipelines. VocalPy is designed to facilitate mixing-and-matching of different spectrogram generation, segmentation, annotation etc. approaches, so that researchers can design and implement their own custom analysis pipelines. This flexibility is useful in many cases. For instance, it could allow researchers who have very different noise filtering and annotation needs, like those working with field recordings versus acoustic chamber recordings, to analyze their data using this platform. However, when it comes to comparisons across zebra finch research labs, this flexibility comes at the expense of direct comparison and integration of song features across research groups. This is the context in which AVN is most useful. It presents a single approach to song segmentation, labeling, and featurization that has been shown to generalize well across research groups, and which allows direct comparisons of the resulting features. AVN’s single, extensively validated, standard pipeline approach is fundamentally incompatible with VocalPy’s emphasis on flexibility. We are excited to see how VocalPy continues to evolve in the future, and recognize the value that both AVN and VocalPy bring to the songbird research community, each with their own distinct strengths, weaknesses, and ideal use cases. 

While the code is well-documented, including web-based documentation for both the core package and the GUI, the latter is available only on Windows, which might limit the scope of adoption. 

We thank the reviewer for their kind words about AVN’s documentation. We recognize that the GUI’s exclusive availability on Windows is a limitation, and we would be happy to collaborate with other researchers and developers in the future to build a Mac compatible version, should the demand present itself. That said, the python package works on all operating systems, so non-Windows users still have the ability to use AVN that way.

That is to say, whether AVN is adopted by the field in the medium term will have much more to do with the quality of its maintenance and responsiveness to users than any particular feature, but I believe that many of the analysis recipes that the authors have carefully worked out may find their way into other code and workflows. 

Second, two notes about new analysis approaches:

(1) The authors propose a new means of measuring tutor-pupil similarity based on first learning a latent space of syllables via a self-supervised learning (SSL) scheme and then using the earth mover's distance (EMD) to calculate transport costs between the distributions of tutors' and pupils' syllables. While to my knowledge this exact method has not previously been proposed in birdsong, I suspect it is unlikely to differ substantially from the approach of autoencoding followed by MMD used in the Goffinet et al. paper. That is, SSL, like the autoencoder, is a latent space learning approach, and EMD, like MMD, is an integral probability metric that measures discrepancies between two distributions. (Indeed, the two are very closely related: https://stats.stackexchange.com/questions/400180/earth-movers-distance-andmaximum-mean-discrepency.) Without further experiments, it is hard to tell whether these two approaches differ meaningfully. Likewise, while the authors have trained on a large corpus of syllables to define their latent space in a way that generalizes to new birds, it is unclear why such an approach would not work with other latent space learning methods.  

We recognize the similarities between these approaches and have included comparisons of the VAE and MMD as in the Goffinet paper to our triplet loss model and EMD.  As discussed in the updated results section of the paper and shown in the new Figure 6–figure supplement 1, the Triplet loss model with MMD performs best for evaluating song learning on new birds, not included in model training. We’ve updated the main text of the paper to reflect this switch from EMD to MMD for the primary similarity scoring approach. 

(2) The authors propose a new method for maturity scoring by training a model (a generalized additive model) to predict the age of the bird based on a selected subset of acoustic features. This is distinct from the "predicted age" approach of Brudner, Pearson, and Mooney, which predicts based on a latent representation rather than specific features, and the GAM nicely segregates the contribution of each. As such, this approach may be preferred by many users who appreciate its interpretability.  

In summary, my view is that this is a nice paper detailing a well-executed piece of software whose future impact will be determined by the degree of support and maintenance it receives from others over the near and medium term.

Reviewer #3 (Public Review):

Summary: 

The authors invent song and syllable discrimination tasks they use to train deep networks. These networks they then use as a basis for routine song analysis and song evaluation tasks. For the analysis, they consider both data from their own colony and from another colony the network has not seen during training. They validate the analysis scores of the network against expert human annotators, achieving a correlation of 80-90%. 

Strengths: 

(1) Robust Validation and Generalizability: The authors demonstrate a good performance of the AVN across various datasets, including individuals exhibiting deviant behavior. This extensive validation underscores the system's usefulness and broad applicability to zebra finch song analysis, establishing it as a potentially valuable tool for researchers in the field.

(2) Comprehensive and Standardized Feature Analysis: AVN integrates a comprehensive set of interpretable features commonly used in the study of bird songs. By standardizing the feature extraction method, the AVN facilitates comparative research, allowing for consistent interpretation and comparison of vocal behavior across studies.

(3) Automation and Ease of Use. By being fully automated, the method is straightforward to apply and should introduce barely an adoption threshold to other labs.

(4) Human experts were recruited to perform extensive annotations (of vocal segments and of song similarity scores). These annotations released as public datasets are potentially very valuable. 

Weaknesses: 

(1) Poorly motivated tasks. The approach is poorly motivated and many assumptions come across as arbitrary. For example, the authors implicitly assume that the task of birdsong comparison is best achieved by a system that optimally discriminates between typical, deaf, and isolated songs. Similarly, the authors assume that song development is best tracked using a system that optimally estimates the age of a bird given its song. My issue is that these are fake tasks since clearly, researchers will know whether a bird is an isolated or a deaf bird, and they will also know the age of a bird, so no machine learning is needed to solve these tasks. Yet, the authors imagine that solving these placeholder tasks will somehow help with measuring important aspects of vocal behavior.  

We appreciate this reviewer’s concerns and apologize for not providing sufficiently clear rationale for the inclusion of our phenotype classifier and age regression models in the original manuscript. These tasks are not intended to be taken as a final, ultimate culmination of the AVN pipeline. Rather, we consider the carefully engineered 55-interpretable feature set to be AVN’s final output, and these analyses serve merely as examples of how that feature set can be applied. That said, each of these models do have valid experimental use cases that we believe are important and would like to bring to the attention of the reviewer.

For one, we showed how the LDA model that can discriminate between typical, deaf, and isolate birds’ songs not only allows us to evaluate which features are most important for discriminating between these groups, but also allows comparison of the FoxP1 knock-down (FP1 KD) birds to each of these phenotypes. Based on previous work (Garcia-Oscos et al. 2021), we hypothesized that FP1 KD in these birds specifically impaired tutor song memory formation while sparing a bird’s ability to refine their own vocalizations through auditory feedback. Thus, we would expect their songs to resemble those of isolate birds, who lack a tutor song memory, but not to resemble deaf birds who lack a tutor song memory and auditory feedback of their own vocalizations to guide learning. The LDA model allowed us to make this comparison quantitatively for the first time and confirm our hypothesis that FP1 KD birds’ songs are indeed most like isolates’. In the future, as more research groups publish their birds’ AVN feature sets, we hope to be able to make even more fine-grained comparisons between different groups of birds, either using LDA or other similar interpretable classifiers. 

The age prediction model also has valid real-world use cases. For instance, one might imagine an experimental manipulation that is hypothesized to accelerate or slow song maturation in juvenile birds. This age prediction model could be applied to the AVN feature sets of birds having undergone such a manipulation to determine whether their predicted ages systematically lead or lag their true biological ages, and which song features are most responsible for this difference. We didn’t have access to data for any such birds for inclusion in this paper, but we hope that others in the future will be able to take inspiration from our methodology and use this or a similar age regression model with AVN features in their research. We have added a couple lines to the ‘Comparing Song Disruptions with AVN Features’ and ‘Tracking Song Development with AVN Features’ sections of the results to make this more clear. 

Along similar lines, authors assume that a good measure of similarity is one that optimally performs repeated syllable detection (i.e. to discriminate same syllable pairs from different pairs). The authors need to explain why they think these placeholder tasks are good and why no better task can be defined that more closely captures what researchers want to measure. Note: the standard tasks for self-supervised learning are next word or masked word prediction, why are these not used here? 

This reviewer appears to have misunderstood our similarity scoring embedding model and our rationale for using it. We will explain it in more depth here and have added a paragraph to the ‘Measuring Song Imitation’ section of the results explaining this rationale more briefly.

First, nowhere are we training a model to discriminate between same and different syllable pairs. The triplet loss network is trained to embed syllables in an 8-dimensional space such that syllables with the same label are closer together than syllables with different labels. The loss function is related to the relative distance between embeddings of syllables with the same or different labels, not the classification of syllables as same or different. This approach was chosen because it has repeatedly been shown to be a useful data compression step (Schorff et al. 2015, Thakur et al. 2019) before further downstream tasks are applied on its output, particularly in contexts where there is little data per class (syllable label). For example, Schorff et al. 2015 trained a deep convolutional neural network with triplet loss to embed images of human faces from the same individual closer together than images of different individuals in a 128dimensional space. They then used this model to compute 128-dimensional representations of additional face images, not included in training, which were used for individual facial recognition (this is a same vs. different category classifier), and facial clustering, achieving better performance than the previous state of the art. The triplet loss function results in a model that can generate useful embeddings of previously unseen categories, like new individuals’ faces, or new zebra finches’ syllables, which can then be used in downstream analyses. This meaningful, lower dimensional space allows comparisons of distributions of syllables across birds, as in Brainard and Mets 2008, and Goffinet et al. 2021. 

Next word and masked word prediction are indeed common self-supervised learning tasks for models working with text data, or other data with meaningful sequential organization. That is not the case for our zebra finch syllables, where every bird’s syllable sequence depends only on its tutor’s sequence, and there is no evidence for strong universal syllable sequencing rules (James et al. 2020). Rather, our embedding model is an example of a computer vision task, as it deals with sets of two-dimensional images (spectrograms), not sequences of categorical variables (like text). It is also not, strictly speaking, a selfsupervised learning task, as it does require syllable labels to generate the triplets. A common selfsupervised approach for dimensionality reduction in a computer vision task such as this one would be to train an autoencoder to compress images to a lower dimensional space, then faithfully reconstruct them from the compressed representation.  This has been done using a variational autoencoder trained on zebra finch syllables in Goffinet et al. 2021. In keeping with the suggestions from reviewers #1 and #2, we have included a comparison of our triplet loss model with the Goffinet et al. VAE approach in the revised manuscript. 

(2) The machine learning methodology lacks rigor. The aims of the machine learning pipeline are extremely vague and keep changing like a moving target. Mainly, the deep networks are trained on some tasks but then authors evaluate their performance on different, disconnected tasks. For example, they train both the birdsong comparison method (L263+) and the song similarity method (L318+) on classification tasks. However, they evaluate the former method (LDA) on classification accuracy, but the latter (8-dim embeddings) using a contrast index. In machine learning, usually, a useful task is first defined, then the system is trained on it and then tested on a held-out dataset. If the sensitivity index is important, why does it not serve as a cost function for training?

Again, this reviewer seems not to understand our similarity scoring methodology. Our similarity scoring model is not trained on a classification task, but rather on an embedding task. It learns to embed spectrograms of syllables in an 8-dimensional space such that syllables with the same label are closer together than syllables with different labels. We could report the loss values for this embedding task on our training and validation datasets, but these wouldn’t have any clear relevance to the downstream task of syllable distribution comparison where we are using the model’s embeddings. We report the contrast index as this has direct relevance to the actual application of the model and allows comparisons to other similarity scoring methods, something that the triplet loss values wouldn’t allow. 

The triplet loss method was chosen because it has been shown to yield useful low-dimensional representations of data, even in cases where there is limited labeled training data (Thakur et al. 2019). While we have one of the largest manually annotated datasets of zebra finch songs, it is still quite small by industry deep learning standards, which is why we chose a method that would perform well given the size of our dataset. Training a model on a contrast index directly would be extremely computationally intensive and require many more pairs of birds with known relationships than we currently have access to. It could be an interesting approach to take in the future, but one that would be unlikely to perform well with a dataset size typical to songbird research. 

Also, usually, in solid machine learning work, diverse methods are compared against each other to identify their relative strengths. The paper contains almost none of this, e.g. authors examined only one clustering method (HDBSCAN).  

We did compare multiple methods for syllable segmentation (WhisperSeg, TweetyNet, and Amplitude thresholding) as this hadn’t been done previously. We chose not to perform extensive comparison of different clustering methods as Sainburg et al. 2020 already did so and we felt no need to reduplicate this effort. We encourage this reviewer to refer to Sainburg et al.’s excellent work for comparisons of multiple clustering methods applied to zebra finch song syllables.

(3) Performance issues. The authors want to 'simplify large-scale behavioral analysis' but it seems they want to do that at a high cost. (Gu et al 2023) achieved syllable scores above 0.99 for adults, which is much larger than the average score of 0.88 achieved here (L121). Similarly, the syllable scores in (Cohen et al 2022) are above 94% (their error rates are below 6%, albeit in Bengalese finches, not zebra finches), which is also better than here. Why is the performance of AVN so low? The low scores of AVN argue in favor of some human labeling and training on each bird.  

Firstly, the syllable error rate scores reported in Cohen et al. 2022 are calculated very differently than the F1 scores we report here and are based on a model trained with data from the same bird as was used in testing, unlike our more general segmentation approach where the model was tested on different birds than were used in training. Thus, the scores reported in Cohen et al. and the F1 scores that we report cannot be compared. 

The discrepancy between the F1_seg scores reported in Gu et al. 2023 and the segmentation F1 scores that we report are likely due to differences in the underlying datasets. Our UTSW recordings tend to have higher levels of both stationary and non-stationary background noise, which make segmentation more challenging. The recordings from Rockefeller were less contaminated by background noise, and they resulted in slightly higher F1 scores. That said, we believe that the primary factor accounting for this difference in scores with Gu et al. 2023 is the granularity of our ‘ground truth’ syllable segments. In our case, if there was never any ambiguity as to whether vocal elements should be segmented into two short syllables with a very short gap between them or merged into a single longer syllable, we chose to split them. WhisperSeg had a strong tendency to merge the vocal elements in ambiguous cases such as these. This results in a higher rate of false negative syllable onset detections, reflected in the low recall scores achieved by WhisperSeg (see Figure 2–figure supplement 1b), but still very high precision scores (Figure 2–figure supplement 1a). While WhisperSeg did frequently merge these syllables in a way that differed from our ground truth segmentation, it did so consistently, meaning it had little impact on downstream measures of syntax entropy (Figure 3c) or syllable duration entropy (Figure 3–figure supplement 2a). It is for that reason that, despite a lower F1 score, we still consider AVN’s automatically generated annotations to be sufficiently accurate for downstream analyses. 

Should researchers require a higher degree of accuracy and precision with their annotations (for example, to detect very subtle changes in song before and after an acute manipulation) we suggest they turn toward one of the existing tools for supervised song annotation, such as TweetyNet.

(4) Texas bias. It is true that comparability across datasets is enhanced when everyone uses the same code. However, the authors' proposal essentially is to replace the bias between labs with a bias towards birds in Texas. The comparison with Rockefeller birds is nice, but it amounts to merely N=1. If birds in Japanese or European labs have evolved different song repertoires, the AVN might not capture the associated song features in these labs well.  

We appreciate the author’s concern about a bias toward birds from the UTSW colony. However, this paper shows that despite training (for the similarity scoring) and hyperparameter fitting (for the HDBSCAN clustering) on the UTSW birds, AVN performs as well if not better on birds from Rockefeller than from UTSW. To our knowledge, there are no publicly available datasets of annotated zebra finch songs from labs in Europe or in Asia but we would be happy to validate AVN on such datasets, should they become available. Furthermore, there is no evidence to suggest that there is dramatic drift in zebra finch vocal repertoire between continents which would necessitate such additional validation. While we didn’t have manual annotations for this dataset (which would allow validation of our segmentation and labeling methods), we did apply AVN to recordings shared with us by the Wada lab in Japan, where visual inspection of the resulting annotations suggested comparable accuracy to the UTSW and Rockefeller datasets. 

(5) The paper lacks an analysis of the balance between labor requirement, generalizability, and optimal performance. For tasks such as segmentation and labeling, fine-tuning for each new dataset could potentially enhance the model's accuracy and performance without compromising comparability. E.g. How many hours does it take to annotate hundred song motifs? How much would the performance of AVN increase if the network were to be retrained on these? The paper should be written in more neutral terms, letting researchers reach their own conclusions about how much manual labor they want to put into their data.  

With standardization and ease of use in mind, we designed AVN specifically to perform fully automated syllable annotation and downstream feature calculations. We believe that we have demonstrated in this manuscript that our fully automated approach is sufficiently reliable for downstream analyses across multiple zebra finch colonies. That said, if researchers require an even higher degree of annotation precision and accuracy, they can turn toward one of the existing methods for supervised song annotation, such as TweetyNet. Incorporating human annotations for each bird processed by AVN is likely to improve its performance, but this would require significant changes to AVN’s methodology, and is outside the scope of our current efforts.

(6) Full automation may not be everyone's wish. For example, given the highly stereotyped zebra finch songs, it is conceivable that some syllables are consistently mis-segmented or misclassified. Researchers may want to be able to correct such errors, which essentially amounts to fine-tuning AVN. Conceivably, researchers may want to retrain a network like the AVN on their own birds, to obtain a more fine-grained discriminative method.  

Other methods exist for supervised or human-in-the-loop annotation of zebra finch songs, such as TweetyNet and DAN (Alam et al. 2023). We invite researchers who require a higher degree of accuracy than AVN can provide to explore these alternative approaches for song annotation. Incorporating human feedback into AVN was never the goal of our pipeline, would require significant changes to AVN’s design and is outside the scope of this manuscript.

(7) The analysis is restricted to song syllables and fails to include calls. No rationale is given for the omission of calls. Also, it is not clear how the analysis deals with repeated syllables in a motif, whether they are treated as two-syllable types or one.  

It is true that we don’t currently have any dedicated features to describe calls. This could be a useful addition to AVN in the future. 

What a human expert inspecting a spectrogram would typically call ‘repeated syllables’ in a bout are almost always assigned the same syllable label by the UMAP+HDBSCAN clustering. The syntax analysis module includes features examining the rate of syllable repetitions across syllable types, as mentioned in lines 222-226 of the revised manuscript. See https://avn.readthedocs.io/en/latest/syntax_analysis_demo.html#Syllable-Repetitions for further details.

(8) It seems not all human annotations have been released and the instruction sets given to experts (how to segment syllables and score songs) are not disclosed. It may well be that the differences in performance between (Gu et al 2023) and (Cohen et al 2022) are due to differences in segmentation tasks, which is why these tasks given to experts need to be clearly spelled out. Also, the downloadable files contain merely labels but no identifier of the expert. The data should be released in such a way that lets other labs adopt their labeling method and cross-check their own labeling accuracy.  

All human annotations used in this manuscript have indeed been released as part of the accompanying dataset. Syllable annotations are not provided for all pupils and tutors used to validate the similarity scoring, as annotations are not necessary for similarity comparisons. We have expanded our description of our annotation guidelines in the methods section of the revised manuscript. All the annotations were generated by one of two annotators. The second annotator always consulted with the first annotator in cases of ambiguous syllable segmentation or labeling, to ensure that they had consistent annotation styles. Unfortunately, we haven’t retained records about which birds were annotated by which of the two annotators, so we cannot share this information along with the dataset. The data is currently available in a format that should allow other research groups to use our annotations either to train their own annotation systems or check the performance of their existing systems on our annotations.  

(9) The failure modes are not described. What segmentation errors did they encounter, and what syllable classification errors? It is important to describe the errors to be expected when using the method. 

As we discussed in our response to this reviewer’s point (3), WhisperSeg has a tendency to merge syllables when the gap between them is very short, which explains its lower recall score compared to its precision on our dataset (Figure 2–figure supplement 1). In rare cases, WhisperSeg also fails to recognize syllables entirely, again impacting its precision score. TweetyNet hardly ever completely ignores syllables, but it does tend to occasionally merge syllables together or over-segment them. Whereas WhisperSeg does this very consistently for the same syllable types within the same bird, TweetyNet merges or splits syllables more inconsistently. This inconsistent merging and splitting has a larger effect on syllable labeling, as manifested in the lower clustering v-measure scores we obtain with TweetyNet compared to WhisperSeg segmentations. TweetyNet also has much lower precision than WhisperSeg, largely because TweetyNet often recognizes background noises (like wing flaps or hopping) as syllables whereas WhisperSeg hardly ever segments non-vocal sounds. 

Many errors in syllable labeling stem from differences in syllable segmentation. For example, if two syllables with labels ‘a’ and ‘b’ in the manual annotation are sometimes segmented as two syllables, but sometimes merged into a single syllable, the clustering is likely to find 3 different syllable types; one corresponding to ‘a’, one corresponding to ‘b’ and one corresponding to ‘ab’ merged. Because of how we align syllables across segmentation schemes for the v-measure calculation, this will look like syllable ‘b’ always has a consistent cluster label (or is missing a label entirely), but syllable ‘a’ can carry two different cluster labels, depending on the segmentation. In certain cases, even in the absence of segmentation errors, a group of syllables bearing the same manual annotation label may be split into 2 or 3 clusters (it is extremely rare for a single manual annotation group to be split into more than 3 clusters). In these cases, it is difficult to conclusively say whether the clustering represents an error, or if it actually captured some meaningful systematic difference between syllables that was missed by the annotator. Finally, sometimes rare syllable types with their own distinct labels in the manual annotation are merged into a single cluster. Most labeling errors can be explained by this kind of merging or splitting of groups relative to the manual annotation, not to occasional mis-classifications of one manual label type as another.

For examples of these types of errors, we encourage this reviewer and readers to refer to the example confusion matrices in figure 2f and Figure 2–figure supplement 3b&e. We also added two paragraphs to the end of the ‘Accurate, fully unsupervised syllable labeling’ section of the Results in the revised manuscript. 

(10) Usage of Different Dimensionality Reduction Methods: The pipeline uses two different dimensionality reduction techniques for labeling and similarity comparison - both based on the understanding of the distribution of data in lower-dimensional spaces. However, the reasons for choosing different methods for different tasks are not articulated, nor is there a comparison of their efficacy.  

We apologize for not making this distinction sufficiently clear in the manuscript and have added a paragraph to the ‘Measuring Song Imitation’ section of the Results explaining the rational for using an embedding model for similarity scoring. 

We chose to use UMAP for syllable labeling because it is a common embedding methodology to precede hierarchical clustering and has been shown to result in reliable syllable labels for birdsong in the past (Sainburg et al. 2020). However, it is not appropriate for similarity scoring, because comparing EMD or MMD scores between birds requires that all the birds’ syllable distributions exist within the same shared embedding space. This can be achieved by using the same triplet loss-trained neural network model to embed syllables from all birds. This cannot be achieved with UMAP because all birds whose scores are being compared would need to be embedded in the same UMAP space, as distances between points cannot be compared across UMAPs. In practice, this would mean that every time a new tutor-pupil pair needs to be scored, their syllables would need to be added to a matrix with all previously compared birds’ syllables, a new UMAP would need to be computed, and new EMD or MMD scores between all bird pairs would need to be calculated using their new UMAP embeddings. This is very computationally expensive and quickly becomes unfeasible without dedicated high power computing infrastructure. It also means that similarity scores couldn’t be compared across papers without recomputing everything each time, whereas EMD and MMD scores obtained with triplet loss embeddings can be compared, provided they use the same trained model (which we provide as part of AVN) to embed their syllables in a common latent space. 

(11) Reproducibility: are the measurements reproducible? Systems like UMAP always find a new embedding given some fixed input, so the output tends to fluctuate.

There is indeed a stochastic element to UMAP embeddings which will result in different embeddings and therefore different syllable labels across repeated runs with the same input. We observed that v-measures scores were quite consistent within birds across repeated runs of the UMAP, and have added an additional supplementary figure to the revised manuscript showing this (Figure 2–figure supplement 4).

Reviewer #1 (Recommendations For The Authors):

(1) Benchmark their similarity score to the method used by Goffinet et al, 2021 from the Pearson group. Such a comparison would be really interesting and useful.  

This has been added to the paper. 

(2) Please clarify exactly what is new and what is applied from existing methods to help the reader see the novelty of the paper.  

We have added more emphasis on the novel aspects of our pipeline to the paper’s introduction. 

Minor:

It's unclear if AVN is appropriate as the paper deals only with zebra finch song - the scope is more limited than advertised.

We assume this is in reference to ‘Birdsong’ in the paper’s title and ‘Avian’ in Avian Vocalization Network. There is a brief discussion of how these methods are likely to perform on other commonly studied songbird species at the end of the discussion section.

Reviewer #2 (Recommendations For The Authors):

A few points for the authors to consider that might strengthen or inform the paper:

(1) In the public review, I detailed some ways in which the SSL+EMD approach is unlikely to be appreciably distinct from the VAE+MMD approach -- in fact, one could mix and match here. It would strengthen the authors' claim if they showed via experiments that their method outperforms VAE+MMD, but in the absence of that, a discussion of the relation between the two is probably warranted.  

This comparison has been added to the paper.

(2) ll. 305-310: This loss of accuracy near the edge is expected on general Bayesian grounds. Any regression approach should learn to estimate the conditional mean of the age distribution given the data, so ages estimated from data will be pulled inward toward the location of most training data. This bias is somewhat mitigated in the Brudner paper by a more flexible model, but it's a general (and expected) feature of the approach.

(3) While the online AVA documentation looks good, it might benefit from a page on design philosophy that lays out how the various modules fit together - something between the tutorials and the nitty-gritty API. That way, users would be able to get a sense of where they should look if they want to harness pieces of functionality beyond the tutorials.

Thank you for this suggestion. We will add a page on AVN’s design philosophy to the online documentation. 

(4) While the manuscript does compare AVN to packages like TweetyNet and AVA that share some functionality, it doesn't really mention what's been going on with the vocalpy ecosystem, where the maintainers have been doing a lot to standardize data processing, integrate tools, etc. I would suggest a few words about how AVN might integrate with these efforts.

We thank the reviewer for this suggestion.

(5) ll. 333-336: It would be helpful to provide a citation to some of the self-supervised learning literature this procedure is based on. Some citations are provided in methods, but the general approach is worth citing, in my opinion. 

We have added a paragraph to the results section with more background on self-supervised learning for dimensionality reduction, particularly in the context of similarity scoring.

(6) One software concern for medium-term maintenance: AVN docs say to use Python 3.8, and GitHub says the package is 3.9 compatible. I also saw in the toml file that 3.10 and above are not supported. It's worth noting that Python 3.9 reaches its end of life in October 2025, so some dependencies may have to be altered or changed for the package to be viable going forward.  

Thank you for this comment. We will continue to maintain AVN and update its dependencies as needed.

Minor points:

(1) It might be good to note that WhisperSeg is a different install from AVN. May be hard for novice users, though there's a web interface that's available. 

We’ve added a line to the methods section making this clear. 

(2) Figure 6b: Some text in the y-axis labels is overlapping here. 

This has been fixed. Thank you for bringing it to our attention. 

(3) The name of the Python language is always capitalized.  

We’ve fixed this capitalization error throughout the manuscript. Thank you.

Reviewer #3 (Recommendations For The Authors):

(1) I recommend that the authors improve the motivation of the chosen tasks and data or choose new tasks that more clearly speak to the optimizations they want to perform. 

We have included more details about the motivation for our LDA classification analysis, age prediction model and embedding model for similarity scoring in the results of the revised manuscript, as discussed in more detail in the above responses to this reviewer. Thank you for these suggestions. 

(2) They need to rigorously report the (classification) scores on the test datasets: these are the scores associated with the cost function used during training.  

Based on this reviewer’s ‘Weaknesses: 3’ comment in the public reviews, we believe that they are referring to a classification score for the triplet loss model. As we explained in response to that comment, this is not a classification task, therefor there is no classification score to report. The loss function used to train the model was a triplet loss function. While we could report these values, they are not informative for how well this approach would perform in a similarity scoring context, as explained above. As such, we prefer to include contrast index and tutor contrast index scores to compare the models’ performance for similarity score, as these are directly relevant to the task and are established in the field for said task.

(3) They need to explain the reasons for the poor performance (or report on the inconsistencies with previous work) and why they prefer a fully automated system rather than one that needs some fine-tuning on bird-specific data.

We’ve addressed this comment in the public response to this reviewer’s weakness points 3, 5, and 6. 

(4) They should consider applying their method to data from Japanese and European labs.  

We’ve addressed this comment in the public response to this reviewer’s weakness point 4.

(5) The need to document the failure modes and report all details about the human annotations.  

We’ve added additional description of the failure modes for our segmentation and labeling approaches in the results section of the revised manuscript.

Details: 

The introduction is very vague, it fails to make a clear case of what the problem is and what the approach is. It reads a bit like an advertisement for machine learning: we are given a hammer and are looking for a nail.  

We thank the reviewer for this viewpoint; however, we disagree and have decided to keep our Introduction largely unchanged. 

L46 That interpretability is needed to maximize the benefits of machine learning is wrong, see self-driving cars and chat GPT.  

This line states that ‘To truly maximize the benefits of machine learning and deep learning methods for behavior analysis, their power must be balanced with interpretability and generalizability’. We firmly believe that interpretability is critically important when using machine learning tools to gain a deeper scientific understanding of data, including animal behavior data in a neuroscience context. We believe that the introduction and discussion of this paper already provide strong evidence for this claim. 

L64 What about zebra finches that repeat a syllable in the motif, how are repetitions dealt with by AVN?  

This is already described in the results section in lines 222-226, and in the methods in the ‘Syntax Features: Repetition Bouts’ section.

L107 Say a bit more here, what exactly has been annotated?  

We’ve added a sentence in the introduction to clarify this. Line 113-115. 

L112 Define spectrogram frames. Do these always fully or sometimes partially contain a vocalization? 

Spectrogram frames are individual time bins used to compute the spectrogram using a short-term Fourier transform. As described in the ‘Methods; Labeling : UMAP Dimensionality Reduction” section, our spectrograms are computed using ‘The short term Fourier transform of the normalized audio for each syllable […] with a window length of 512 samples and a hop length of 128 samples’. Given that the song files have a standard sampling rate of 44.1kHz, this means each time bin represents 11.6ms of song data, with successive frames advancing in time by 2.9ms. These contain only a small fraction of a vocalization. 

L122 The reported TweetyNet score of 0.824 is lower than the one reported in Figure 2a.  

The center line in the box plot in Figure 2a represents the median of the distribution of TweetyNet vmeasure scores. Given that there are a couple outlying birds with very low scores, the mean (0.824 as reported in the text of the results section) is lower than the median. This is not an error.

L155 Some of the differences in performance are very small, reporting of the P value might be necessary. 

These methods are unlikely to statistically significantly differ in their validation scores. This doesn’t mean that we cannot use the mean/median values reported to justify favoring one method over another. This is why we’ve chosen not to report p-values here.

L161 The authors have not really tested more than a single clustering method, failing to show a serious attempt to achieve good performance.  

We’ve addressed this comment in the public response to this reviewer’s weakness point 2.

L186 Did isolate birds produce stereotyped syllables that can be clustered? 

Yes, they did. The validation for clustering of isolate bird songs can be found in Figure 2–figure supplement 4. 

Fig. 3e: How were the multiple bouts aligned?

This is described in lines 857-876 in the ‘Methods: Song Timing Features: Rhythm Spectrograms” section of the paper.

L199 There is a space missing in front of (n=8).  

Thank you for bringing this to our attention. It’s been corrected in the updated manuscript. 

L268 Define classification accuracy.  

We’ve added a sentence in lines 953-954 of the methods section defining classification accuracy. 

L325 How many motifs need to be identified, why does this need to be done manually? There are semiautomated methods that can allow scaling, these should be  cited here. Also, the mention of bias here should be removed in favor of a more extensive discussion on the experimenter bias (traditionally vs Texas bias (in this paper).  

All of the methods cited in this line have graphical user interfaces that require users to select a file containing song and manually highlight the start and end each motif to be compared. The exact number of motifs required varies depending on the specific context (e.g. more examples are needed to detect more subtle differences or changes in song similarity) but it is fairly standard for reviewers to score 30 – 100 pairs of motifs. 

We’ve discussed the tradeoffs between full automation and supervised or human-in-the loop methods in response to this reviewer’s public comment ‘weakness #5 and 6’. Briefly, AVN’s aim is to standardize song analysis, to allow direct comparisons between song features and similarity scores across research groups. We believe, as explained in the paper, that this can be best achieve by having different research groups use the same deep learning models, which perform consistently well across those groups. Introducing semi-automated methods would defeat this benefit of AVN. 

We’ve also addressed the question of ‘Texas bias’ in response to their reviewer’s public comment ‘Weakness #4’. 

L340 How is EMD applied? Syllables are points in 8-dim space, but now suddenly authors talk about distributions without explaining how they got from points to distributions. Same in L925.  

We apologize for the confusion here. The syllable points in the 8-d space are collectively an empirical distribution, not a probability distribution. We referred to them simply as ‘distributions’ to limit technical jargon in the results of the paper, but have changed this to more precise language in the revised manuscript.

L351 Why do authors now use 'contrast index' to measure performance and no longer 'classification accuracy'?  

We’ve addressed this comment in the public response to this reviewer’s weakness points 1 and 2.

Figure 6 What is the confusion matrix, i.e. how well can the model identify pupil-pupil pairings from pupiltutor and from pupil-unrelated pairings? I guess that would amount to something like classification accuracy.  

There is no model classifying comparisons as pupil-pupil vs. pupil-tutor etc. These comparisons exist only to show the behavior of the similarity scoring approach, which consists of a dissimilarity measure (MMD or EMD) applied to low dimensional representations of syllable generated by the triplet loss model or VAE. This was clarified further in our public response to this reviewer’s weakness points 1 and 2. 

L487 What are 'song files', and what do they contain?   

‘Song files’ are .wav files containing recordings of zebra finch song. They typically contain a single song bout, but they can include multiple song bouts if they are produced close together, or incomplete song bouts if the introductory notes were very soft or the bouts were very long (>30s from the start of the file). Details of these recordings are provided in the ‘Methods: Data Acquisition: UTSW Dataset’ section of the manuscript.

L497 Calls were only labelled for tweetynet but not for other tasks.  

That is correct. The rationale for this is provided in the ‘Methods: Manual Song Annotation’ section of the manuscript. 

L637 There is a contradiction (can something be assigned to the 'own manual annotation category' when the same sentence states that this is done 'without manual annotation'?) 

We believe there is confusion here between automated annotation and validation. Any bird can be automatically annotated without the need for any existing manual annotations for that individual bird. However, manual labels are required to compare automatically generated annotations against for validation of the method.

L970 Spectograms of what? (what is the beginning of a song bout, L972). 

The beginning of a song bout is the first introductory note produced by a bird after a period without vocalizations. This is standard.

Reviewer #3 (Public review):

Summary:

The aim of this study was to investigate the temporal progression of the neural response to event boundaries in relation to uncertainty and error. Specifically, the authors asked (1) how neural activity changes before and after event boundaries, (2) if uncertainty and error both contribute to explaining the occurrence of event boundaries, and (3) if uncertainty and error have unique contributions to explaining the temporal progression of neural activity.

Strengths:

One strength of this paper is that it builds on an already validated computational model. It relies on straightforward and interpretable analysis techniques to answer the main question, with a smart combination of pattern similarity metrics and FIR. This combination of methods may also be an inspiration to other researchers in the field working on similar questions. The paper is well written and easy to follow. The paper convincingly shows that (1) there is a temporal progression of neural activity change before and after an event boundary, and (2) event boundaries are predicted best by the combination of uncertainty and error signals.

Weaknesses:

Regarding question 3, I am less convinced by the results. They show that overlapping but somewhat distinct sets of brain regions relate to uncertainty and error boundaries over time. And that some regions show distinct patterns of temporal progressions in pattern change with both types of boundaries. However, most of the effects they observe in this analysis may still be driven by shared variance, as suggested by the results in Figure 6 and the high correlation between the two boundary time series. More specific comments are provided below.

Impact:

If these comments can be addressed sufficiently, I expect that this work will impact the field in its thinking on what drives event boundaries and spur interest in understanding the mechanisms behind the temporal progression of neural activity around these boundaries.

Comments

(1) The current analysis of the neural data does not convincingly show that uncertainty and prediction error both contribute to the neural responses. As both terms are modelled in separate FIR models, it may be that the responses we see for both are mostly driven by shared variance. Given that the correlation between the two is very high (r=0.49), this seems likely. The strong overlap in the neural responses elicited by both, as shown in Figure 6, also suggests that what we see may mainly be shared variance. To improve the interpretability of these effects, I think it is essential to know whether uncertainty and error explain similar or unique parts of the variance. The observation that they have distinct temporal profiles is suggestive of some dissociation, but not as convincing as adding them both to a single model.

(2) The results for uncertainty and error show that uncertainty has strong effects before or at boundary onset, while error is related to more stabilization after boundary onset. This makes me wonder about the temporal contribution of each of these. Could it be the case that increases in uncertainty are early indicators of a boundary, and errors tend to occur later?

(3) Given that there is a 24-second period during which the neural responses are shaped by event boundaries, it would be important to know more about the average distance between boundaries and the variability of this distance. This will help establish whether the FIR model can properly capture a return to baseline.

(4) Given that there is an early onset and long-lasting response of the brain to these event boundaries, I wonder what causes this. Is it the case that uncertainty or errors already increase at 12 seconds before the boundaries occur? Or if there are other makers in the movie that the brain can use to foreshadow an event boundary? And if uncertainty or errors do increase already 12 seconds before an event boundary, do you see a similar neural response at moments with similar levels of error or uncertainty, which are not followed by a boundary? This would reveal whether the neural activity patterns are specific to event boundaries or whether these are general markers of error and uncertainty.

(5) It is known that different brain regions have different delays of their BOLD response. Could these delays contribute to the propagation of the neural activity across different brain areas in this study?

(6) In the FIR plots, timepoints -12, 0, and 12 are shown. These long intervals preclude an understanding of the full temporal progression of these effects.

Author response:

Reviewer #1 (Public review):

Summary:

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

Strengths:

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

We thank the reviewer for their positive comments.

Weaknesses:

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

We thank the reviewer for their comment. The code and data for our manuscript are an important aspect of the study, and we had intended to make them publicly available upon publication. The link to our code and data on figshare can be found here: (https://doi.org/10.6084/m9.figshare.28950032.v1). We will further add this link to the Data Availability Statement of our revised version.  

Reviewer #2 (Public review):

Summary:

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

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

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

Strengths:

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

We thank the reviewer for their positive comments.

Weaknesses:

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

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

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

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

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

References:

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

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

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

Author response:

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

Reviewer #1 (Public review):

Summary:

In this manuscript by Lopez-Blanch and colleagues, 21 microexons are selected for a deep analysis of their impacts on behavior, development, and gene expression. The authors begin with a systematic analysis of microexon inclusion and conservation in zebrafish and use these data to select 21 microexons for further study. The behavioral, transcriptomic, and morphological data presented are for the most part convincing. Furthermore, the discussion of the potential explanations for the subtle impacts of individual microexon deletions versus lossof-function in srrm3 and/or srrm4 is quite comprehensive and thoughtful. One major weakness: data presentation, methods, and jargon at times affect readability / might lead to overstated conclusions. However, overall this manuscript is well-written, easy to follow, and the results are of broad interest.

We thank the Reviewer for their positive comments on our manuscript. In the revised version, we will try to improve readability, reduce jargon and avoid overstatements.  

Strengths:

(1) The study uses a wide variety of techniques to assess the impacts of microexon deletion, ranging from assays of protein function to regulation of behavior and development.

(2) The authors provide comprehensive analyses of the molecular impact of their microexon deletions, including examining how host-gene and paralog expression is affected.

Weaknesses:

Major Points:

(1) According to the methods, it seems that srrm3 social behavior is tested by pairing a 3mpf srrm3 mutant with a 30dpf srrm3 het. Is this correct? The methods seem to indicate that this decision was made to account for a slower growth rate of homozygous srrm3 mutant fish. However, the difference in age is potentially a major confound that could impact the way that srrm3 mutants interact with hets and the way that srrm3 mutants interact with one another (lower spread for the ratio of neighbour in front value, higher distance to neighbour value). This reviewer suggests testing het-het behavior at 3 months to provide age-matched comparisons for del-del, testing age-matched rather than size-matched het-del behavior, and also suggests mentioning this in the main text / within the figure itself so that readers are aware of the potential confound.

Thank you for bringing up this point. For the tests shown in Figure 5, we indeed decided to match the pairs involving srrm3 mutant fish by fish size since we reasoned this would be more comparable to the other lines, both biologically and methodologically (in terms of video tracking, etc.). However, we are confident the results would be very similar if matched by age, since the differences in social interactions between the srrm3 homozygous mutants and their control siblings are very dramatic at any age. As an example, this can be appreciated, in line with the Reviewer's suggestion, in Videos S2 and S3, which show groups of five 5 mpf fish that are either srrm3 mutant or wild type. It can be observed that the behavior of 5 mpf WT fish (Video S3) is very similar to those of 1 mpf WT fish pairs, with very small interindividual distances, while the difference with repect to the srrm3 mutant group (Video S2) is dramatic. We nonetheless agree that this decision on the experimental design should be clearly stated in the main text and figure legend and we have done so in the revised version.

(2) Referring to srrm3+/+; srrm4-/- controls for double mutant behavior as "WT for simplicity" is somewhat misleading. Why do the authors not refer to these as srrm4 single mutants?

This comment applies to Figure 4 as well as the associated figure supplements. We reasoned that this made the understanding of plots easier, but the Reviewer is correct that it can be misleading. As a middle ground, we have now changed Figure 4 to follow the nomenclature of Figure 3D (WD, HD, DD), which is further explained in the legend, but kept the original format in the figure supplements for consistency with the (many) other plots in those figures.

(3) It's not completely clear how "neurally regulated" microexons are defined / how they are different from "neural microexons"? Are these terms interchangeable?

Yes, they are interchangeable. We have now double checked the wording to avoid confusion and for consistency.

(4) Overexpression experiments driving srrm3 / srrm4 in HEK293 cells are not described in the methods.

We apologized for this omission. We now briefly describe the data and asscoiated methods in more detail in the revised version; however, please note that the data was obtained from a previous publication (Torres-Mendez et al, 2019), where the detailed methodology is reported.

(5) Suggest including more information on how neurite length was calculated. In representative images, it appears difficult to determine which neurites arise from which soma, as they cross extensively. How was this addressed in the quantification?

We have added further details to the revised version. With regards to the specific question, we would like to mention that this has not been a very common issue for the time points used in the manuscript (10 hap and 24 hap). At those stages, it was nearly always evident how to track each individual neurite. Dubious cases were simply ignored and not measured, as we aimed for 100 neurites per well. Of course, such complex cases become much more common at later time points (48 and 72 hap), which were not used in this study.

Reviewer #2 (Public review):

Summary:

This manuscript explores in zebrafish the impact of genetic manipulation of individual microexons and two regulators of microexon inclusion (Srrm3 and Srrm4). The authors compare molecular, anatomical, and behavioral phenotypes in larvae and juvenile fish. The authors test the hypothesis that phenotypes resulting from Srrm3 and 4 mutations might in part be attributable to individual microexon deletions in target genes.

The authors uncover substantial alterations in in vitro neurite growth, locomotion, and social behavior in Srrm mutants but not any of the individual microexon deletion mutants. The individual mutations are accompanied by broader transcript level changes which may resemble compensatory changes. Ultimately, the authors conclude that the severe Srrm3/4 phenotypes result from additive and/or synergistic effects due to the de-regulation of multiple microexons.

Strengths:

The work is carefully planned, well-described, and beautifully displayed in clear, intuitive figures. The overall scope is extensive with a large number of individual mutant strains examined. The analysis bridges from molecular to anatomical and behavioral read-outs. Analysis appears rigorous and most conclusions are well-supported by the data.

Overall, addressing the function of microexons in an in vivo system is an important and timely question.

Weaknesses:

The main weakness of the work is the interpretation of the social behavior phenotypes in the Srrm mutants. It is difficult to conclude that the mutations indeed impact social behavior rather than sensory processing and/or vision which precipitates apparent social alterations as a secondary consequence. Interpreting the phenotypes as "autism-like" is not supported by the data presented.

The Reviewer is absolutely right. It was not our intention to imply that these social defects should be interpreted simply as autistic-like. It is indeed very likely that the main reason for the social alterations displayed by the srrm3 mutants is their impaired vision. We have now added this discussion point explicitly in the revised version. 

Reviewer #3 (Public review):

Summary:

Microexons are highly conserved alternative splice variants, the individual functions of which have thus far remained mostly elusive. The inclusion of microexons in mature mRNAs increases during development, specifically in neural tissues, and is regulated by SRRM proteins. Investigation of individual microexon function is a vital avenue of research since microexon inclusion is disrupted in diseases like autism. This study provides one of the first rigorous screens (using zebrafish larvae) of the functions of individual microexons in neurodevelopment and behavioural control. The authors precisely excise 21 microexons from the genome of zebrafish using CRISPR-Cas9 and assay the downstream impacts on neurite outgrowth, larvae motility, and sociality. A small number of mild phenotypes were observed, which contrasts with the more dramatic phenotypes observed when microexon master regulators SRRM3/4 are disrupted. Importantly, this study attempts to address the reasons why mild/few phenotypes are observed and identify transcriptomic changes in microexon mutants that suggest potential compensatory gene regulatory mechanisms.

Strengths:

(1) The manuscript is well written with excellent presentation of the data in the figures.

(2) The experimental design is rigorous and explained in sufficient detail.

(3) The identification of a potential microexon compensatory mechanism by transcriptional alterations represents a valued attempt to begin to explain complex genetic interactions.

(4) Overall this is a study with a robust experimental design that addresses a gap in knowledge of the role of microexons in neurodevelopment.

Thank you very much for your positive comments to our manuscript.

Reviewer #1 (Recommendations for the authors):

Minor Suggestions

(1) Axes are often scaled differently even between panels in the same figure. For example in Figure 5 - supplement 10, the srrm3_17 y axis scales from 0-20, while the neighboring panels scale from ~1-2.5. This somewhat underrepresents the finding that srrm3 mutants have much larger inter-individual distances. Similarly, in the panel above (src_1), the y-axis is scaled to include a single point around 17cm. As a result, it appears at first glance that the src_1 trials resulted in much lower inter-individual distance. Suggest scaling all of these the same to improve readability.

While the Reviewer is certainly correct, after careful consideration we decided to have autoscaled axis to prioritize within-plot visualization (i.e. among genotypes within an experiment) than across plots (i.e. among experiments and lines).

(2) Attention to italicizing gene names.

Thanks.

(3) In many points in the methods, we are instructed to "see below." Suggest directing the reader to a particular section heading.

We found only one such instance, and we directed the reader to the specific section, as suggested.

(4) In Methods, remove "in the corpus callosum." This is not an accurate descriptor for the site at which Mauthner axons cross.

This is absolutely correct, apologies for this mistake.

Clarify:

(1) In the results section, "tissue-specific regulation was validated..." - suggest mentioning that this was performed in adult tissues / describe dissection in the methods.

Added.

(2) In the results section, the meaning of "no event ortholog" is not clear. Does this mean that a microexon does not have a human homolog? If so, suggest stating more clearly.

Correct. We have added addition information.

(3) In the results, the authors state that 78% of microexons are affected by srrm3/4 loss-offunction. Suggest stating the method used here (e.g. RNA-seq in mutants as compared to siblings)

Added.

(4) It is not clear what "siblings for the main founders means" for example in 3D. Is this effectively the analysis of microexon knockouts across multiple independent lines? Are the lines pooled for stats, for example in 3C?

The main founder correspond to that listed as _1 and as default for experiments when only one found is used. We now explicitely state this.  

For 3C, the lines are not pooled for stats; the stats correspond only to the main founder for each line. However, for each main founder line, multiple experiments are usually analyzed together and the stats are done taking their data structure into account (i.e. not simply pooling the values).

(5) The purpose and a general description of NanoBRET assays should be included in the results.

We added the main purpose of the NanoBRET assays (testing protein-protein interactions).

(6) Specify that baseline behavior is analyzed in the light.

Added.

(7) In Figure 4A, adult fish are schematized being placed into a 96-well plate. Suggest using the larval diagram as in Figure 6 for accuracy.

Done.

(8) In Figure 4, plot titles could be made more accessible, especially in 4 F. Suggest removing extraneous information / italicizing gene names, etc. In G, suggest writing out Baseline, Dark, and Light to make it more accessible. Same in 4B.

We have implemented some of the suggestions. In particular, italics were not used, since we are referring to the founder line, not the gene.

(9) Figure 6 legend B - after (barplots), suggest inserting the word "and", to make clear that barplots indicate host gene *and* closely related paralogs are indicated by dots.

Done.

(10) In methods: "To better capture all microexons..." This sentence is difficult to understand. Suggested edit: "we excluded *from our calculation?* tissues with known or expected partial overlap... from comparison (for example, ...).

Done.

(11) In the methods, "which were defined with similar parameters but -min_rep 2." Suggest spelling this out, e.g. "with similar parameters, but requiring sufficient read coverage in at least n=2 samples per valid tissue group, whereas we only required one.".

Done.

(12) RNA was extracted for event and knockout validations. What does event mean here?

Event refers to the validation of the exon regulatory pattern in WT tissues. We added this information.

Provide definitions for abbreviations:

(1) (Figure 6) Delta corrected VST Expression.

Done.

(2) "Mic-hosting genes" paralogs.

Done.

(3) In Figure 1F, "emic" is not defined.

Done.

Misspellings:

All corrected.

(1) Figure 6B (percentile is spelled percentil).

(2) Figure 6B legend (bottom or top decile*).

(3) Figure 6D - Schizophrenia* genes.

(4) In Zebrafish husbandry and genotyping: suggest "srrm3 mutants grew more slowly.".

(5) In results, "reduced body size at 90pdf" > 90dpf.

Reviewer #2 (Recommendations for the authors):

(1) Characterization of microexon mutants (Figure 2): The semi-quantitative PCR with flanking primers (Figure 2, supplement1) is well-suited to assess successful deletion of the exon and enables detection of potential mis-splicing around the alternative segment. However, it does not quantify the impact on total transcript levels. The authors should complement those experiments with qPCR measures of the transcript levels - otherwise, it is difficult to link mutant phenotypes to isoforms (as opposed to alterations in the level of gene expression). This point is somewhat addressed in Figure 6 by the RNA Seq analysis but it might help to add data specifically in Figure 2.

As the Reviewer says, this point is explicitely addressed in Figure 6, where were show the change in the host gene's expression that follows the the removal of some microexons. We prefer to keep this in Figure 6, for consistency, as we believe this is not a direct (regulatory) consequence of the removal, but more likely a compensation effect.

(2) Social behavior alterations in juvenile fish: The authors report "increased leadership" in Srrm3 mutant fish. However, these fish have impaired vision. Thus, "increased leadership" may simply reflect the fact that they do not perceive their conspecifics and, thus, do not follow them. The heterozygous conspecific will then mostly follow the Srrm3 mutant which appears as the mutant exhibiting an increase in leadership. Figure 5D suggests that Srrm3 del and het fish have the same ratio of "neighbor in front" which would be consistent with the hypothesis that the change in this metric is a consequence of a loss of following behavior due to a loss of vision. The authors should either adjust the discussion of this point or assess with additional experiments whether this is indeed a "social phenotype" or rather a secondary consequence of a loss of vision.

The Reviewer is absolutely correct, and we have thus modified the short discussion directly related to these patterns.

(3) The discussion centers on potential reasons why only mild phenotypes are observed in the single microexon mutants. One caveat of the phenotypic analysis provided in the manuscript is that it does not very deeply explore the phenotypic space of neuronal morphologies or circuit function. The behavioral and anatomical read-outs are rather coarse. There are no experiments exploring fine-structure of neuronal projections in vivo or synapse number, morphology, or function. Moreover, no attempts are made to explore which cell types normally express the microexons to potentially focus the loss-of-function analysis to these specific cell types. Of course, such analysis would substantially expand the scope of a study that already covers a large number of mutant alleles. However, the authors may want to add a discussion of these limitations in the manuscript.

The Reviewer is correct. We aimed at covering this when referring to "(i) we may not be assessing the traits that these microexons are impacting, (ii) we may not have the sensitivity to robustly measure the magnitude of the changes caused by microexon removal". We have now added some of the specific points raised by the Reviewer as examples.

(4) Note typos in Figure 6D: "schizoFrenia", "WNT signIalling"

Done.

Reviewer #3 (Recommendations for the authors):

I only have a few minor suggestions for the authors.

(1) It is interesting that a not insignificant number of microexon deletions (3/21) result in cryptic inclusions of intron fragments, and perhaps alludes to an as yet unreported molecular function of microexons in the regulation of host gene expression. Is it possible that microexon inclusion in these 3 genes could be important for expression? I think this requires some further discussion, as (if I'm not mistaken) microexons have thus far only been hypothesised to act as modulators of protein function, not as gene regulatory units.

While we see that microexon removal can impact expression of the host gene (Figure 6), this is likely a compensatory mechanism (or so we suggest). We do not think these three cases are related to a putative physiological regulation, since the cryptic exons appear only in the deletion line. On the contrary, we think these are "regulatory artifacts" that originate in the nonWT mutated context. I.e. we removed the exon but some splicing signals remained in the intron, which are then recoginized by the spliceosome that incorrectly includes a different piece of the intron.

(2) The flow of the text accompanying the molecular investigation of microexon function for evi5b and vav in Figure 3 could be improved. The text currently fades out with a speculative explanation for the lack of evi5b interaction phenotype. This final sentence could be moved to the discussion and replaced with a more general summary of the data.

We have now swapped the order in which these results are described and leave out the discussion about evi5b's microexon function.

(3) Is this a co-submission with Calhoun et al? If so, both papers should reference each other in the discussion and discuss the relative contributions of each.

Done

(4) "1 × 104 cells" in methods Nanobret paragraph should be superscript.

Done

Cyrus is such a fascinating leader! He conquered Babylon without bloodshed, supported the Jews, and even started building amazing projects like the Royal Road. It’s wild to think how his actions might have even influenced the development of Jewish monotheism!

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

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Reply to the reviewers

Reviewer #1

Evidence, reproducibility and clarity

SUMMARY

In this study, Fernandes and colleagues addressed the question of the role of micro-RNAs in regulating the coupling between organ growth and developmental timing. Using Drosophila, they identified the conserved micro-RNA miR-184 as a regulator of the developmental transition between juvenile larval stages and metamorphosis. This transition is under the control of the steroid hormone Ecdysone, and has been shown to be modulated in case of abnormal tissue growth to adjust the duration of larval growth in response to developmental perturbations. The relaxin-like hormone Dilp8 has been identified as a key secreted factor involved in this coupling. Here, the authors show that miR-184 is involved in the regulation of Dilp8 expression both in physiological conditions and upon growth perturbation. They propose that this function is carried out in imaginal tissues, where miR-184 levels are modulated by tissue stress. While several factors have already been involved in triggering sharp dilp8 induction at the transcriptional level, this study adds another level of complexity to the regulation of Dilp8 by proposing that its expression is fine-tunned post-transcriptionally through repression by miR-184.

__MAJOR COMMENTS______

Overall, the manuscript is well organized, and the logics of the experimental plan well presented. The results are clear, and I appreciate the quality of the pupariation curves. However, I believe that two main conclusions of the paper are not fully supported by the results presented in the figures: the direct regulation of dilp8 3'UTR by miR-184, and the specificity of this regulation in imaginal discs. Here I develop in more details these two aspects.

Comment 1) The strategy of the 3'UTR sensor is not fully optimized. Indeed, in most experiments, qRT-PCR is used to assess dilp8 expression levels, although it reflects both transcriptional and post-transcriptional. Importantly, to show that post-transcriptional regulation is involved in the response to tissue damage, the levels of the 3'UTR sensor should be analyzed in discs expressing RAcs (showing at the same time that the response is cell-autonomous in the discs). The expected upregulation of the sensor should be prevented by simultaneous expression of miR-184. This approach would shed light on the relative contribution of transcriptional versus post-transcriptional regulation of dilp8 in response to growth perturbation.

Response: We thank the reviewer for this comment. We agree that qRT-PCRs do not distinguish between transcriptional and post-transcriptional changes of dilp8 levels, in response to changes in miR-184 levels and tissue damage. In addition to the qRT-PCR data we have looked at dilp8-3’UTR-GFP reporter in response to overexpression of miR-184 in the wingdisc using patched-Gal4 driver, which show downregulation of the GFP reporter in the ptc domain (Fig 4C-D’). This suggests that dilp8 mRNA is a direct target of miR-184 by post-transcriptional regulation through its 3’UTR. Further, to confirm the specificity of the effect of miR-184 on dilp8-3’UTR, we generated a dilp8-3’UTR mutant in which the single target site for miR-184 was mutated. We show that the mutated dilp8-3’UTR reporter doesn’t show any regulation in response to miR-184 overexpression in the ptc domain of the wingdisc (Fig. 4E, E’, F, F’). This experiment confirms the specificity of the dilp8-3’UTR regulation by miR-184.

As suggested by the reviewer we analysed dilp8-3’UTR-GFP reporter expression by overexpressing RicinA using ptcGAL4 driver in the wing imaginal disc (Fig. S6F-G’). We observed a slight but consistent increase in the dilp8-3’UTR-GFP reporter expression, indicating post-transcriptional regulation of dilp8 expression in response to tissue damage. However, the increase of reporter GFP levels observed in this experiment in response to tissue damage is mild (Fig. S6F-G’) than expected based on the qRT-PCR results (Fig S6A and B). We have added this new data to the manuscript (Fig. S6F-G’).

We propose the following reasons to explain this result:

a) both transcriptional and post-transcriptional regulation of dilp8 mRNA in response to developmental perturbations

b) the data on 3’UTR reporter GFP is specifically from the ptc domain expression of RicinA, whereas for dilp8 transcript levels we have expressed RicinA in all larval imaginal tissues, or in the entire wing imaginal disc, which could be one of the reasons for the stronger effect seen on dilp8 mRNA levels

c) we are not certain if the tubulin-promoter driven dilp8-3’UTR GFP reporter reflects post-transcriptional regulation of dilp8 by miR-184 efficiently in comparison to qRT-PCR. This is especially as the reporter-GFP-3’UTR will be expressed at very high levels due to the tubulin promoter, a majority of this reporter-GFP mRNA may not be relieved from degradation due to the moderate suppression of miR-184 in response to RicinA overexpression.

Thus, our experiments suggest that dilp8 levels are regulated post-transcriptionally by miR-184 which contributes to pupariation delays in response to tissue damage. In support of this, we could rescue pupariation delays and dilp8 induction caused by RicinA expression using overexpression of miR-184 (Figs 5B, C). Thus, we confirm that the effect of post-transcriptional regulation by miR-184 during developmental perturbations also contributes to dilp8 induction and pupariation delays. Unfortunately, due to experimental limitations we could not perform simultaneous expression of RicinA and miR-184 to evaluate the rescue of dilp8-3’UTR-GFP sensor expression. The levels of dilp8-3’UTR sensor GFP is reduced efficiently by miR-184 overexpression (Fig 4D), which prevented us from attempting the rescue of the moderate increase of dilp8-3’UTR GFP levels in response to RicinA.

Comment 2) In my opinion, the use of a 3'UTR sensor is not sufficient to conclude that the regulation by miR-184 is direct, as miR-184 could also regulate an intermediate factor that acts on dilp8 post-transcriptional regulation. To solve this issue, a common strategy is to generate a 3'UTR sensor with mutated binding sites that should abolish the regulation by miR-184. This mutated 3'UTR might also respond differently to tissue damage, which would strongly support the conclusions of the study.

Response: We couldn’t agree more with the reviewer, this comment is addressed in the response to comment 1. We have confirmed the specificity of regulation of dilp8-3’UTR by miR-184 using target site mutated dilp8-3’UTR (new figures added to the manuscript Fig. 4E, E’, F, F’). We tested if the changes in dilp8 mRNA levels in response to tissue damage is post-transcriptional mediated by miR-184. We observe that there is a slight, but consistent increase of dilp8-3’UTR GFP reporter levels in the ptc domain of wingdisc in response to RicinA expression, suggesting a role for miR-184 mediated post-translational regulation of dilp8. However, we have not yet tested the mutated dilp8-3’UTR GFP reporter in response to tissue damage.

Comment 3) Concerning the tissue-specific regulation of Dilp8 by miR-184, these results need to be strengthened. Indeed, this comes mostly from phenotypes observed with rn-GAL4. Although this is a classical tool for driving expression in imaginal discs, rn-GAL4 also drives strong expression in other tissues that could contribute to triggering a delay, such as the CNS and part of the gut (proventriculus). In our hands, some growth phenotypes in the wing obtained with rn-GAL4 could be fully reverted by blocking GAL4 in the CNS indicating that the phenotype was not wing-specific. Importantly, miR-184 seems to be highly expressed in the CNS according to FlyBase, reinforcing the possibility that it plays a role in this organ. Here I propose approaches to confirm that miR-184 mediated regulation of dilp8 and developmental timing indeed occur in the discs:

- Another driver with less secondary expression sites could be used (pdmR11F02-GAL4), or rn-GAL4 could be combined with an elav-GAL80 to prevent expression in most neurons. - The authors could identify the source of Dilp8 upregulation in miR-184 mutants using tissue-specific qRT-PCR instead of whole larvae expression like in Fig 4A-B. - This tissue-specific upregulation could be functionally tested using a rescue experiment, in which the delay observed in miR-184 mutants could be rescued by disc-specific downregulation of Dilp8 (using pdm2-GAL4 for instance).

Response: We are thankful to the reviewer, and agree that it is important to show that the effects that we see using rn-Gal4 are specific to imaginal discs, and not due to an effect in CNS. We tested this by expressing miR-184 sponge in the CNS. Though miR-184 is highly expressed in the larval CNS, downregulation of miR-184 specifically in the pan-neuronal background using elav-GAL4 led to no effects on pupariation timepoint. We have added this as supplementary data Figure S4. Therefore, we believe that the miR-184 downregulation phenotype in the rnGAL4 background can be mainly attributed to its role in the imaginal discs. In addition, as suggested by the reviewer we have also demonstrated that downregulation of miR-184 in the imaginal discs using rnGAL4 driver leads to an increase in dilp8 expression (Fig S5B). Thus confirming that dilp8 mRNA is enhanced in the imaginal discs by blocking miR-184.

OPTIONAL: Because it is known that dilp8 is strongly regulated at the transcriptional level, the relative input from post-transcriptional upregulation is an important question arising from this study. Although it might be a more long-term approach, I believe that generating a Dilp8 mutant lacking its 3'UTR or, even better, with mutated miR-184 binding sites, would shed light on the role of this regulation for the response to growth perturbation and/or developmental stability (fluctuating asymmetry).

Response: We thank the reviewer for the suggestion. This would have been an interesting experiment to carry out especially in the context of fluctuating asymmetry.

MINOR COMMENTS

1. __ I think that a number of results could be moved to SI as they are either controls, or reproduce published data without bringing novelty. For instance, results in Fig 5A-D are similar to data published by Sanchez et al, as stated in the text. Fig6A as well.__

__Response: __We thank the reviewer for this suggestion, Fig. 5A-D, and F has been moved to Fig. S6A-E. We have also moved data from Fig. 6 to Fig. 5, as a result Fig 6 A-D has become Fig. 5 B-D.

__ Fig 6D is quite mysterious, as it suggests that basal JNK activation regulates miR-184, which is different from a context of tissue damage. I think that this result could be removed. Alternatively, if the authors want to dig in that direction, more experiments should be provided, such as bskDN expression in an RAcs context and the effects on miR-184 levels and the 3'UTR sensor (since transcript levels are already published).__

Response: We would like to clarify that our experiments suggest that endogenous JNK signalling negatively regulates miR-184, as blocking basal JNK signalling using bskDN increased the levels of miR-184 (changed to Fig 5D). Enhanced JNK signalling has been reported to be involved in tissue damage responses, and we propose that RicinA mediated increase in JNK signalling leads to the reduction of miR-184 (changed to Fig 5A, S6D-E). However, we are not strongly implying this as we did not co-express RicinA and bskDN to show that JNK signalling is responsible for the drop in miR-184 levels in response to tissue damage. We thank the reviewer for seeking this explanation, we have rewritten the results section to improve clarity.

__ The references related to Dilp8 should be checked more in detail in the intro and discussion. About Dilp8 and developmental stability: remove the ref to Colombani et al 2012, instead put Boone et al 2016 and add Blanco-Obregon et al 2022 (in addition to Garelli et al 2012 who initially identified this phenotype. About Lgr3 as the receptor for Dilp8: add Colombani et al, Current Biology 2015, and cite here Vallejo et al 2015, Garelli et al 2015. Among the important transcriptional regulators of Dilp8, Xrp1 could be mentioned (Boulan et al 2019, Destefanis et al 2022) as it plays a complementary function to JNK depending on the type of tissue stress.__

__Response: __We are really sorry for the glaring errors in citing appropriate references. We thank the reviewer for correcting this for us. We have made necessary changes to the text.

Significance

GENERAL ASSESSMENT This study provides convincing data showing that the conserved microRNA miR-184 plays a role in regulating developmental timing in Drosophila through modulating the levels of Dilp8, a key factor in the coupling between tissue growth and developmental transitions. The results are convincing, but the general conclusions of the paper need to be strengthened regarding the direct regulation of dilp8 by miR-184 and the tissue-specificity of this interaction.

ADVANCE Dilp8 is a key factor that modulates growth and timing in response to developmental perturbations and contributes to developmental precision in physiological conditions. As such, its regulation has been studied by different groups in the last decade, leading to the identification of several inputs for its transcriptional regulation. Here, the authors uncover a post-transcriptional regulation by miR-184, adding another level of regulation of Dilp8 that contribute to ensuring proper regulation of developmental timing, and opening the possibility that miR-184 might play similar roles in other species.

AUDIENCE This study is of interest for researchers in the field of basic science, with a focus on developmental timing, tissue damage and biological function of microRNAs.

REVIEWER EXPERTISE Drosophila, growth control, developmental timing, Dilp8.

Reviewer #2

Evidence, reproducibility and clarity

Drosophila has helped to characterize the mechanisms that coordinate tissue growth with developmental timing. The insulin/relaxin-like peptide Dilp8 has been identified as a key factor that communicates the abnormal growth status of larval imaginal discs to neuroendocrine neurons responsible for regulating the timing of metamorphosis. Dilp8, derived from imaginal discs, targets four Lgr3-positive neurons in the central nervous system, activating cyclic-AMP signaling in an Lgr3-dependent manner. This signaling pathway reduces the production of the molting hormone, ecdysone, delaying the onset of metamorphosis. Simultaneously, the growth rates of healthy imaginal tissues slow down, enabling the development of proportionate individuals.

In this manuscript "miR-184 modulates dilp8 to control developmental timing during normal growth conditions and in response to developmental perturbations" by Dr. Varghese and colleagues, the authors identify a new post transcriptional regulator of Dilp8. The authors show that miR-184 plays a pivotal role in tissue damage responses by inducing dilp8 expression, which in turn delays pupariation to allow sufficient time for damage repair mechanisms to take effect.

Major points:

Comment 1) In most of the experiments for percentage of pupariation, the 50% pupariation in control is around 110 hours AED in figures 1, 2 and 3. In figures 5 and 6 using the UAS Ricin, the controls are more around 90 hours AED. Why this discrepancy?

Response: We thank the reviewer for asking for this clarification. The former experiments for Figs 1-3 were carried out at 25oC while the latter experiments with a cold sensitive version of RicinA (UAS-RAcs), Figs 5 and 6 (now changed to Figs. 5 and S6 as suggested by reviewer #1) were carried out at 29oC (permissive temperature). This difference in temperature has led to alterations in pupariation timing. We apologise for not having mentioned this in the text, now we have made necessary corrections to the methods section clearly indicating this.

Comment 2) What is the mechanism behind the expression of miR-184 in stress conditions? Is miR-184 also implicated in other conditions giving rise to a developmental delay (X-rays irradiation or animal bearing rasV12, scrib-/- tumors)?

Response: We thank the reviewer for these questions.

a) In response to developmental perturbations by RicinA, we believe that activation of JNK signalling controls miR-184 expression. We propose this as our experiments show that imaginal disc damage leads to enhancement of JNK signalling and increase in dilp8 mRNA levels (as reported earlier by Colombani et al 2012; Sánchez et al 2019), and a simultaneous reduction of miR-184 (Figs. S6A, D, E). We also have performed new experiments to show that in response to RicinA expression in the wingdisc there is moderate increase in the dilp8-3’UTR-GFP sensor expression (Figs. S6F-G’), indicating a post-transcriptional regulation of dilp8 expression in response to tissue stress. We also show that RicinA induced dilp8 expression and pupariation delay can be rescued by increasing miR-184 levels (Fig 5B and C), suggesting that the reduction of miR-184 in response to tissue damage contributes to the damage responses. In a separate experiment we show that blocking the endogenous JNK pathway by the expression of bskDN enhances miR-184 levels, suggesting that miR-184 is under the regulation of JNK signalling (Fig 5D). Hence, we speculate that during tissue stress, activation of JNK signalling leads to a reduction of miR-184 levels which contributes to regulating the levels of dilp8 post-transcriptionally and resulting in pupariation delays. The text has been modified to explain this better.

b) In a previous paper by Shu et al., 2017 (https://doi.org/10.18632/oncotarget.22226) decreased expression of miR-184 was observed in a lglRNAi; RasV12 tumor background. Apart from this various studies have shown that dilp8 levels increase in response to tumour, radiation stress, apoptosis, and tissue damage (Yeom et al 2021, Ray et al 2019, Demay et al 2014, Katsuyama et al 2015, Colombani et al 2012, Garelli et al 2012). Whether the regulation of dilp8 by miR-184, occurs in these backgrounds is yet to be tested. We have now discussed this possibility in the manuscript.

Comment 3) dilp8 mutant animals have also been shown to be more resistant to starvation or desiccation (https://doi.org/10.3389/fendo.2020.00461). Is miR-184 implicated in this answer?

Response: We thank the reviewer for this question. In our earlier experiments miR-184 has been demonstrated to be regulated by nutrition in the larval stages and lack of miR-184 led to enhanced larval death in response to diet restriction (Fernandes et al., 2022). miR-184 was also demonstrated to play a role in the insulin producing cells (IPCs) in regulating lifespan (Fernandes & Varghese., 2022). In the current work, we propose miR-184 to act upstream of dilp8 in response to stress stimuli. Hence, it is possible that miR-184 might be involved in responses to starvation and desiccation stress in the adult female flies, by regulating dilp8 levels post-transcriptionally. However, it has not been tested yet if the miR-184 regulation of dilp8 plays a role in resistance to starvation or desiccation in adult females, as this was not within the scope of the current study. We have now added this reference in the discussion section.

Comment 4) dilp8 expression has been also shown to be regulated by Xrp1 in response to ribosome stress (https://doi.org/10.1016/j.devcel.2019.03.016). This paper should be included in the manuscript. Is it possible that the expression levels of miR184 are regulated by Xrp1?

Response: We thank the reviewer for the suggestion and have incorporated the reference into the paper. During ribosome stress in the larval imaginal discs the stress-response transcription factor Xrp1 acts through dilp8 in regulating systemic growth. We agree with the reviewer, it is possible that expression of miR-184 is regulated by Xrp1. Currently we have not explored this possibility. We have now added this to the discussion section.

Minor points:

1. __ Does the overexpression of miR184 induce an increased fluctuating asymmetry?__

Response: We thank the reviewer for asking this question. The role of dilp8 in the fluctuation asymmetry is only observed in the dilp8 hypomorphic mutant background. To replicate this we would have to overexpress miR-184 in either the whole larvae or in the wing discs. Unfortunately overexpression of miR-184 in the wing discs (using rnGAL4) leads to pupal lethality while as overexpression of miR-184 in the whole larvae leads to embryonic lethality and therefore we were not be able to conclude from our experiments if miR-184 overexpression induces increased fluctuating asymmetry.

2. There are 2 references Colombani et al. (2012 for Dilp8 and 2015 for Lgr3). Can you double check that they are used accordingly

Response: We thank the reviewer for pointing these errors out and we have incorporated these changes into the paper.

Significance

Altogether, the paper present compiling lines of evidence supporting the proposed model. The experiments are well designed and are convincing. The papers is interesting and relevant for a broad audience.

__Reviewer #3 __

Evidence, reproducibility and clarity (Required):

This is an interesting study demonstrating an interaction between miR-184 and the Drosophila insulin-like peptide 8 (dilp8) in the tissue damage response. The authors show that Dilp8 activity is negatively regulated by miR-184, apparently through direct interaction between miR-184 and the dilp8-3'UTR, which leads to lower dilp8 mRNA transcript levels, via an undetermined mechanism, supposedly its degradation? Furthermore, the authors show that during aberrant tissue growth, miR-184 levels are very slightly downregulated (see comment below), and based on other experiments, imply causation of this with the increased dilp8 mRNA levels that occur in these tissues, again via an unclear mechanism: upregulation or stabilization of dilp8 mRNA. The authors present evidence that the JNK pathway, which had been known to be critical for dilp8 mRNA upregulation upon tissue damage, does so via miR-184.

Major Comments:

__Comment 1: The data showing the direct regulation of dilp8-3'UTR by miR-184 are not very strong and would require more controls to strengthen the claim, as described below. __

Response: We have performed new experiments to validate that dilp8-3’UTR is regulated by miR-184. Please see the detailed responses to comments 10-12 below.

__Comment 2: The miR-184 effects are also very small (less than 2-fold reduction with tissue damage; or less than 2-fold induction with JNK-pathway inhibition via bskDN). These two points are the weakest part of the manuscript and model. __

Response: We agree with the reviewers on this point. The reduction in miR-184 levels in response to RicinA expression is modest (25–30%), and the induction of miR-184 in response to bskDN expression is less than two-fold (Figs. 5A and D). In contrast, dilp8 transcript levels increase several-fold in response to RicinA expression (Fig. 5C, S6A and B). Since we measure dilp8 transcript levels by qPCR, we detect both transcriptional and post-transcriptional contributions to dilp8 regulation. In addition, we have performed a new experiment to check the post-transcriptional regulation of dilp8, in response to tissue damage. Though the change in the dilp8-3′UTR GFP reporter upon RicinA expression in the ptc domain of the wingdisc is mild (Figs. S6F-G’), this strongly suggests a post-transcriptional outcome of the reduction of miR-184 levels on dilp8. Hence, we propose that tissue damage induces strong transcriptional activation of dilp8, while the reduction of miR-184, despite its smaller magnitude, contributes to dilp8 upregulation via post-transcriptional regulation. In support of this, our experiments demonstrate direct regulation of the dilp8-3′UTR by miR-184 (Figs. 4C-F’), and show strong dilp8 mRNA upregulation in miR-184 deficient conditions (Fig. 4A and B), suggesting the role of miR-184 in maintaining dilp8 levels. We also show that RicinA induced effects on dilp8 and pupariation delay are reversed by co-expression of miR-184 (Fig. 5C). We do not claim that regulation by miR-184 is the sole mechanism for driving dilp8 induction during tissue damage, but suggest that miR-184-mediated post-transcriptional regulation acts in a complementary manner to transcriptional responses. Furthermore, we believe that the mild effect of JNK signaling on miR-184 (as shown by the bskDN experiment) is sufficient for the moderate reduction of miR-184 in response to tissue damage.

Comment 3: ____Regarding the expression levels, it does not help that the authors show bar graphs with standard errors of the mean instead of the actual data points to allow reliable appreciation of the data dispersion.

Response: We have modified our figures and have performed statistical analysis according to the suggestions of the reviewers, please see responses to comments 1-9, and 13-19.

Comment 4: It is difficult to understand how minute changes in miR-184 levels can lead to over an order of magnitude differences (in some cases) in dilp8 mRNA levels considering that it is a stoichiometric relationship. Maybe ?miR-184-Dicer1? complexes are highly stable and re-used for multiple dilp8 transcripts - the authors could discuss how they understand this occurring in their manuscript.

On the same line, discussion is also rather weak on what regards the mechanism of control of dilp8 mRNA levels by miR-184. Please discuss eg, the evidence for mRNA degradation induction by microRNAs with this UTR binding profile (imperfect UTR binding Fig S4) and-if appropriate-how other possible regulatory models (direct and indirect) could explain the findings.

Response: We accept the reviewers comment that 25-30% reduction of miR-184 is low in comparison to the many fold increase in dilp8 levels. We believe that both post-transcriptional and transcriptional changes are responsible for the induction of dilp8 in response to tissue damage. However, our experiments suggest the role of post-transcriptional regulation by miR-184, as pupariation delay is rescued by miR-184 overexpression (also please see the response to the previous comment). We are not ruling out the possibility of transcriptional regulation of dilp8 mRNA, rather we are suggesting the possibility that both transcriptional and post-transcriptional means are responsible for changes in dilp8. Moreover, we have not performed absolute measurement of miR-184 in the imaginal discs (what we show is a comparison between control and RicinA expression), hence we do not have an exact estimate of how many miR-184 molecules are reduced and if they would be greatly equal or more in comparison to the dilp8 mRNA molecules that are upregulated, as again while measuring dilp8 mRNA we are not checking how many molecules of dilp8 exactly are increased. As the reviewer suggests, it is possible that miR-184-RISC could be stable to handle multiple dilp8 molecules one after the other, hence it is not a 1:1 relationship between miR-184:dilp8. We have included this in the manuscript. It is also known that imperfect 3’UTR binding as seen in most animal microRNAs leads to translational repression and mRNA deadenylation, which eventually results in mRNA degradation.

Comment 5: ____We suggest the authors carefully revise their citations to cite appropriate work that supports the claims, and also to avoid missing the seminal studies that report the claims they cite.

Response: We are really apologetic for the errors citing the key references. We are grateful to the reviewers for correcting this for us. We have made changes to the text to include and correct the references.

We have the suggestions below which we hope will help the authors improve their manuscript. If the authors address these points raised above, we believe the manuscript should be a valuable contribution to the field, and help in the understanding of how tissues respond to growth aberrations and the regulation of transcript levels by microRNAs.

Detailed Comments:

Comment 1. Results 1st paragraph: please describe the screen in more detail. As written, one only discovers it was a miRNA loss-of-function screen when reading the legend of Table S1. Please show the original data of the screen - with dispersion if possible.

Response: We thank the reviewers for these suggestions, we have now included the data from the screen with SEM, and p-values.

Comment 2. Results 1st paragraph, Fourth line, "While several miRNAs caused delays in pupariation by 12 hours or more..". Please correct, as actually loss of miRNAs caused delays.

Response: We thank the reviewer for pointing out this error, we have corrected the text accordingly.

Comment 3. ____Results (Figure 1) - It says that data from three independent experiments are shown. However there is no dispersion in the data. Could the authors please explain this? Are the results of the three experiments summed and presented as one? or is this one of the three?

Response: We thank the reviewers for these suggestions and have plotted data with the SEM values.

Comment 4. It is reported in the legend of Figure S2 that LogRank test was performed to determine statistical significance. However, no statistical data is presented. Please show the results.

__Response: __We thank the reviewers for these suggestions to improve the data presentation, we have incorporated the p-value as suggested.

Comment 5. Fig2A and B. Please show the data points in the bar graphs (as in Figure. 2C), or choose another data representation. ____Please consider redoing statistical analysis with a simple t-test. ____It is not clear to me why ANOVA was used to compare two samples. Please state that data are normalized also to control (tub-GAL4>UAS-scramble). Please ____state____ the h post-hatching from which the RNA samples were collected (as in Fig 2C for 20HE quantification).

__Response: __We thank the reviewers for these suggestions to improve the data presentation, we have incorporated all changes as suggested. Similar changes have been incorporated to the rest of the figures of the manuscript as well. Hours post-hatching information for each figure is now added to the figure legends. __ __

Comment 6. Fig2C. Fig legend states the bar graphs are "absolute values". Please specify if the bar represents the average, median or something else.

Response: We thank the reviewer for pointing this out, we have made the suggested changes.

Comment 7. Throughout the manuscript: please use GAL4 in capital letters or at least standardize it throughout the ms. Currently there are GAL4s and Gal4s.. eg compare Fig 2 and 3 legends.

Response: We thank the reviewer for pointing this out, we have incorporated all changes as recommended.

Comment 8. FigS3A and B. Please revise as Fig2A and B above. and apply the same criteria in the respective figure legend.

__Response: __We thank the reviewer for pointing this out, we have made the changes as recommended.

Comment 9. Fig. 4 - please indicate on the figures what is whole larvae and what is wing imaginal discs. This will facilitate understanding of the figure.

__Response: __We thank the reviewers for these suggestions and have included this information in all the figures.

Comment 10. Fig 4 - Data - Authors do not show that rn-GAL4>miR-184-sponge causes up regulation of dilp8 mRNA levels, hence the model is weakened. Doing this experiment would significantly strengthen the study whatever the result is.

Response: We thank the reviewer for pointing this out and we have included this in the manuscript (Fig S5B).

Comment 11. The dilp8-3'UTR experiment is weak especially because its generation is not sufficiently well described in the manuscript. "The dilp8 3'UTR-GFP reporter line was created as described in (Vargheese & Cohen, 2007)" is not sufficient. Please describe the construct generation in sufficient detail so that the experiments can be reproduced by others.

Response: We thank the reviewer for pointing this out and we have elaborated in the methods section on how we generated the dilp8 3'UTR-GFP reporter and dilp8 3'UTR mutant GFP reporter lines. The plasmid was originally created in Steve Cohen’s lab at EMBL, by modifying pCasper4 plasmid, by introducing a tubulin promoter, EGFP and a multiple cloning site, which allows one to clone 3’UTRs of target genes into this plasmid. Not1 and Xho1 sites were used to clone the dilp8-3’UTR and mut-3’UTR. We hope this explains our strategy sufficiently.

Comment 12. Making assumptions, if the construct is as described in Vargheese & Cohen, 2007 and contains all of the dilp8 3'UTR - it should be a Tubulin-driven GFP gene with a dilp8-3'UTR "Tub-GFP-(dilp8 3'UTR)". In this case the authors need to rule out the alternative interpretation of the result in Fig. 4D by showing that the expression of miR-184 does not down regulate Tub-GFP expression itself. The best scenario would be to have a mutated dilp8 3'UTR for the miR-184 recognition site. This experiment would significantly strengthen the study and model.

Response: We thank the reviewer for pointing this out. We agree with the reviewers that this experiment is needed to prove direct regulation of the dilp8-3’UTR by miR-184. We have mutated the sequences complementary to the seed region of miR-184 in the dilp8-3’UTR, and demonstrated that overexpression of miR-184 does not regulate the mutated tub-GFP-(dilp8 3'UTR) expression. This confirms that the dilp8 gene is a direct target of miR-184. This data is added to the manuscript as Figs 4E-F’.

Comment 13. Figure 4C-D please separate dilp8 from 3'UTR with a space or hyphen.

Response: We thank the reviewer for pointing this out and have separated dilp8 from 3’UTR with a hyphen.

Comment 14. Figure 4E. Please name the dilp8 allele as MI00727 as it is not a KO, but rather a hypomorphic mutation (fully WT dilp8 transcripts are still generated, albeit at a much lower level).

Response: We thank the reviewer for pointing this out and we have made the necessary changes.

Comment ____15. Figure 6D: please add UAS to bskDN/+. All figures have rn-GAL4 alone or with UAS-GFP as control. This finding would be strengthened with this other control, especially because the size effect is small.____ This being said a general comment for all experiments is that hemi-controls are generally missing for all figures. eg, in Fig 3. One would typically include controls such as A. Phm>+ and +>miR.184; B. aug21>+ and +>miR.184; C. ptth>+ and +>miR.184; D. rn>+ and +>miR.184

Response: We thank the reviewer for pointing this out. We have added UAS to bskDN, now Fig 5D and have also added the rnGAL4/+ control. We have also performed various hemi-control experiments as suggested by the reviewer to our best capabilities. We have added a separate graph with the hemicontrols in the as a Reviewer Response Figure 1.

Comment 16. Figure 7: Are IPCs necessary for the model? If not, I suggest removing them and placing the Lgr3 neuron cell bodies much more anterior in this scheme. Their cell bodies are as anterior and rostral as it gets, approximately where the IPCs are depicted in this type of view of the CNS.

Response: We thank the reviewer for pointing this out and have removed IPCs from the figure, this figure is now labelled as Fig. 6.

Comment ____17. Table S1- It would be preferable to see the data of these experiments, but if the authors prefer to show this data in a table, please at least add the dispersion analyses (eg standard deviation.. OR median+-quartiles OR Confidence intervals..), N of animals analysed, and statistics against controls.

Response: We thank the reviewer for pointing this out, we have added the number of larvae analysed, SEM values and statistics against the control condition.

Comment ____18. In all figures with pupariation time: please also indicate significant findings in the graphs (with an asterisk, for instance) and adjust figure legends accordingly. This could facilitate understanding the data.

__Response: __Thanks for the suggestion. We have incorporated this information into figure legends.

Comment ____19. Please revise Figure legends for punctuation.

__Response: __We have rectified all the errors in punctuation. We thank the reviewers for suggesting this.

__Comment ____20. __

a) Abstract:

Line 10: What is the evidence to call Dilp8 a "paracrine" factor?

Response: We thank the reviewer for pointing this out, we have changed the text to ‘secreted factor’.

b) Introduction:

4th paragraph, 3rd sentence " Dilp8... buffers developmental noise and delays pupariation..." Buffering of developmental noise was first shown in Garelli et al., Science 2012, so this publication should be cited. ____4th paragraph, 5th sentence: please include Jaszczak et al., Genetics 2016. This paper was published together with the 2015 papers, just a matter of timing that it got a 2016 date. Moreover, I do not think Katsuyama et al., 2015 is well cited to back up the statement in this sentence, hence I recommend removing that citation in this sentence.

Response: We thank the reviewer for pointing this out and have made necessary changes.

c) 6th paragraph: 5th line "targeting dilp8" : please specify if you mean the gene or the mRNA, or both. Same for line 7.

Response: We thank the reviewer for pointing this out and have made necessary changes.

d) Results Page 10, 1st paragraph, 1st sentence: the works cited are not the appropriate studies that demonstrated what is being stated. This was shown in Garelli et al., Science 2012 and Colombani et al., Science 2012. Results Page 10, 1st paragraph, line 11: Please also cite Colombani et al., Science 2012, who first showed that JNK is required for dilp8 regulation.

Response: We thank the reviewer for pointing this out and are extremely apologetic for this oversight. We have made necessary changes to the manuscript.

e) Discussion, 2nd paragraph, line 4: again, please indicate the rationale for using "paracrine" to describe Dilp8's activities. The current widely accepted model is that Dilp8 acts on interneurons in the brain ____(eg, reviewed in Juarez-Carreno et al., Cell Stress, 2018; Gontijo and Garelli, Mech Dev, 2018; Mirth and Shingleton, Front Cell Dev Biol, 2019; Texada et al., Genetics 2020; Boulan and Leopold, 2021).____ In order to reach the brain, Dilp8 has to be secreted from the discs and travel to the brain. This is as an endocrine mechanism as it gets for a small larva, considering that some discs can be on the opposite side of the larva (eg, genital discs). While this does not exclude that Dilp8 could also act paracrinally, the only evidence that I am aware of comes from other contexts such as during transdetermination (where Dilp8 has been proposed to work in an autocrine or paracrine fashion, via Drl in imaginal discs (Nemoto et al., Genes to Cells, 2023), however, this is not cited appropriately in this manuscript and is less related to the Lgr3-dependent pathway being studied here.

Response: We totally agree with the reviewer and appreciate clarifying this for us. We have made necessary changes to the text.

f) Discussion Page 13, 1st paragraph, This claim is supported by data presented in Garelli et al., Science 2012, not the other two papers. Garelli et al., 2015 shows that the Lgr3 receptor also participates in buffering developmental noise. Other studies have corroborated the Garelli et al., 2012 finding: eg, Colombani et al., Curr Biol 2015; Boone et al., Nat Commun 2016; Blanco-Obregon et al., Nat Commun 2022). Many other studies have shown that Dilp8 promotes developmental stability under tissue stress and challenges.

Discussion Page 12, 3rd paragraph, 2nd sentence: "The Lgr3 neurons directly interact with ... PTTH ...and insulin-producing neurons" Please cite Colombani et al., 2015 and Vallejo et al., Science 2015. Vallejo et al., propose that circuit with insulin-producing neurons. In the 3rd sentence, only Jaszczak et al., 2016 is cited, whereas this claim/model comes from many studies, such as Halme et al., Curr Biol, 2010; Hackney et al., PLoS One 2012; Garelli et al. Science 2012; Colombani et al., Science, 2012; and the Lgr3 papers from 2015). Jaszczak et al., actually propose that Lgr3 is also required in the ring gland in addition to neurons.

Discussion page 14 last paragraph,10 line, "In Aedes aegypti ....regulates ilp8 (Ling et al., 2017)". As far as I understand mosquitoes do not have a dilp8 orthologue (see for instance Gontijo and Gontijo, Mech Dev 2018; and Jan Veenstra's work). ilp nomenclature (numbering) does not follow that of Drosophila, so ilp8 is probably a typical Insulin/IGF-like peptide and is NOT an orthologue of Dilp8, a relaxin, so this citation needs to be removed or placed into the broader context of microRNA regulation of ilps.

Response: We are really sorry for the numerous glaring errors in the references. We thank the reviewers for correcting this for us. We have made necessary changes to the text.

Thank you for the opportunity to review your interesting work,

Alisson Gontijo and Rebeca Zanini

Reviewer #3 (Significance (Required)):

If the authors address these points raised above, we believe the manuscript should be a valuable contribution to the field, and help in the understanding of how tissues respond to growth aberrations and the regulation of transcript levels by microRNAs.

__Author’s concluding response: __

We thank all the reviewers for the overall positive comments and suggestions that we believe have helped us to improve our manuscript. We have incorporated all the changes suggested, especially regarding errors in citing key references. We have performed most of the experimental suggestions. Also, we have modified the way in which graphs are presented, including statistical tests as suggested by the reviewers. Several controls have been performed to strengthen the manuscript further. We believe that this review process aided in significantly improving this manuscript.

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

1. General Statements

We thank the reviewer for their positive comments regarding the research article titled "The Ketogenic Diet Metabolite 1 β-Hydroxybutyrate Promotes Mitochondrial Elongation via Deacetylation and Improves Autism-like Behaviour in Zebrafish" by Uddin GM and colleagues. We appreciate your input, and we will address these comments as indicated below with specific responses to each point raised by reviewers.

The main changes in the updated manuscript are as follows:

We have revised the introduction to now incorporate additional background information on mitochondria, NAD, and mitochondrial dynamics and function. This addition aims to provide readers with a broader understanding of the mitochondrial context in relation to our study.

Furthermore, we recognize that previous studies have explored mitochondrial function in the context of the ketogenic diet. While our specific investigation centered on mitochondrial morphology, we acknowledge the importance of comprehensively investigating mitochondrial function. To this end, we have added new data showing how BHB impacts mitochondrial oxidative phosphorylation in HeLa cells (Sup Fig 2), and how both BHB and NMN impact oxygen consumption/glycolysis in zebrafish (Fig 7).

We have also added new behaviour analysis of the zebrafish (Fig 6), and have re-framed the discussion around neurodevelopment generally, rather than ASD specifically.

Finally, we have now included a section in our manuscript that discusses the limitations of our study. These limitations can be further investigated to explore and characterize the full mechanistic potential behind the effects of the ketogenic diet and/or NMN on mitochondrial dynamics.

2. Point-by-point description of the revisions

This section is mandatory. *Please insert a point-by-point reply describing the revisions that were already carried out and included in the transferred manuscript. *

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

Uddin GM and colleagues presented a research article entitled 'The Ketogenic Diet Metabolite 1 β-Hydroxybutyrate Promotes Mitochondrial Elongation via Deacetylation and Improves Autism-like Behaviour in Zebrafish'. Roles of ketogenic diet (KD) and NAD+ precursors in health promotion and longevity, as well as on the alleviation of a broad range of diseases are evident. However, their roles in autism are not well done, which is the novelty of the current study. Addressing below questions will improve the quality of the paper.

Major concerns 1. In the introduction section, a broad overview of the roles of ketogenic diet (KD) in neurodegenerative disease (and ageing, if possible) should be provided. E.g., the authors should summarize exciting progress on the use of KD to treat Alzheimer's disease in animal models (PMID: 23276384). *

Response: Thank you for your valuable suggestion. While it is true that the KD appears to be beneficial in neurodegenerative (and other disease) models, our focus in this paper is looking at neurodevelopment, rather than all potential benefits of the KD. Nonetheless, we have addressed this comment by incorporating a brief overview of the roles of the KD in neurodegenerative diseases, including Alzheimer's disease (AD), in the introduction section of the manuscript. Specifically, we have summarized the exciting progress made in utilizing KD to treat AD in animal models, as highlighted in the suggested study. This addition helps to provide a better overview of the potential therapeutic effects of KD in neurodegenerative diseases and strengthens the introduction section of the manuscript.

• Roles of high fat diet to treat diseases could be extended to rare premature ageing diseases. In such scenario, high fat and NAD+ boosting shared some joint mechanisms (PMID: 25440059 ). *

Response: This information and the reference are now added to the discussion.

*In the introduction, a more detailed introduction of NAD+ and its roles in mitochondrial homeostasis (especially mitophagy and the mitochondrial fusion-fission balance) should be included (PMID: 24813611; PMID: 30742114; PMID: 31577933). *

Response: Although our paper focused primarily on mitochondrial fission and fusion, we have incorporated a new paragraph in the introduction to provide a more detailed introduction detailing NAD+ and its roles in mitochondrial homeostasis, specifically highlighting mitophagy. We have included the suggested references.

• In regarding to the statement of KD increases NAD+, was it due to increased generation (to check protein levels and activities of different NAD+ synthetic enzymes, such as iNAMPT, NMNAT1-3, and NRK) and/or reduced consumption (in addition to reduced glycolysis, does KD inhibit the activities of CD38 and PARPs? In this paper, Sirtuins' activities is (are increased)). Detailed exploration of the activities of these proteins will unveil a clear molecular mechanisms on how KD affects/regulates NAD+. *

Response: Thank you for the comment. We agree that exploring the detailed mechanism of how the ketogenic diet (KD) affects NAD+ is an interesting question that will have important implications once answered. However, fully elucidating the mechanism of action would require a more comprehensive investigation, which is beyond the scope of this current project. We have now added this as a future direction in the manuscript.

*Fig. 1: in the NAD+ field, the normal used NR/NMN concentrations are normally high like to use 500 µM to 2-5 mM (as the NAD+ levels in cells are high). In addition to use 50 µM, the authors are strongly to have a dose-dependent study (50 µM, 500µM, 1, 2, 5 mM), and see changes of mitochondrial funciton and parameters. In this condition, NAD+ levels should be also checked. *

Response: We have added new supplemental data showing the initial dose response of the effects of BHB and NMN on mitochondrial morphology, which led us to choosing the relevant doses for the remainder of the paper. Our objective was not to investigate the broad impacts of different NMN concentrations on mitochondrial function and parameters, or NAD+ levels. As such, we have only focused on doses where we see effects on mitochondrial morphology.

*Fig. 2: a comprehensive characterization of mitochondrial fusion-fission should be performed. In addition to the protein evaluated, changes on other key fusion-fission proteins, like Bax, Bak, Mfn-1, Mfn-2, etc should be performed (PMID: 17035996; PMID: 24813611). *

Response: We agree that looking at other key proteins involved in mediating mitochondrial fission and fusion could provide additional insight. Indeed, given the changes in global acetylation that we see, it is expected that some other proteins may also be regulated in this way. However, there are at least a dozen proteins involved in mediating mitochondrial fusion and fission, not to mention many more proteins that regulate these proteins. Unfortunately, it is not feasible to analyze all the proteins involved in mitochondrial fusion-fission. Moreover, looking only at protein levels, doesn't necessarily inform about the activity of any protein. Instead, we concentrated in this paper on investigating known links between protein acetylation and mitochondrial dynamics, particularly focusing on the proteins that have known links to acetylation (i.e., DRP1, OPA1, MFNs). We have added a note in the discussion acknowledging that other means of regulation could also be occurring in parallel.

*Figs. 1-5 were focused on mitochondrial morphology, whether KD and NMN changed mitochondrial funciton should be explored, such as to use seahorse to check ECR and OCR. *

Response: Although our question was focused on morphology, we agree that mitochondrial function is important. We have added new data showing that BHB increases basal oxygen consumption in HeLa cells (Sup Fig 2), as well as new data showing that BHB and NMN influence oxygen consumption and glycolysis in our zebrafish model (Fig 7)

• Fig. 6: NR/NMN used in animal studies (via gavage or in drinking water in mice, and on plate for worms and flies) are normally high (e.g., in drinking water for mice could be 4-12 mM; for worms and flies are normally 1-5 mM); for zebrafish, while they are swimming in water, this reviewer concerned whether it was true that 50 µM of NMN was sufficient to show the benefit presented.*

Response: Our data show that these doses are indeed sufficient. We did look at some higher doses for NMN, but these were toxic, leading to poor survival and were not studied further.

*Minor concerns 1. Line 26: For 'a growing list of neurological disorders, including autism spectrum disorder (ASD)', please add AD in. *

Response: Line 26 is part of the abstract, which we feel should be focused more on the main message of the paper, which does not involve AD. As addressed above, we have added AD as an example in the introduction.

*Line 57: For 'with side effects such as gastrointestinal disturbances, nausea/vomiting, diarrhea, constipation, and hypertriglyceridemia being reported', rate of frequency shall be provided if any. *

Response: We have modified the statement to indicate the relative percent of patients suffering the various side effects.

*Reviewer #1 (Significance (Required)):

The novelty of the current study was to investigate effects of KD and NAD+ on autism. This investigation was not performed before and thus is the novelty.

Weakness, effects of KD and NAD+/NMN on mitochondrial function were not well-investigated and should be done. Introduction was not well done, many key information in the fields were not provided which may mislead the readers an over-evaluation of the novelty of the current study.*

Response: As outlined above, we have edited the introduction to include additional information requested by the reviewer. Moreover, our focus in this manuscript was to look at the mechanisms underlying changes in mitochondrial morphology, not mitochondrial function per se, though this is clearly important and related. Nonetheless, as discussed above, we have also added new data showing how BHB impacts mitochondrial function.

*My expertise lies in NAD+, mitochondria, and brain health.

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

The study examined the effect of beta-hydroxybutyrate and nicotinamide nucleotide on mitochondrial morphology and the molecular pathways which mitigate this effect as well as the effect of these treatments on behavior in zebrafish. The study is well done and well written. The only thing I think that could be improved are the bar in the graph some the significant comparisons. It is sometimes difficult to see which groups are being compared.*

Response: We're happy to adjust how the data is displayed in the relevant bar graphs, but it is not clear exactly what changes the reviewer would like. To some degree this will depend on the specific guideline of the final journal where we hope the manuscript will be published. As such, we have not made changes at this point.

***Referees cross-commenting**

The other reviewers do have some fair comments. Multiple doses would be helpful and showing bioenergetic data would complement the morphological measurements. Additionally, behavioral assays showing changes in social behavior in the Zebrafish would provide a stronger link to ASD. *

Response: As discussed above, we have added new information on doses and mitochondrial bioenergetics. With respect to behaviour, we have added thigmotaxis data and reworked the discussion around behaviour and neurodevelopment so that it is less specific to ASD.

*Reviewer #2 (Significance (Required)):

As beta-hydroxybutyrate is an important substrate for the ketogenic diet, this study helps explain the potential mechanisms in which the ketogenic diet may enhance mitochondrial function.

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

In this paper, Uddin and colleagues have investigated components of the ketogenic diet to understand changes in both mitochondrial morphology and protein expression, and zebrafish locomotor behaviour. They investigate whether beta-hydroxybutyrate (BHB) or nicotinamide nucleotide (NMN) application can later human mitochondria in HeLA cell lines, and also recue a locomotion defect in shank3b+/- zebrafish larvae that have previously been proposed as a model for autism. This study is strengthened by showing data from two species; however the link between the HeLA cell line data and larval zebrafish is not strong. The study would be improved by assessing zebrafish mitochondrial changes after drug application, and testing more than one concentration of BH and NMN in the behavioural assay. This is an interesting study, and it is nicely written and presented. I have made some comments to strengthen the study below.

Major comments My expertise is in modelling some aspects of autism in zebrafish. To this end I have focussed on the zebrafish part of this manuscript more fully. I have several comments related to the zebrafish experiments. 1. The changes in mitochondrial morphology, peroxisome number and mitochondrial protein levels were measured in HeLA cells and not comparable data is shown for zebrafish. The same experiments should be repeated using larval zebrafish or a zebrafish cell line. *

Response: We chose to use HeLa cells for the mechanistic studies due to practical reasons. Cell lines offer a controlled and well-established system for investigating cellular processes and molecular mechanisms. Measuring these parameters in tissues is significantly more challenging and requires different reagents (e.g., antibodies) and methodology (electron microscopy) that are not feasible in the current study.

On the other hand, zebrafish larvae were employed for the behavior studies, which cannot be conducted using cell lines. By utilizing zebrafish, we were able to examine the effects of beta-hydroxybutyrate (BHB) and nicotinamide nucleotide (NMN) on locomotor behavior, providing valuable insights into potential therapeutic implications for autism.

While we acknowledge the limitations of not directly measuring mitochondrial morphology, peroxisome number, and mitochondrial protein levels in zebrafish, we believe that our study provides significant contributions to understanding the effects of BHB and NMN in zebrafish behavior. Future studies could certainly consider incorporating zebrafish-specific experiments to complement the findings in HeLa cells.

• How did you choose the concentration of BHB and NMN to use in behavioural experiments? And the timing of application - I don't really understand why you waited 3 days after drug application to measure locomotion. *

Response: These doses chosen initially as they were similar the doses that induced mitochondrial elongation in HeLa cells and were tolerated by the fish larvae. As we saw promising effects at these initial doses, we decided to explore them in more detail. While we agree that it would be worth comparing the effects of additional doses, as well as looking at their effects at other timepoints, such work would be a major endeavour and is beyond the scope of our initial investigations, which we feel are worth reporting in their current state.

With respect to the treatment paradigm, fish larvae were treated 10-48 hours post fertilization, as this is a critical neurogenic developmental timepoint that is often used for exposure studies. Fish do not fully hatch until 3-4 days post fertilization, and display only minimal movement before 5 days, which is why we waited until 5 days to look at movement.

• Do the shank3b+/- larvae show any morphological deficits? Their decrease in locomotion is striking. Is the morphology also rescued by drug application? Can you tie this to the mitochondrial changes that you observed in HeLA cells?*

Response: We do not observe any gross changes in fish morphology that might explain a decrease in locomotion. Unfortunately, it is not feasible to look at mitochondrial morphology in the fish at this time. However, based on previous published work showing that the ketogenic diet promotes mitochondrial elongation in mouse brains (PMID:32380723), we would expect mitochondrial morphology also to be changed in the fish. Nonetheless, as we have not examined this directly in fish, we are not making this specific claim in this manuscript.

• In figure 6A you use time spent swimming as a readout of distance. This doesn't really make sense, because without also showing speed of swimming it is not possible to know whether time and distance correlate in the same way across genotypes. This figure could be improved by showing more detail - speed of swimming, time spent immobile etc. This can easily be extracted from the films that you have already made using the ViewPoint software. *

Response: As requested, we have reanalyzed the zebrafish movement data for a more refined analysis. In the revised version (Fig 6), we include analysis of both speed and distance travelled within a defined time. Importantly, these findings still support differences between WT and shank3b+/- fish that are restored by BHB and NMN to varying degrees.

• Showing a change in locomotion is not enough to claim that a model is autism-like. At a minimum I think that you need to show changes in social behaviour - likely using older fish (more than three weeks) that interact with each other. Changes in locomotion can be caused by so many factors, many of which are not indicative of autism. It is important that as a field we do not simply claim that locomotion can be used as a proxy for more complex disease phenotypes. This recent review may help you with this point:* https://www.frontiersin.org/articles/10.3389/fnmol.2020.575575/full.

Response: The reviewer makes an important point that the movement behaviour phenotypes that we see do not necessarily represent classic ASD phenotypes (i.e., repetitive behaviour, reduced sociability, and reduced communication). To begin to address this issue, we analyzed thigmotaxis, which can be a measure of anxiety. Notably, we also see differences that are reversed by BHB and NMN. However, we cannot model all ASD behaviours in a fish model, and we are not set up to look at social behaviour, especially in the young fish that we were studying. As such, even though Shank3 is a recognized ASD gene, and the shank3b+/- model we are studying is a validated ASD model (PMID: 29619162), we have re-phrased the manuscript in the context of neurodevelopment generally, rather than with respect to ASD specifically. As such, we ascribe the movement and thigmotaxis phenotypes as neurodevelopmental phenotypes that are improved by BHB and NMN.

*For the statistics, as far as I can tell, all of the data should be analysed by ANOVA or the non-parametric equivalent followed by a post-hoc test. Please check this and add information about normality in. *

Response: As requested, we have clarified our statistical methodology throughout the manuscript.

For the mechanistic data, we used t-tests for direct comparisons between two groups (e.g., vehicle vs. treatment). While multiple conditions such as vehicles, NMN, BHB, or etomoxir were tested, statistical comparisons were only conducted comparisons between the vehicle and each treatment group individually. As we are not also making comparisons between treatments this is not a multiple comparison, and ANOVA is not applicable in this context. We have clarified this rationale in the manuscript to avoid any confusion.

For the zebrafish study, where multiple factors were involved (e.g., treatments across different time points or conditions), we performed a two-way ANOVA followed by Tukey's post-hoc test to identify specific group differences. This approach was appropriate for analyzing these datasets and ensures robust conclusion.

With respect to normality testing, all datasets were assessed for normality using the Shapiro-Wilk test, and no violations of normality were observed. The updated text now includes these details.

*Minor comments

1. Make sure that you refer to the fish line as shank3b+/- throughout - see abstract.*

This has bee corrected.

• Please add a space between all numbers and units (e.g. 5 Mm). *

This has bee corrected.

• There is a spelling error on line 340 page 16: finings instead of findings. *

This has bee corrected.

• In figure 1, if each dot represents a different sample, then there appear to be many fewer samples analysed in 1D compared to 1B. Can you comment upon this please*

__Response: __A total of 80-150 cells were counted per condition, and the analyses were performed on 3 independent replicates with 2 independent technical replicates for each treatment condition. The quantification of mean mitochondrial branch length in Figure 1B was measured using Image-J and the MiNA plugin. The measurements were taken from three independent replicates using a standard region of interest (ROI) and randomly selected areas from each image.

In Figure 1D, NAD+ levels were measured 24 hours after treatment of vehicle, βHB, NMN, or Eto+βHB in HeLa cells (n=3-6/group). Each sample lysate represents an independent experimental dish from which coverslips were collected for image analysis.

The difference in sample numbers between Figure 1B and 1D arises because image analysis involves individual cells fixed and stained on coverslips, whereas the NAD assay requires the whole lysate from the entire cell culture dish. Therefore, the higher cell count in Figure 1B represents the number of cells analyzed on coverslips, while Figure 1D represents NAD levels from the lysate normalized to the protein concentration.

*Reviewer #3 (Significance (Required)):

I think that this will be interesting to autism researchers and it could lead to more investigation of the ketogenic diet. Some more work is needed, likely in other model organisms, before this research can be translated to human patients. *

__Response: __We agree that the findings of our study could be of interest to autism researchers and have implications for further investigation of the ketogenic diet (KD). It is important to note that further work, including studies in other model organisms, would be beneficial before translating this research to human patients.

Our study aimed to provide mechanistic insights into the effects of the KD on mitochondrial morphology and behavior. We recognize that the translation of research findings to human patients requires rigorous investigation, including preclinical and clinical studies. Our study contributes to the understanding of the underlying mechanisms involved in the KD's effects, laying the groundwork for future research and potential therapeutic avenues.

We appreciate your perspective and emphasize that our intention is to provide valuable insights into the mechanisms underlying the KD's effects rather than suggesting immediate translation to human patients. Further investigation and validation in diverse models and clinical settings will be necessary before considering clinical applications.

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

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Referee #3

Evidence, reproducibility and clarity

In this paper, Uddin and colleagues have investigated components of the ketogenic diet to understand changes in both mitochondrial morphology and protein expression, and zebrafish locomotor behaviour. They investigate whether beta-hydroxybutyrate (BHB) or nicotinamide nucleotide (NMN) application can later human mitochondria in HeLA cell lines, and also recue a locomotion defect in shank3b+/- zebrafish larvae that have previously been proposed as a model for autism. This study is strengthened by showing data from two species; however the link between the HeLA cell line data and larval zebrafish is not strong. The study would be improved by assessing zebrafish mitochondrial changes after drug application, and testing more than one concentration of BH and NMN in the behavioural assay.

This is an interesting study, and it is nicely written and presented. I have made some comments to strengthen the study below.

Major comments

My expertise is in modelling some aspects of autism in zebrafish. To this end I have focussed on the zebrafish part of this manuscript more fully. I have several comments related to the zebrafish experiments.

1. The changes in mitochondrial morphology, peroxisome number and mitochondrial protein levels were measured in HeLA cells and not comparable data is shown for zebrafish. The same experiments should be repeated using larval zebrafish or a zebrafish cell line.
2. How did you choose the concentration of BHB and NMN to use in behavioural experiments? And the timing of application - I don't really understand why you waited 3 days after drug application to measure locomotion.
3. Do the shank3b+/- larvae show any morphological deficits? Their decrease in locomotion is striking. Is the morphology also rescued by drug application? Can you tie this to the mitochondrial changes that you observed in HeLA cells?
4. In figure 6A you use time spent swimming as a readout of distance. This doesn't really make sense, because without also showing speed of swimming it is not possible to know whether time and distance correlate in the same way across genotypes. This figure could be improved by showing more detail - speed of swimming, time spent immobile etc. This can easily be extracted from the films that you have already made using the ViewPoint software.
5. Showing a change in locomotion is not enough to claim that a model is autism-like. At a minimum I think that you need to show changes in social behaviour - likely using older fish (more than three weeks) that interact with each other. Changes in locomotion can be caused by so many factors, many of which are not indicative of autism. It is important that as a field we do not simply claim that locomotion can be used as a proxy for more complex disease phenotypes. This recent review may help you with this point: https://www.frontiersin.org/articles/10.3389/fnmol.2020.575575/full.
6. For the statistics, as far as I can tell, all of the data should be analysed by ANOVA or the non-parametric equivalent followed by a post-hoc test. Please check this and add information about normality in.

Minor comments

1. Make sure that you refer to the fish line as shank3b+/- throughout - see abstract.
2. Please add a space between all numbers and units (e.g. 5 Mm).
3. There is a spelling error on line 340 page 16: finings instead of findings.
4. In figure 1, if each dot represents a different sample, then there appear to be many fewer samples analysed in 1D compared to 1B. Can you comment upon this please?

Significance

I think that this will be interesting to autism researchers and it could lead to more investigation of the ketogenic diet. Some more work is needed, likely in other model organisms, before this research can be translated to human patients.

Author response:

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

Reviewer #1 (Public Review)

The weaknesses are in the clarity and resolution of the data that forms the basis of the model. In addition to whole embryo morphology that is used as evidence for convergent extension (CE) defects, two forms of data are presented, co-expression and IP, as well as a strong reliance on IF of exogenously expressed proteins. Thus, it is critical that both forms of evidence be very strong and clear, and this is where there are deficiencies; 1) For vast majority of experiments general morphology and LWR was used as evidence of effects on convergent extension movements rather than Keller explants or actual cell movements in the embryo. 2) The study would benefit from high or super resolution microscopy, since in many cases the differences in protein localization are not very pronounced. 3) The IP and Western analysis data often show subtle differences, and not apparent in some cases. 4) It is not clear how many biological repeats were performed or how and whether statistical analyses were performed. 

(1) To more objectively assess the convergent extension phenotypes, we developed a Fiji macro to automatically quantify the LWR in various injected Xenopus embryos, as detailed in the Methods section. We acknowledge that a limitation in the current manuscript is how to link our mechanistic model at the molecular level with the actual cellular behavior during convergent extension, and we plan to perform cell biological studies in the future to elucidate the link;

(2) We have repeated some of the imaging experiments in DMZ explants using a Zeiss LSM 900 confocal equipped with Airyscan2 detector that can increase the resolution to ~100 nm. The new data are in Suppl. Fig. 4, 9, 11, 16;

(3) We have repeated all IP and western blots at least three times and provided quantification and statistical analyses;

(4) We have added the information on biological repeats and statistical analyses in all figures and figure legends.

Reviewer #2 (Public Review):

The protein localization experiments in animal cap assays are for the most part convincing, but with the caveat that the authors assume that the proteins are acting within the same cell. As Fzd and Vangl2 are thought to localize to opposite cell ends in many contexts, can the authors be sure that the effects they observe are not due to trans interactions? 

In our previous publication, we provided evidence that Vangl is necessary and sufficient to recruit Dvl to the plasma membrane within the same cell (Figure 3 in 10.1093/hmg/ddx095). In a more recent publication ( 10.1038/s41467-025-57658-0 ), we further elucidated a mechanism through which Dvl oligomerization switches its binding from Vangl to Fz, and determined that Dvl binding to Vangl and Fz are differentially mediated by its PDZ and DEP domain, respectively. In the current manuscript, we also performed co-IP experiment under various conditions to demonstrate binding between Dvl and Vangl. We feel that these evidences together provide a strong argument for our model where Vangl2 acts within the same cell to sequester Dvl from Fz.

In regards to the Dvl patches induced by Wnt11 (Fig. 3 and Suppl. Fig. 9), we performed separate injection of EGFP- and mSc-tagged Dvl into adjacent blastomeres, and demonstrated that the Wnt11-induced patches arise from symmetrical accumulation of Dvl at contact of two neighboring cells (Suppl. Fig. 9a-c’). This scenario is different from epithelial PCP where Fz/Dvl and Vangl/Pk are asymmetrically accumulated at the contact between two adjacent cells.

The authors propose a model whereby Vangl2 acts as an adaptor between Dvl and Ror, to first prevent ectopic activation of signaling, and then to relay Dvl to Fzd upon Wnt stimulation. This is based on the observation that Ror2 can be co-IPed with Vangl2 but not Dvl; and secondly that the distribution of Ror2 in membrane patches after Wnt11 stimulation is broader than that of Fzd7/Dvl, while Vangl2 localizes to the edges of these patches. The data for both these points is not wholly convincing. The co-IP of Ror2 and Vangl2 is very weak, and the input of Dvl into the same experiment is very low, so any direct interaction could have been missed. Secondly, the broader distribution of Ror2 in membrane patches is very subtle, and further analysis would be needed to firm up this conclusion. 

(1) We repeated the co-IP experiment with Myc-tagged Vangl or Dvl. Using the same anti-Myc antibody and experimental condition (including the expression level of Vangl, Dvl and Ror2), we still found that Ror2 could be pulled down by Vangl but not Dvl (Suppl. Fig. 15b). Whereas this data confirms our previous conclusion, we acknowledge that a negative data does not fully exclude the possibility for direct biding between Ror and Dvl.

(2) We re-analyzed the signal intensity of Dvl and Ror in Wnt11-induced patches. By quantifying the intensity ratio between Ror and Dvl along the patches, we found an increase over two folds at the border of the patches (Fig. 7j, bottom panel). We interpret this data to suggest that Ror is accumulated to a higher level than Dvl at the patch borders.     

A final caveat to these experiments is that in the animal cap assays, loss of function and gain of function both cause convergence and extension defects, so any genetic interactions need to be treated with caution i.e. two injected factors enhancing a phenotype does not imply they act in the same direction in a pathway, in particular as there are both cis/trans and positive/negative feedbacks between the PCP proteins. 

We agree with the reviewer that a difficulty in studying PCP/ non-canonical signaling is that both loss and gain of function of any its components can cause convergence and extension defects. Genetic interactions, especially synergistic interactions, should be interpreted with caution. But we do want to point out that, in a number of case, we were also able to demonstrate epistasis. For instance, we found that Dvl2 over-expression induced CE defects can be rescued by Pk over-expression (Fig. 1e and f), whereas Vangl/ Pk co-injection induced severe CE defects can be reciprocally rescued by Dvl2 over-expression (Fig. 1g). Likewise, we showed that Fz2/ Dvl2 co-injection induced CE defects can be rescued by wild-type Vangl2 but not Vangl2 RH mutant (Suppl. Fig. 6b), and Ror2 can rescue Vangl2 overexpression induced CE defect (Suppl. Fig. 14). Collectively, these functional interaction data consistently demonstrate an antagonism between Dvl/ Fz/ Ror2 and Vangl2/ Pk, which is correlated with our imaging and biochemical studies.

As you can see from the reviews, the referees generally agree that your paper is a potentially valuable contribution to the field. Your observations are important because of the novel model based on the inhibitory feedback regulation between planar cell polarity (PCP) protein complexes. However, the reviewers also stated that the model is only partly supported by data because of insufficient clarity and missing controls in several experiments supporting the proposed model. The paper would be significantly improved if your conclusions are backed up by additional experimentation. Specifically, the referees wanted to see the reproducibility of the results shown in Figures 3, 4, 8, S3, S7, S12. 

We hope that you are able to revise the paper along the lines suggested by the referees to increase the impact of your study on the current understanding of PCP signaling mechanisms. 

We thank the reviewers for careful reading of our manuscript and for their constructive critiques and suggestions. We have repeated the animal cap studies in original Figures 3, 4, 8 and S3 with DMZ explants, and the new data are in Supplementary Fig. 9, 11, 16 and 4, respectively. We also repeated the biochemical studies in original Figure S 7and 12, and the new data are in Supplementary Fig. 8 and 15.

Reviewer #1 (Recommendations For The Authors):

Major points:(1) The author conducted an analysis of the subcellular localization of PCP core proteins, including Vangl2, Pk, Fz, and Dvl, within animal cap explants (ectodermal explants). To validate the model proposing that 'non-canonical Wnt induces Dvl to transition from Vangl to Fz, while PK inhibits this transition, and they function synergistically with Vangl to suppress Dvl during Convergent Extension (CE),' it is crucial to assess the subcellular localization of PCP core proteins in dorsal marginal zone (DMZ) cells, which are known to undergo CE. Notably, the overexpression of Wnt11 alone, as employed by the author, does not induce animal cap elongation. Therefore, the use of animal cap explants may not be sufficient to substantiate the model during Convergent Extension (CE). Indeed, previous knowledge indicates that Vangl2 and Pk localize to the anterior region in DMZ explants. However, the results presented in this manuscript appear to differ from this established understanding. Consequently, to provide more robust support for the proposed model, it is advisable to replicate the key experiments (Figures 3, 4, 8, and Figure S3) using DMZ explants. 

We repeated the experiments in Figure 3, 4, 8 and Figure S3 with DMZ explant and the new data are in new Supplementary Fig. 9, 11, 16 and 4, respectively.In regards to “previous knowledge indicates that Vangl2 and Pk localize to the anterior region in DMZ explants”, we are aware Vangl/ Pk localization to the anterior cell cortex in neural epithelium from the studies by the Sokol and Wallingford labs, but are not aware of similar reports in DMZ explants. When we examined the localization of small amount of injected EGFP-mPk2 (0.1 ng mRNA) in DMZ explants, we saw a somewhat uniform distribution on the plasma membrane (Suppl. Fig. 4). In addition, in a related recent publication, we examined endogenous XVangl2 protein localization in activin induced animal cap explants that do undergo CE. What we observed was that whereas low level injected Dvl2 and Fz form clusters on the plasma member, endogenous XVangl2 remains uniformly distributed on the plasma membrane (Suppl. Fig. 3S-Z in 10.1038/s41467-025-57658-0 ). These observations may suggest potential differences of PCP protein localization during neural vs. mesodermal convergence and extension.

(2) The author suggests that 'Vangl2 and Pk together synergistically disrupt Fz7-Dvl2 patches.' As shown in Figure 4 (panels J' to I'), it is evident that the co-expression of Pk and Vangl2 increases Fz7 endocytosis. Nevertheless, a significant amount of Fz7 still co-localizes with Dvl2. To strengthen the author's hypothesis, additional clear assay is required such as Fluorescence resonance energy transfer (FRET) assay. 

We appreciate this valuable advice. Since none of the tagged Fz/ Dvl/ Vangl proteins we had were suitable for FRET, we made proteins tagged with mClover and mRuby2, which were reported as optimized FRET pairs. But in our hands mRuby2 seems to require very long time (~2 days) to mature and become detectable at room temperature, and is not suitable for our Xenopus experiments. We are in the process of establishing a luciferase based NanoBiT system to detect Fz-Dvl and Dvl-Vangl interactions in live cells and cell lysates, and will use it in future studies to investigate their interaction dynamics.

For the current manuscript, we reason that a substantial reduction of Fz7-Dvl2 clusters with Vangl2/ Pk co-injection would still support our idea that Vangl2 and Pk act synergistically to sequester Dvl from Fz to prevent their clustering in response to non-canonical Wnt ligands.

(3) The IP data is less clear and evident. A couple of examples are: a) Fig 2g where the authors report that the Vangl2 R177H variant reduced Vangl2 interaction with Pk and recruitment of Pk to the plasma membrane, but it appears that the variant interacts slightly better than WT Vangl2 with Pk. In Fig. S7a, the authors state that Pk overexpression can indeed significantly reduce Wnt11-induced dissociation of EGFP-Vangl2 and Flag-Dvl2 in the DMZ. However, there is a minimal impact when compared to the Wnt11 absent control. Based on the results presented in Fig S12a the authors indicate that Wnt11 reduces the association between Vangl2 and Dvl2, which can be discerned, but loss of Ror2 does not change this in any obvious way - but the authors indicate it does. In S12b, the authors have suggested that Ror and Dvl do not form a direct binding interaction. However, the interpretation of Figure S12b is not entirely convincing due to several issues. Notably, the expression levels of each protein appear inconsistent, the bands are not sufficiently clear, and there is the detection of three different tag proteins on a single blot. To strengthen the validity of these findings, it is advisable to repeat this experiment with improved quality. 

We repeated all the co-IP and western blot analyses pointed out by the reviewer, and performed quantification and statistical analyses.

Fig 2g had a mistake in the labeling and is replaced with new Figure 2g;

Fig. S7a is replaced by new data in Supplementary Figure 8a and b;

Fig. S12a and 12b are replaced by new data in Supplementary Figure 15a, a’ and b, respectively. In 15a and a’, we noticed a consistent decrease of Dvl2-Vangl2 co-IP in Xror2 morphant. The reason for this is not yet clear and will need further study in the future.

Minor points: (1) In all the whole embryo injection assays examining morphology, no Western analysis is performed to show roughly equivalent and appropriate levels of the various proteins are being expressed. Differences will affect the data. 

Although we did not do western analyses to examine the protein levels in various functional interaction assays, we did examine how co-expression of Vangl2, mPk2 or Dvl2 may impact each other’s protein levels in Supplementary Fig. 2, which did not reveal any significant change when co-injected in different combination.

(2) The author's prior publication (Bimodal regulation of Dishevelled function by Vangl2 during morphogenesis, Hum Mol Genet. 2017) presented clear evidence of Vangl2 overexpression inducing Dvl2 membrane localization. However, Figure S4 in the current manuscript did not provide clear evidence of membrane localization. To strengthen the hypothesis that Vangl2-RH mutant also induces Dvl2 membrane localization, further comprehensive imaging analysis is needed. 

We re-analyzed the imaging data and replaced old Figure S4 with a new Supplementary Fig. 5.

(3) In Supplementary Figure 9, the authors propose that the overexpression of Vangl2/Pk induces Fz7 endocytosis, as indicated by its co-localization with FM4-64. However, it raises a question: how does the Fz7-GFP protein internalize into the cells without endocytosis, as seen in Figures S9a-c'? To enhance readers' understanding, a discussion addressing this point should be included. 

We think that this might be a technical issue. As detailed in the Method section, we only incubated the embryos transiently with FM4-64 for 30 minutes, and the embryos were subsequently washed and dissected in 0.1X MMR without the dye. Therefore, only the Fz7-GFP protein endocytosed during the 30 minute-incubation would be labeled by FM-64, whereas that endocytosed before or after the incubation would not. Alternatively, the very few Fz7-GFP puncta occasionally observed in the absence of Vangl2/Pk overexpression could be vesicles trafficking to the plasma membrane.

(4) Statistical analyses are absent for several results, including those in Figure 2f, Figure S4d, and Figure S7b. 

We repeated these experiments and included statistical analyses. The new data are in Figure 2f, Supplementary Fig. 5d and Supplementary Fig. 8b.

(5) This manuscript lacks any results regarding Ck1. Therefore, it is advisable to consider removing the discussion or mention of CK1. 

We agree, and tune down the discussion on CK1 and removed CK1 from our model in Fig. 9.

Reviewer #2 (Recommendations For The Authors):

(1) In all the convergence and extension assays, the authors should report n numbers (i.e. number of animals), what statistical test is used, and what the error bars show. Ideally dot-plots would be used instead of bar charts as they give a better insight into the data distribution. It might be useful to give a section on the statistical analyses used in the M&M, including e.g. any power calculations carried out, as now required by many journals. 

We have follow the advice to use dot-plots for all the quantification analyses in the manuscript. We include in the figure legends the statistical test used and what the error bars show. The number of embryos analyzed were included in each panel in the figures. We also provided more details in the Methods section on how the LWR quantification was carried out.

(2) I think Figure 2g is wrongly labelled? FLAG bands are in all three lanes in the western blot, but not labelled as such in the schematic. 

We corrected the schematic labeling in Figure 2g, and thank the reviewer for catching this mistake.

(3) In Figure S7, the authors show that co-IP of Dvl and Vangl2 is reduced by Wnt11 and the effects of Wnt are blocked by Pk. Does Pk have any effect in the absence of Wnt? 

We examined the effect of Pk over-expression on Dvl2-Vangl2 co-IP as advised, and did not see a significant impact in the absence of Wnt11 co-injection. The data is included in the new Supplementary Figure 8a. We interpret the data to suggest that “at least under the condition of our co-IP experiment, Pk may not directly impact the steady-state binding between Vangl and Dvl”.

(4) In Figure 3, the authors show (as published previously) that Wnt11 induces patches of Dvl at the plasma membrane. It would be useful to see Dvl in the absence of Wnt and Vangl2/Dvl in the absence of Wnt. 

Dvl is widely known as a cytoplasmic protein and its localization has been published by many labs over the past 20-30 years. In our recent publication (10.1038/s41467-025-57658-0 ), we also re-examined Dvl localization when injected at various dosages. So we did not feel it was necessary to show its localization in the absence of Wnt11 again, but included a reference to our prior publication. In regards to Vangl/Dvl distribution in the absence of Wnt11, the readers can see Suppl. Fig. 5b as an example, in addition to our previous publications referenced in the manuscript.

(5) In the review figures, the difference in Fz7-GFP patch formation in d' and e' (vs e.g. a') is not very clear. Could the images be improved or (better) quantified in some way? 

We assume that “review figures” refer to Figure 3 or 4? If so, we felt that Fz7-GFP patch formation was clear in Fig. 3d’, e’ or Fig. 4d’, e’. Nevertheless, we repeated these experiments in DMZ explants as advised by Reviewer 1, and additional examples of Fz7-EGFP patch formation can be seen in the new Suppl. Fig. 9d-f’ and Suppl. Fig. 11d-f’.

(6) In Figure 6d, I'm concerned that the loss of flag-Dvl2 might occur via dephosphorylation in the IP reaction. Also the M&M don't include methodological details about buffers and whether phosphatase inhibitors were used. A compelling control would be anti-FLAG pulldown showing retention of phosphorylation. Also Figure 6f shows a reduced ratio of fast-to-slow migrating bands of Dvl with Vangl2/Pk - unless I have misunderstood, is this ratio the wrong way round? 

We added co-IP buffer and protease inhibitor information in Methods.

We agree that the concern about dephosphorylation during IP reaction is valid, and that direct pull down of Dvl to show the phosphorylated form is a compelling control. We therefore note that in Suppl. Fig. 8a and 15b, direct pull down of Flag-Dvl or Myc-Dvl (with anti-Flag or anti-Myc) did show the slower migrating, phosphorylated form. Additional examples in which Vangl only co-IP the faster migrating unphosphorylated Dvl include Suppl. Fig. 15a, and in a related paper we published recently (Fig. 3R and R’ in 10.1038/s41467-025-57658-0 ).

Finally, we did wrongly label Figure 6f in the last submission, and the ratio should have been “slow/fast”. We have made the correction, and appreaicte the reviewer for the meticulousness in perusing our manuscript.

(7) In Figure 7, what does Ror2 look like in the absence of Wnt11? 

We included new Figure 7a-c to show that without Wnt11 co-injection, Ror2 is uniformly distributed on the plasma membrane.

(8) Also in Figure 7, Ror2 patches are said to be slightly wider than Dvl2 patches "reminiscent of Vangl2" - I wouldn't describe them as being similar. Vangl2 shows a distinct dip in the center of the Dvl patches, Ror2 does not show a dip, and is only (at best) in a slightly wider patch, and I would want to see further examples to be convinced that the localization domain is reproducibly wider. The merge of many samples in 7d may actually be making the distribution harder to see and if the Xror2 and Dvl2 intensities were normalized I'm not sure how different the curves would appear. (i.e. the Xror2 curve looks like a flattened version of the Dvl2 curve). 

We have added an additional panel in the new Figure 7j to compare the intensity ratio of Ror/ Dvl2 along the patches, and this analysis reveals an over two folds increase of the ratio at the border region. This quantification may make a more convincing argument that at the patch border region, Dvl is diminished whereas Ror2 accumulate with Vangl2. 

(9) In Figure S12a, the authors suggest Wnt11 induced dissociation of Dvl from Vangl2 (by co-IP), and this is reduced after Ror2 MO. This would be more convincing with replicates and quantitation. 

We have repeated this experiment with Vangl2 pull down and added quantification. The data is in the new Suppl. Fig. 15a.

(10) In Figure S12b, the authors suggest Ror2 can co-IP Vangl2 but not Dvl. This is not very convincing, as the Dvl input band is very weak, and the Vangl2 co-IP band is very weak. 

We repeated the co-IP experiment with Myc-tagged Vangl or Dvl. Using the same anti-Myc antibody and experimental condition (including the expression level of Vangl, Dvl and Ror2), we still found that Ror2 could be pulled down by Vangl but not Dvl (Suppl. Fig. 15b).

(11) "Prickle" spelled "Prickel" in the abstract (and abbreviated to "PK" not "Pk" at one place in the abstract and several places in text) 

We have corrected these typos.

(12) Quite a lot of interesting observations are in supplemental figures. Normally it might be expected that extra data supporting a conclusion would be in supplemental, but here some of the supplemental data feels like it is more than simply additional evidence. For instance supplemental Figures 2 and 3 feel more than just supplemental (and Supplemental Figure 3 if merged with Figure 2 would make it easier for the reader). Moreover, for example, the description of the results in Figure 2 is punctuated by references to supplemental Figures 4 and 5 that contain key data to support the conclusions, which means the reader has to flick backwards and forwards from place to place in the manuscript to follow the argument. It is of course up to the authors, but in some cases putting supplemental data back into the main figures (for which there is no size or number limit) would increase clarity. 

These are excellent points; in the resubmitted manuscript we have a total of 24 data figures, and we used 8 as main figures since we felt that they provide the most relevant and conclusive evidence to our model. We will consult the copy editors at eLife on how to arrange the rest as main vs. supporting figures when requesting publication as version of record.

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Reply to the reviewers

We thank the reviewers for their thoughtful comments and overall very supportive feedback.

Reviewer #1 writes: "The study is very thorough and the experiments contain the appropriate controls. (...) The findings of the study can have relevance for human conditions involving disrupted mitochondrial dynamics, caused for example by mutations in mitofusins." Reviewer #2 writes: "The dataset is rich and the time-resolved approach strong." Reviewer #3 writes: "I admire the philosophy of the research, acknowledging an attempt to control for the many possible confounding influences. (...) This is a powerful and thoughtful study that provides a collection of new mechanistic insights into the link between physical and genetic properties of mitochondria in yeast."

We address all points below. We have not yet updated our text and figures since we expect substantial additions from new experiments. But we have included Figure R1 with some additional analyses of existing data at the bottom of the manuscript.

Reviewer1

1.1 Statistical comparisons are missing throughout the manuscript (with the exception of Fig. 2c). Appropriate statistical tests, along with p-values, should be used and reported where different gorups are compared, for example (but not limited to) Fig. 3d and most panels of Fig. 4.

We initially decided not to add too many extra labels to the already very busy plots, given that the magnitude of change mostly speaks for itself. However, we will try to find meaningful statistical tests together with a sensible graphical representation for all of the figures. For one example see Figure R1A.

1.2. I do not agree with the use of Atp6 protein as a direct read-out of mtDNA content. While Atp6 protein levels will decrease with decreasing mtDNA content, the inverse is not necessarily true: decreased Atp6 protein levels do not necessarily indicate decreased mtDNA levels, because they could alternatively or additionally be caused by decreased transcription and/or translation. Therefore, please do not equate Atp6 protein levels to mtDNA levels, and instead rephrase the text referencing the Atp6 experiments in the Results and Discussion sections to measure "mtDNA expression" or "mt-encoded protein" or similar. For example, on p. 14 line 431 should read "mtDNA expression" rather than "decreased synthesis of mtDNA", and line 440 on the same page "mean mtDNA levels" should be "mtDNA expression" or similar.

All three reviewers agree that using Atp6-NG as a direct proxy for mtDNA requires more validation, or at least rephrasing of the text. We agree that this is the most important point to address. We had previously tried using the mtDNA LacO array (Osman et al. 2015) to directly assess the amount of nucleoids per cell. However, the altered mitochondrial morphology of the Fzo1 depleted cells combined with the LacI-GFP which is still in mitochondria even when mtDNA is gone, increases the noise level to a point that we cannot interpret the signal. However, as this manuscript was in the submission process, the Schmoller lab (co-authors #2 and #7) adapted the HI-NESS system to label mtDNA in live yeast cells(Deng et al. 2025). This system promises much better signal to noise and we expect we can address all concerns regarding the actual count of nucleoids per cell. Should this unexpectedly fail for technical reasons, we will try to calibrate the Atp6-levels with DAPI staining at defined time points and will rephrase the text as the reviewer suggests.

1.3. In Fig. 3, the authors use the fluorescence intensity of a mitochondrially-targeted mCardinal as a read-out of mitochondrial mass. Please provide evidence that this is not affected by MMP, either with relevant references or by control experiments (e.g. comparing it to N-acridine orange or other MMP-independent dyes or methods).

Whether or not the import of any mitochondrial protein is dependent on the MMP depends largely on the signal sequence. The preSu9-signaling sequence was previously characterized as largely independent of the MMP compared to other presequences (Martin, Mahlke, and Pfanner 1991), which is why Vowinckel (Vowinckel et al. 2015) and others (Di Bartolomeo et al. 2020; Perić et al. 2016; Ebert et al. 2025) have previously used this as a neutral reference to the strongly MMP-dependent pre-Cox4 signal to estimate MMP. As one control in our own data, we consider that the population-averaged mitochondrial fluorescent signal Figure S3C stays constant in the first few hours, in agreement with the total averaged mitochondrial proteome (Fig R1E). As additional controls, we plan to compare the signal to an MMP independent dye as the reviewer suggests.

1.4. In Fig. 2e-f, the authors use a promoter reporter with Neongreen to answer whether the reduced levels of the nuclear-encoded mitochondrial proteins Mrps5 and Qcr7 are due to decreased expression or to protein degradation, and find no evidence of degradation of the Neongreen reporter protein. However, subcellular localization might affect the availability of the protein to proteases. Although not absolutely required, it would be relevant to know if the Neongreen fusion protein is found in the same subcellular compartment as Mrps5 and Qcr7 at 0h and 9h after Fzo1 depletion.

Here, it seems we need to explain the set-up and interpretation of the data better. The key point we are trying to make with the promoter-Neongreen construct is that the regulation is not mainly at the level of transcription. We are showing that the reduction in the levels of the actual protein (orange bars) is not (mainly) explained by a reduction in expression, since the promoter is similarly active at 0 and at 9 hours (grey bars). If expression from the promoter were strongly reduced, the Neongreen would be diluted with growth and would also decrease, but this is not the case. The fluorophore itself is just floating around in the cytosol and is not subject to the same post-translational regulation as Mrps5 and Qcr7, so there is no reason to expect degradation.

1.5. Fzo1 depletion leads to a very rapid drop in MMP during the first hour of depletion. In the Discussion, can the authors speculate on the possible mechanism of this rapid MMP drop that occurs well before mtDNA or mt-encoded proteins are decreased in level?

This is indeed an interesting point. We think there are likely three reasons causing this initial drop: Firstly, due to the fragmentation the mixing of mitochondrial content is disturbed and smaller fragments may have suboptimal stoichiometry of components (see also (Khan et al. 2024) who look at this in detail including the Fzo1 deletion); secondly, already fairly early, some mitochondrial fragments may not contain any mtDNA and therefore will be unable to synthesize ETC proteins; thirdly, altered morphological features like changes in the surface-to-volume ratios may play a role. Sadly, mechanistically following up on this is not possible with the tools in our hands and therefore outside of the scope of this manuscript. But we are happy to include these speculations in our discussion.

1.6. In Fig. 2a, the mtDNA copy number of Fzo1-depleted cells is ca 1.3-fold of the control cells at the 0h timepoint. Why might this be? Is it an impact of one of the inducers? If so, we might be looking at the combination of two different processes when measuring copy number: one that is an induction caused by the inducer(s), and the other a consequence of Fzo1 depletion itself.

We believe that this 30% increase is within the noise of the experiment rather than an effect of the induction. Since we normalize to t=0 uninduced, the first black data point does not have error bars, emphasizing this difference. None of the protein data suggests that there is an increase in mtDNA encoded proteins (see e.g. 2B, or Atp6 fluorescence data). In the planned HI-NESS experiment, we will see in our single cell data whether there is an actual increase in mtDNA upon TIR induction. Additionally, we will run a qPCR to carefully determine mtDNA levels of untreated wild-type cells, tetracycline treated wild-type cells and tetracycline induced TIR expressing cells to exclude effects of tetracycline as well as the expression of TIR on mtDNA.

Minor comments:

1.7. p. 3, line 71: "ten thousands of dividing cells.." should be "tens of thousands of dividing cells".

Thank you, will correct.

1.8.-p.4, line 116: please be even more clear with what the "depleted" cells and controls are treated with: are depleted cells treated with both inducers, and controls with neither?

We will make this more clear. Depleted cells are treated with both inducers, the control cells are not. However, in Figure 1A and in S1 we do controls to show that inducing TIR per se or adding aTC per se does not change growth rate or mitochondrial morphology. We will make this more clear.

1.9. -p.5, lines 147-148: the authors write "the rate with which the abundance of Cox2 and Var1 proteins decreases was similar to the rate of mtDNA loss" though the actual rate is not shown. Please calculate and show rates for these processes side by side to make comparison possible, or alternatively rephrase the statement.

Indeed this was not phrased well. We will call it dynamics rather than rates.

1.10. -Fig. 2d: changing the y-axis numbering to match those in panels a and b would facilitate comparisons.

Makes sense, we will change this.

1.11. Fig. 2e: it is recommended to label the western blot panels to indicate what protein is being imaged in each (Neongree,, Mrps5, Qcr7).

We will adapt the labelling to make it more clear.

1.12. -p.9, line 262: I suggest referencing Fig. 4e at the end of the first sentence for clarity.

We will modify the sentence as suggested.

1.13. -In the sections related to Fig. 3a and Fig. 5a as well as the connected supplemental data, the authors discuss both the median and the mean of mitochondrial mass and Atp6 protein, respectively. For purposes of clarity, I suggest decreasing the focus on the mean (that is provided only in the supplemental data) and focusing the text mainly on the median. The two show differing trends and it is very good that both are shown, but the clarity of the text can be improved by focusing more on the median where possible.

We will check the phrasing and simplify.

1.14. -p. 14, line 435: the statement that mt mass is maintained over the first 9h of depletion is only true for the mean mt mass, not for the median. Please make this clear or rephrase.

We will check phrasing, make it more clear and also point out the extended proteomics data (see Fig R1), which corresponds to the mean of the populations

1.15.-p.14, line 452: "mitofusions" should be "mitofusins".

Thanks for catching this.

Reviewer 2:

2.1. While inducible TIR is used to reduce background, the manuscript should rigorously exclude auxin/TIR off-targets (growth, mitochondrial phenotypes, gene expression). Please include full matched controls: (plus minus)auxin, (plus minus)TIR, epitope tag alone, and a degron control on an unrelated mitochondrial membrane protein.

We agree that rigorous controls are crucial for the interpretation of the results. However, we think we have already included most of the controls the reviewer is asking for, but we might have not pointed this out clearly enough. For example, in Fig 1A, we could make it more clear by adding more labels in which samples we added aTC, which is only described in the figure legend.

Here is a list of all the controls:

• Each depletion experiment is always matched with an experiment of the same strain without induction. So the genetic background as well as effects such as light exposure, time spent in the microfluidics systems, etc are controlled for.
• Figure S1D shows that the growth rate is wildtype like in a strain containing either the AID tag or the TIR protein AND upon addition of both chemicals. It also shows that the final genetic background (AID-tag and TIR) also grows like wildtype if the inducers are not added. This conclusively shows that neither the tags/constructs nor the chemicals per se affect growth rate
• In Figure S1C we show the mitochondrial morphology of the same controls. We will make sure to label them more consistently to match panel D, and include an actual wildtype and a FLAG-AID-Fzo1 strain without TIR treated with both aTC and 5-Ph-IAA as direct comparison
• In figure 1A we compare the Fzo1 protein levels of a strain with and without TIR. We show that in absence of TIR, adding either aTC or Auxin does not change Fzo1 levels and that the levels are comparable in the strain that is able to deplete Fzo1 directly before addition of 5-Ph-IAA (after 2 h of induction of TIR through addition of tetracycline)
• Additionally, in Figure S2C we show that two hours after adding aTC, the entire proteome does not change significantly apart from a strong induction of TIR. We can also make this more clear in the figure legend.
• Additionally, we will run a qPCR to carefully determine mtDNA levels of untreated wild-type cells, tetracycline treated wild-type cells and tetracycline induced TIR expressing cells to exclude effects of tetracycline as well as the expression of TIR on mtDNA. (also in response to 1.6.) In summary, we think we have controlled sufficiently for all confounding parameters and most importantly showed that addition of either aTC or Auxin as well as the FLAG-AID tag per se does not disturb mitochondria or cell growth. We do not see what a degron control on an unrelated protein will tell us. Depending on the nature of the protein, it may or may not have a phenotype that may or may not be related to morphology changes etc.

2.2. The Mitoloc preSu9 vs Cox4 import ratio is only a proxy of mitochondrial membrane potential (ΔΨm) and itself depends on mitochondrial mass, protein expression, matrix ATP, and import saturation. The authors need to calibrate ΔΨm with orthogonal dyes (TMRE/TMRM) and pharmacologic titrations (FCCP/antimycin/oligomycin) to generate a response curve; show that Mitoloc tracks dye-based ΔΨm across the relevant range and corrects for mass/photobleaching. Report single-cell ΔΨm vs mass residuals.

We completely agree that the MitoLoc system is only a rough proxy for the actual membrane potential. That is why we make no quantitative claims on the absolute value or absolute difference between groups of cells. We also make very clear in Fig 3B what we are actually measuring and can emphasize again in the text that this is only a proxy. We agree that it is a good idea to compare MitoLoc values to TMRE staining as the reviewer suggests, we will do these experiments in depleted and control cells at different timepoints. Please note though that also dye staining has its caveats, especially in dynamic live cell experiments. TMRM for example is not compatible with the acidic pH 5 medium that is typically used for yeast and subjecting cells to washing steps and higher pH may change both morphology of mitochondria and the MMP, especially in cells that are already “stressed”. We prefer not to complete elaborate pharmacological titration experiments because firstly, this was extensively done in the original MitoLoc paper by the Ralser lab ((Vowinckel et al. 2015), cited 120 times); secondly, the value of the MMP is not the most critical claim of the manuscript. See also 3.12. Please note that in Figure S4D we had already plotted MMP vs mitochondrial concentration.

2.3. To use Atp6-mNeon as a proxy for mtDNA is an assumption. Interpreting Atp6 intensity as "functional mtDNA" could be confounded by translation, turnover, or assembly. Please (i) report mtDNA copy number time courses (you have qPCR), nucleoid counts (DAPI/PicoGreen or TFAM/Abf2 tagging), and (ii) assess translation (e.g., 35S-labeling or puromycin proxies) and turnover (proteasome/AAA protease inhibition, mitophagy mutants -some data are alluded to- plus mRNA levels for mtDNA-encoded genes). This will support the "reduced synthesis" versus "increased degradation" conclusion.

We agree with all three reviewers that Atp6 is only a proxy for mtDNA (Jakubke et al. 2021; Roussou et al. 2024) and the correlation should be checked more carefully. We will use the very recently established Hi-NESS system to follow nucleoids/ mtDNA during depletion experiments. See detailed reply to 1.2.

(ii) in Figure 2C we inhibit mitochondrial translation and show that in this case control and depleted cells have the same level of Cox2, at least suggesting that degradation is not the key mechanism controlling the levels of mtDNA encoded proteins. We cannot do proteasome inhibitor assays since the nature of the AID-TIR systems requires an active proteasome. In figure S5C we show that the Atp6 depletion is similar in an atg32 deletion. This does not completely exclude a contribution of mitophagy to the observed phenotype, but does confirm that mitophagy is not the primary reason for cells becoming petite.

2.4. The promoter-NeonGreen reporters argue against transcriptional down-regulation of nuclear OXPHOS. Please add mRNA (RT-qPCR/RNA-seq) for representative genes and a pulse-chase or degradation-pathway dependency (e.g., proteasome/mitophagy/autophagy mutants) to firmly assign active degradation. The authors need to normalize proteomics to mitochondrial mass (e.g., citrate synthase/porin) to separate organelle abundance from protein turnover.

While we are happy to perform qPCR experiments for selected genes, a full RNA-seq experiment seems outside the scope of this study. As explained above, a proteasome inhibitor experiment is not possible in this set-up. Bulk mitophagy/autophagy seems unlikely to be the cause of the decrease of the nuclear-encoded OXPHOS proteins, since most other mitochondrial proteins do not decrease on average on population level in the first hours. This data is now plotted as additional figure (see below) and will be included in the supplementary of the revised manuscript (Fig R1E).

2.5. Using preSu9-mCardinal intensity as "mitochondrial concentration" is sensitive to expression, import competence, and morphology/segmentation. The authors should provide validation that this metric tracks 3D volume across fragmentation states (e.g., correlation with mito-GFP volumetrics; detergent-free CS activity; TOMM20/Por1 immunoblot per cell).

We agree that this is an important point and the co-authors discussed this point quite intensively. In figure S3A and B we show (using confocal data) that there is a very strong correlation between the total fluorescence signal and the 3D volume reconstruction. However, the slope of the correlation is different between tubular and fragmented mitochondria (compare panels A and B) and see figure legend. Since we are dealing with diffraction-limited objects it is likely that the 3D reconstruction is sensitive to morphology, especially if mitochondria are “clumping”. We therefore think that the total fluorescence signal is actually a better estimate of mitochondrial mass per cell than the 3D volume reconstruction (especially for our data obtained with a conventional epifluorescence microscope). The mean of the total mitochondrial fluorescence also better matches the population average mitochondrial proteome (Fig R1E). To consolidate this assumption, we will additionally compare our data to a strain with Tom70-Neongreen and to MMP independent dyes.

Notably, since the morphology is similarly altered in mothers and buds this is of minor impact for our main point – the unequal distribution between mother and buds.

2.6. The unequal mother-daughter distribution is compelling, but causality remains inferred. Test whether modulating inheritance machinery (actin cables/Myo2, Num1, Mmr1) or altering fission (Dnm1 inhibition) modifies segregation defects and rescues mtDNA/Atp6 decline. Complementation with Fzo1 re-expression at defined times would help order the phenotype cascade.

We agree that rescue experiments would be very useful. We have some preliminary data for tether experiments, for example with Num1. The general problem is that the fragmented mitochondria clump together. We have not found a method to restore an equal distribution between mother and daughter cells. We will try to optimize the assay, but are not overly confident it will work. Mmr1 deletion aggravates the Fzo1 phenotype, likely also because the distribution becomes even more heterogeneous, but we have not rigorously analyzed this.

We like the idea of the Fzo1 re-expression and will run such experiments. This will be especially powerful in combination with the new HI-NESS mtDNA reporter. We may be able to track exactly when cells reach the point-of-no return and become petite. This will also help connecting our mathematical model more directly to the data.

2.7. The model is useful but should include parameter sensitivity (segregation variance, synthesis slopes, initial nucleoid number) and prospective validation (e.g., predict rescue upon partial restoration of synthesis or inheritance, then test experimentally).

We will refine our model to include the to-be-measured nucleoids/mtDNA values. We will include a parameter sensitivity analysis with the updated model.

Reviewer 3:

3.1. About the use of Atp6 as a good proxy for mtDNA content. This is assumed from l285 onwards, based on a previous publication. As the link is fairly central to part of the paper's arguments, and the system in this study is being perturbed in several different ways, a stronger argument or demonstration that this link remains intact (and unchanged, as it is used in comparisons) would seem important.

We agree, see 1.2.

3.2. About confounding variables and processes. The study does an admirable job of being transparent and attempting to control for the many different influences involved in the physical-genetic link. But some remain less clearly unpacked, including some I think could be quite important. For example, there is a lot of focus on mito concentration -- but given the phenotypes are changing the sizes of cells, do concentration changes come from volume changes, mito changes, or both? In "ruling out" mitophagy -- a potentially important (and intuitive) influence, the argument is not presented as directly as it could be and it's not completely clear that it can in fact be ruled out in this way. There are a couple of other instances which I've put in the smaller points below.

Thank you for acknowledging our efforts to show transparent and well-controlled experiments! We address each of the specific points below.

3.3. full genus name when it first appears

We will add the full name.

3.4. I may be wrong here, but I thought the petite phenotype more classically arises from mtDNA deletion mutations, not loss? The way this is phrased implies that mtDNA loss is [always] the cause. Whether I'm wrong on that point or not, the petite phenotype should be described and referenced.

We can expand the text and cite additional relevant papers. The term “petite” refers to any strain that is respiratory incompetent and leads to small colonies (not necessarily small cells!) (Seel et al. 2023). This can be mutations or gene loss (fragments) on the mtDNA (these are called cytoplasmic petite), or chemically induced loss of mtDNA (e.g. EtBr), or mutations of nuclear genes required for respiration (these are termed nuclear petite; some nuclear petites show loss of mtDNA in addition to the mutation in the nuclear genome) (Contamine and Picard 2000).

3.5. para starting l59 -- should mention for context that mitochondria in (healthy, wildtype) yeast are generally much more fused than in other organisms

ok.

3.6. Fig 1C -- very odd choice of y-axis range! either start at zero or ensure that the data fill as much vertical space of the plot as possible

True, this was probably some formatting relic. We will adapt the axis to fill the full space. Most of our axes start at 0, but that doesn’t make so much sense here, since we consider the solidity in the control as “baseline”.

3.7. "wild-type like more tubular mitochondria" reads rather awkwardly. "more tubular mitochondria (as in the wild-type)"?

Thank you, sounds better.

3.8. l106 -- imaging artefacts? are mitos fragmenting because of photo stress? -- this is mentioned in l577-8 in the Methods, but the data from the growth rate and MMP comparison isn't given -- an SI figure would be helpful here. It would be reassuring to know that mito morphology wasn't changing in response to phototoxicity too.

In the methods we just briefly point out that we have done all our “due diligence” controls to check that we do not generate phototoxicity, something that we highlight in the cited review. We do not explicitly have a figure for this, but figure S1A shows that the solidity of the mitochondrial network in control cells stays the same over 9 hours, even though these cells are exposed to the same cultivation and imaging regime as the depleted cells. We will also add a picture of control cells after 9 h. In S1B we show that control cells containing TIR but no AID tag treated with both chemicals imaged over 9 hours also show the same solidity (~mitochondrial morphology) as untreated control. Also, the doubling times of cells grown in our imaging system (Fig R1B) are very similar to the shake flask (Fig R1A). All in all, we are very confident that our imaging settings did not impact our reported phenotypes.

3.9. para l146 -- so this suggests mtDNA-encoded proteins have a very rapid turnover, O(hours) -- is this known/reasonable?

Reference (Christiano et al. 2014) suggests that respiratory chain proteins are shorter lived than the average yeast protein. However, based on Figure 2C we think the dynamics mostly speak for a dilution by growth.

3.10. section l189 -- it's hard to reason fully about these statistics of mitochondrial concentration given that the petite phenotype is fundamentally affecting overall cell volume. can we have details on the cell size distribution in parallel with these results? to put it another way -- how does mitochondrial *amount* per cell change?

This is a good point. We report mostly on mitochondrial “concentrations” because we think this is what the cell actually cares about (mitochondrial activity in relationship to cytosolic activity). But we will include additional graphs on mitochondrial amount as well as size distributions (Fig R1C, related to Fig 4F). We can already point out that the size distribution of the population does not change much in the first hours. The “petite” phenotype refers to small colonies on growth medium with limited supply of a fermentable carbon source, not to smaller size of single cells.

3.11. l199 the mean in Fig S3C certainly does change -- it increases, clearly relative both to control and to its initial value. rather than sweeping this under the carpet we should look in more detail to understand it (a consequence of the increased skew of the distribution)?

This relates somewhat to the previous point. The increase in average concentration is not due to an increased amount in the population, but due to the fact that it is the small buds that get a very high amount of the mitochondria which “exaggerates” the asymmetric/heterogenous distribution. This will be clarified by the figures we mention in the point above.

3.12. para line 206 -- this doesn't make it clear whether your MMP signal is integrated over all mitochondria in the cell, or normalised by mitochondrial content? this matters quite a lot for the interpretation if the distributions of mitochondrial content are changing. reading on, this is even more important for para line 222. Reading further on, there is an equation on l612 that gives a definition, but it doesn't really clarify (apologies if I'm misunderstanding).

For each cell, we basically calculate the relative mitochondrial enrichment of the MMP sensitive vs the MMP insensitive pre-sequence.

So, MMP= (total intensity of mitochondrial pre-Cox4 Neongreen/ total intensity of mitochondrial pre-Su9 Cardinal) / (total cytosolic pre-Cox4 Neongreen/ total cytosolic pre-Su9 Cardinal).

We calculate this value for each cell, but we do not have the optical resolution to calculate it for individual mitochondrial fragments.

Both constructs are driven by the same strong promoter, so transcription of the fluorophore should never limit the uptake. Also, in Figure 3D we compare control and depleted cells with similar total mitochondrial concentration, so the difference must be due to a different import of the two fluorophores, see also Fig S4D. The calculated “MMP” value is of course only a crude proxy for the actual membrane potential in millivolts and we do not want to make any claims on absolute values or quantitative differences. But essentially what we are interested in is “mitochondrial health/activity” and we think the system is good at reporting this. See also 2.2.

3.13. l230 -- a point of personal interest -- low mito concentrations are connected to low "function" (MMP) and give extended division times -- this is interestingly exactly the model needed to reproduce observations in HeLa cells (https://journals.plos.org/ploscompbiol/article?id=10.1371/journal.pcbi.1002416). That model went on to predict several aspects of downstream cellular behaviour -- it would be very interesting to see how compatible that picture (parameterised using HeLa observations) is with yeast!

Thank you for pointing out your interesting paper, which we will include in our discussion. Another recent preprint about fission yeast (Chacko et al. 2025) also fits into this picture. Since you were kind enough to disclose your identity, we would be happy to discuss this further with you in person if we can maybe follow-up on this.

3.14. l239 "less mitochondria" -- a bit tricky but I'd say "fewer mitochondria" or "less mitochondrial content"

Thanks, we will think about how to best rephrase this, probably less mitochondrial content.

3.15. Section l234 So here (and in Fig 4) the focus is on overall distributions of mitochondrial concentration in different cells (mother-to-be, mother, bud; gen 1, gen >1). But we've just seen that one effect of fzo1 is to broader the distribution of mitochondrial concentration across cells. Can't we look in more depth at the implications of this heterogeneity? For example in Fig 4F (which is cool) we look at the distribution of all fzo1 mothers-to-be, mothers, and buds. But this loses information about the provenance. For example, do mothers-to-be with extremely low mito concentrations just push everything to the bud, while mothers-to-be with high mito concentrations distribute things more evenly? It would seem very easy and very interesting to somehow subset the distribution of mothers-to-be by concentration and see how different subsets behave

This is a good point. When analyzing the data, we pretty much plotted everything against everything and then chose the graphs that we think will best guide the reader through the story-line. We can make additional supplementary plots where we show the starting concentrations/amounts of the mother in relationship to the resulting split ratio at the end of the cycle (Fig R1D).

3.16. l285 -- experimental design -- do we know that Atp6 will continue to be a good proxy for functional mtDNA in the face of the perturbations provided by Fzo1 depletion? Especially if there is impact on the expression of mitoribosomes, the relationship between mtDNA and Atp6 may look rather different in the mutant?

This is actually our top-priority experiment now. We will use the HI-NESS system and possibly DAPI staining to make a more direct link to mtDNA/ nucleoid numbers, see 1.2.

3.17. l290 -- ruled out mitophagy. This message could be much clearer. Comparing Fig S5C and Fig 3A side-by-side is a needlessly difficult task -- put Fig 3A into Fig S5. Then we see that when mitophagy is compromised, the distribution of mitochondrial concentration has a lower median and much lower upper quartile than in the mitophagy-equipped Fzo1 mutant? What is going on here? For a paper motivated by disentangling coupled mechanisms, this should be made clearer!

Thanks for pointing this out. We can of course easily include the control in the corresponding figure. Compromising mitophagy is likely to generally affect mitochondrial health and turnover a little bit, independent of what is going on with Fzo1. The second evidence that speaks against large-scale mitophagy is the proteomics data: On population level the dynamics of the respiratory chain proteins are very different from those of other (nuclear encoded) mitochondrial proteins. We will add additional supplementary figures to make this more clear, see Fig R1E. Most mitochondrial proteins in the proteomics experiment stay constant in the first few hours, consistent with the imaging data showing that the mean mitochondrial content of the population does not change initially. This again highlights that it is the unequal distribution which is the problem and not massive degradation of mitochondria.

3.18. With the Atp6 signal, how do we know that fluorescence from different cells is comparable? Buds will be smaller than mother cells for example, potentially leading to less occlusion of the fluorescent signal by other content in the cytoplasm

This is of course a general problem that anyone faces doing quantitative fluorescence microscopy. From the technical side, we have done the best we could by taking a reasonable amount of z-slices and by choosing fluorophores that are in a range with little cellular background fluorescence (e.g. Neongreen is much better than GFP). From a practical standpoint, we are always comparing to the control, which is subject to the same technical limitations as the depleted cells and the cell sizes are very similar. So, even if we are systematically overestimating the Atp6 concentration in the bud by a few %, the difference to the control would still be qualitatively true. We therefore do not think that any of our conclusions are affected by this.

3.19. l343 -- maintenance of mtDNA -- here the point about l285 (is the Atp6-mtDNA relationship the same in the Fzo1 mutant) is particularly important, as we're directly tying findings about the protein product to implications about the mtDNA

We will carefully address this, see above.

3.20. l367 -- on a first read this description of the model feels like lots of choices have been made without being fully justified. Why a log-normal distribution (when the fit to the data looks rather flawed); why the choice of 5 groups for nucleoid number (why not 3? or 8?); the process used for parameter fitting is very unclear (after reading the methods I think some of these values are read directly from the data, but the shapes of the distributions remain unexplained). l705 -- presumably the ratio was drawn from a log-normal distribution and then the corresponding nucleoid numbers were rounded to integers? the ratio itself wasn't rounded? (also l367) How were the log-normal distributions fitted to experiments (Figs. S7A,B)? Just by eye?

We will update our model based on measured nucleoid counts and then explain more stringently the choices we make/ parameters we select.

3.21. l711 by random selection -- just at random? ("selection" could be confusing) Overall, it feels like the model may be too complicated for what it needs to show. Either (a) the model should show qualitatively that unequal inheritance and reduced production leads to rapid loss -- which a much simpler model, probably just involving a couple of lines of algebra, could show. Or (b) the model should quantitatively reproduce the particular numerical observations from the experiments -- it's not totally clear that it does this (do the cell-cycle-based decay timescales in Fig 7 correspond to the hour-based decay timescales in other plots, for example). At the moment the model is at a (b) level of detail but it's only clear that it's reporting the (a) level of results.

If the HI-NESS and Fzo1 re-addition experiments work as explained above, all parameters will have direct experimental data, and we should get much closer to (a).

3.22. A lot of the discussion repeats the results; depending on editorial preferences some of this text could probably be pared back to focus on the literature connections and context.

We will think about streamlining the discussion once some of the additional material alluded to above has been added.

3.23. Data availability -- it looks like much of the data required to reproduce the results is not going to be made available. Images and proteomic data are promised, but the data associated with mitochondrial concentration and other features are not mentioned. For FAIR purposes all the data (including statistics from analysis of the images) should be published.

We maybe didn’t phrase this clearly. All data will be made available. Where technically feasible, this will be directly accessible in a repository, otherwise by request to the corresponding author.

On our OMERO server, we have deposited many TB of raw images as well as all the intermediate steps such as segmentation masks, and the csv files with all the extracted data for each cell (including background corrections etc). Additionally, we can include csvs with the data grouped in a way that we used to generate all the box blots etc. As of now, the OMERO data is unfortunately only available by requesting a personal guest login from our bioinformatics facility, but we were promised that with the next technical update there will be a public link available. The proteomics data and the model are already fully accessible. The raw western blot images with corresponding ponceau staining will be included with the final publication either as additional supplementary material or in whatever format matches the journal requirements.

3.24 l660 -- can an overview of the EM protocol be given, to avoid having to buy the Mayer 2024 article?

The cited paper is open access. But we can also include more details in our method section.

References:

Chacko, L. A., H. Nakaoka, R. Morris, W. Marshall, and V. Ananthanarayanan. 2025. 'Mitochondrial function regulates cell growth kinetics to actively maintain mitochondrial homeostasis', bioRxiv.

Christiano, R., N. Nagaraj, F. Frohlich, and T. C. Walther. 2014. 'Global proteome turnover analyses of the Yeasts S. cerevisiae and S. pombe', Cell Rep, 9: 1959-65.

Contamine, V., and M. Picard. 2000. 'Maintenance and integrity of the mitochondrial genome: a plethora of nuclear genes in the budding yeast', Microbiol Mol Biol Rev, 64: 281-315.

Deng, Jingti, Lucy Swift, Mashiat Zaman, Fatemeh Shahhosseini, Abhishek Sharma, Daniela Bureik, Francesco Padovani, Alissa Benedikt, Amit Jaiswal, Craig Brideau, Savraj Grewal, Kurt M. Schmoller, Pina Colarusso, and Timothy E. Shutt. 2025. 'A novel genetic fluorescent reporter to visualize mitochondrial nucleoids', bioRxiv: 2023.10.23.563667.

Di Bartolomeo, F., C. Malina, K. Campbell, M. Mormino, J. Fuchs, E. Vorontsov, C. M. Gustafsson, and J. Nielsen. 2020. 'Absolute yeast mitochondrial proteome quantification reveals trade-off between biosynthesis and energy generation during diauxic shift', Proc Natl Acad Sci U S A, 117: 7524-35.

Ebert, A. C., N. L. Hepowit, T. A. Martinez, H. Vollmer, H. L. Singkhek, K. D. Frazier, S. A. Kantejeva, M. R. Patel, and J. A. MacGurn. 2025. 'Sphingolipid metabolism drives mitochondria remodeling during aging and oxidative stress', bioRxiv.

Jakubke, C., R. Roussou, A. Maiser, C. Schug, F. Thoma, R. Bunk, D. Horl, H. Leonhardt, P. Walter, T. Klecker, and C. Osman. 2021. 'Cristae-dependent quality control of the mitochondrial genome', Sci Adv, 7: eabi8886.

Khan, Abdul Haseeb, Xuefang Gu, Rutvik J. Patel, Prabha Chuphal, Matheus P. Viana, Aidan I. Brown, Brian M. Zid, and Tatsuhisa Tsuboi. 2024. 'Mitochondrial protein heterogeneity stems from the stochastic nature of co-translational protein targeting in cell senescence', Nature Communications, 15: 8274.

Martin, J., K. Mahlke, and N. Pfanner. 1991. 'Role of an energized inner membrane in mitochondrial protein import. Delta psi drives the movement of presequences', J Biol Chem, 266: 18051-7.

Osman, C., T. R. Noriega, V. Okreglak, J. C. Fung, and P. Walter. 2015. 'Integrity of the yeast mitochondrial genome, but not its distribution and inheritance, relies on mitochondrial fission and fusion', Proc Natl Acad Sci U S A, 112: E947-56.

Perić, Matea, Peter Bou Dib, Sven Dennerlein, Marina Musa, Marina Rudan, Anita Lovrić, Andrea Nikolić, Ana Šarić, Sandra Sobočanec, Željka Mačak, Nuno Raimundo, and Anita Kriško. 2016. 'Crosstalk between cellular compartments protects against proteotoxicity and extends lifespan', Scientific Reports, 6: 28751.

Roussou, Rodaria, Dirk Metzler, Francesco Padovani, Felix Thoma, Rebecca Schwarz, Boris Shraiman, Kurt M. Schmoller, and Christof Osman. 2024. 'Real-time assessment of mitochondrial DNA heteroplasmy dynamics at the single-cell level', The EMBO Journal, 43: 5340-59-59.

Seel, A., F. Padovani, M. Mayer, A. Finster, D. Bureik, F. Thoma, C. Osman, T. Klecker, and K. M. Schmoller. 2023. 'Regulation with cell size ensures mitochondrial DNA homeostasis during cell growth', Nat Struct Mol Biol, 30: 1549-60.

Vowinckel, J., J. Hartl, R. Butler, and M. Ralser. 2015. 'MitoLoc: A method for the simultaneous quantification of mitochondrial network morphology and membrane potential in single cells', Mitochondrion, 24: 77-86.

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Referee #3

Evidence, reproducibility and clarity

This article addresses the connection between perturbed mitochondrial structure and genetics in yeast. When mitochondrial fusion is compromised, what is the chain of causality -- the mechanism -- that leads to mtDNA populations becoming depleted? This is a fascinating question, linking physical cell biology to population genetics. I admire the philosophy of the research, acknowledging and attempt to control for the many possible confounding influences. The manuscript describes the context and the research tightly and digestibly; the figures illustrate the results in a clear and natural way.

For transparency, I am Iain Johnston and I am happy for this review to be treated as public domain. To my eyes my most important shortcoming as a review is my relative lack of familiarity with the yeast fzo1 mutant; while I am familiar with analysis of yeast mito morphology and mtDNA segregation, a reviewer familiar with the nuances of this strain and its culture would be a useful complement.

I have a few more general points and a collection of smaller points below that I believe might help make the story more robust.

General points

1. About the use of Atp6 as a good proxy for mtDNA content. This is assumed from l285 onwards, based on a previous publication. As the link is fairly central to part of the paper's arguments, and the system in this study is being perturbed in several different ways, a stronger argument or demonstration that this link remains intact (and unchanged, as it is used in comparisons) would seem important.
2. About confounding variables and processes. The study does an admirable job of being transparent and attempting to control for the many different influences involved in the physical-genetic link. But some remain less clearly unpacked, including some I think could be quite important. For example, there is a lot of focus on mito concentration -- but given the phenotypes are changing the sizes of cells, do concentration changes come from volume changes, mito changes, or both? In "ruling out" mitophagy -- a potentially important (and intuitive) influence, the argument is not presented as directly as it could be and it's not completely clear that it can in fact be ruled out in this way. There are a couple of other instances which I've put in the smaller points below.

Smaller points

l47 full genus name when it first appears

l58 I may be wrong here, but I thought the petite phenotype more classically arises from mtDNA deletion mutations, not loss? The way this is phrased implies that mtDNA loss is [always] the cause. Whether I'm wrong on that point or not, the petite phenotype should be described and referenced.

para starting l59 -- should mention for context that mitochondria in (healthy, wildtype) yeast are generally much more fused than in other organisms

Fig 1C -- very odd choice of y-axis range! either start at zero or ensure that the data fill as much vertical space of the plot as possible

l105 "wild-type like more tubular mitochondria" reads rather awkwardly. "more tubular mitochondria (as in the wild-type)"?

l106 -- imaging artefacts? are mitos fragmenting because of photo stress? -- this is mentioned in l577-8 in the Methods, but the data from the growth rate and MMP comparison isn't given -- an SI figure would be helpful here. It would be reassuring to know that mito morphology wasn't changing in response to phototoxicity too.

para l146 -- so this suggests mtDNA-encoded proteins have a very rapid turnover, O(hours) -- is this known/reasonable?

section l189 -- it's hard to reason fully about these statistics of mitochondrial concentration given that the petite phenotype is fundamentally affecting overall cell volume. can we have details on the cell size distribution in parallel with these results? to put it another way -- how does mitochondrial amount per cell change?

l199 the mean in Fig S3C certainly does change -- it increases, clearly relative both to control and to its initial value. rather than sweeping this under the carpet we should look in more detail to understand it (a consequence of the increased skew of the distribution)?

para line 206 -- this doesn't make it clear whether your MMP signal is integrated over all mitochondria in the cell, or normalised by mitochondrial content? this matters quite a lot for the intepretation if the distributions of mitochondrial content are changing. reading on, this is even more important for para line 222. Reading further on, there is an equation on l612 that gives a definition, but it doesn't really clarify (apologies if I'm misunderstanding).

l230 -- a point of personal interest -- low mito concentrations are connected to low "function" (MMP) and give extended division times -- this is interestingly exactly the model needed to reproduce observations in HeLa cells (https://journals.plos.org/ploscompbiol/article?id=10.1371/journal.pcbi.1002416). That model went on to predict several aspects of downstream cellular behaviour -- it would be very interesting to see how compatible that picture (parameterised using HeLa observations) is with yeast!

l239 "less mitochondria" -- a bit tricky but I'd say "fewer mitochondria" or "less mitochondrial content"

Section l234 So here (and in Fig 4) the focus is on overall distributions of mitochondrial concentration in different cells (mother-to-be, mother, bud; gen 1, gen >1). But we've just seen that one effect of fzo1 is to broader the distribution of mitochondrial concentration across cells. Can't we look in more depth at the implications of this heterogeneity? For example in Fig 4F (which is cool) we look at the distribution of all fzo1 mothers-to-be, mothers, and buds. But this loses information about the provenance. For example, do mothers-to-be with extremely low mito concentrations just push everything to the bud, while mothers-to-be with high mito concentrations distribute things more evenly? It would seem very easy and very interesting to somehow subset the distribution of mothers-to-be by concentration and see how different subsets behave

l285 -- experimental design -- do we know that Atp6 will continue to be a good proxy for functional mtDNA in the face of the perturbations provided by Fzo1 depletion? Especially if there is impact on the expression of mitoribosomes, the relationship between mtDNA and Atp6 may look rather different in the mutant?

l290 -- ruled out mitophagy. This message could be much clearer. Comparing Fig S5C and Fig 3A side-by-side is a needlessly difficult task -- put Fig 3A into Fig S5. Then we see that when mitophagy is compromised, the distribution of mitochondrial concentration has a lower median and much lower upper quartile than in the mitophagy-equipped Fzo1 mutant? What is going on here? For a paper motivated by disentagling coupled mechanisms, this should be made clearer!

With the Atp6 signal, how do we know that fluorescence from different cells is comparable? Buds will be smaller than mother cells for example, potentially leading to less occlusion of the fluorescent signal by other content in the cytoplasm

l336 -- similar to the Jajoo et al. mechanism in fission yeast -- but are you talking about feedback control of the mtDNA or the protein (or mRNA) product?

l343 -- maintenance of mtDNA -- here the point about l285 (is the Atp6-mtDNA relationship the same in the Fzo1 mutant) is particularly important, as we're directly tying findings about the protein product to implications about the mtDNA

l367 -- on a first read this description of the model feels like lots of choices have been made without being fully justified. Why a log-normal distribution (when the fit to the data looks rather flawed); why the choice of 5 groups for nucleoid number (why not 3? or 8?); the process used for parameter fitting is very unclear (after reading the methods I think some of these values are read directly from the data, but the shapes of the distributions remain unexplained). l705 -- presumably the ratio was drawn from a log-normal distribution and then the corresponding nucleoid numbers were rounded to integers? the ratio itself wasn't rounded? (also l367) How were the log-normal distributions fitted to experiments (Figs. S7A,B)? Just by eye? l711 by random selection -- just at random? ("selection" could be confusing) Overall, it feels like the model may be too complicated for what it needs to show. Either (a) the model should show qualitatively that unequal inheritance and reduced production leads to rapid loss -- which a much simpler model, probably just involving a couple of lines of algebra, could show. Or (b) the model should quantitatively reproduce the particular numerical observations from the experiments -- it's not totally clear that it does this (do the cell-cycle-based decay timescales in Fig 7 correspond to the hour-based decay timescales in other plots, for example). At the moment the model is at a (b) level of detail but it's only clear that it's reporting the (a) level of results.

A lot of the discussion repeats the results; depending on editorial preferences some of this text could probably be pared back to focus on the literature connections and context.

Data availability -- it looks like much of the data required to reproduce the results is not going to be made available. Images and proteomic data are promised, but the data associated with mitochondrial concentration and other features are not mentioned. For FAIR purposes all the data (including statistics from analysis of the images) should be published.

l660 -- can an overview of the EM protocol be given, to avoid having to buy the Mayer 2024 article?

Significance

This is a powerful and thoughtful study that provides a collection of new mechanistic insights into the link between physical and genetic properties of mitochondria in yeast. Cell biologists, geneticists, and the mitochondrial field will find this of potentially deep interest. Because of the mode and dynamics of inheritance in budding yeast, findings here may not be directly transferrable to other eukaryotes, but these insights are still of interest for researchers outside of yeast for their insight into how this well-studied system manages its mitochondrial populations.

Author response:

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

Reviewer #1 (Public Review):

Summary:

This is a manuscript describing outbreaks of Pseudomonas aeruginosa ST 621 in a facility in the US using genomic data. The authors identified and analysed 254 P. aeruginosa ST 621 isolates collected from a facility from 2011 to 2020. The authors described the relatedness of the isolates across different locations, specimen types (sources), and sampling years. Two concurrently emerged subclones were identified from the 254 isolates. The authors predicted that the most recent common ancestor for the isolates can be dated back to approximately 1999 after the opening of the main building of the facility in 1996. Then the authors grouped the 254 isolates into two categories: 1) patient-to-patient; or 2) environment-to-patient using SNP thresholds and known epidemiological links. Finally, the authors described the changes in resistance gene profiles, virulence genes, cell wall biogenesis, and signaling pathway genes of the isolates over the sampling years.

Strengths:

The major strength of this study is the utilisation of genomic data to comprehensively describe the characteristics of a long-term Pseudomonas aeruginosa ST 621 outbreak in a facility. This fills the data gap of a clone that could be clinically important but easily missed from microbiology data alone.

Weaknesses:

The work would further benefit from a more detailed discussion on the limitations due to the lack of data on patient clinical information, ward movement, and swabs collected from healthcare workers to verify the transmission of Pseudomonas aeruginosa ST 621, including potential healthcare worker to patient transmission, patient-to-patient transmission, patient-to-environment transmission, and environment-to-patient transmission. For instance, the definition given in the manuscript for patient-to-patient transmission could not rule out the possibility of the existence of a shared contaminated environment. Equally, as patients were not routinely swabbed, unobserved carriers of Pseudomonas aeruginosa ST 621 could not be identified and the possibility of misclassifying the environment-to-patient transmissions could not be ruled out. Moreover, reporting of changes in rates of resistance to imipenem and cefepime could be improved by showing the exact p-values (perhaps with three decimal places) rather than dichotomising the value at 0.05. By doing so, readers could interpret the strength of the evidence of changes.

Impact of the work:

First, the work adds to the growing evidence implicating sinks as long-term reservoirs for important MDR pathogens, with direct infection control implications. Moreover, the work could potentially motivate investments in generating and integrating genomic data into routine surveillance. The comprehensive descriptions of the Pseudomonas aeruginosa ST 621 clones outbreak is a great example to demonstrate how genomic data can provide additional information about long-term outbreaks that otherwise could not be detected using microbiology data alone. Moreover, identifying the changes in resistance genes and virulence genes over time would not be possible without genomic data. Finally, this work provided additional evidence for the existence of long-term persistence of Pseudomonas aeruginosa ST 621 clones, which likely occur in other similar settings.

We thank the reviewer for their thorough evaluation of our work, and for the suggested improvements. A main goal of this study was to show that integrating routine wgs in the clinic was a game changer for infection control efforts. We appreciate this aspect was highlighted as a strength by this reviewer. While some of the weaknesses identified are inherent to the data (or lack thereof) available for this study, we have revised the manuscript to include a detailed discussion on limitations (sampling, thresholds of genetic relatedness, definition and categories etc.) that could influence the genomic inferences. We also provided exact p-values for the changes in rates of resistance, as requested. Finally, we have positively answered all the specific recommendations suggested by the reviewer and modified the manuscript accordingly.

Reviewer #2 (Public Review):

Summary:

The authors present a report of a large Pseudomonas aeruginosa hospital outbreak affecting more than 80 patients with first sampling dates in 2011 that stretched over more than 10 years and was only identified through genomic surveillance in 2020. The outbreak strain was assigned to the sequence type 621, an ST that has been associated with carpabapenem resistance across the globe. Ongoing transmission coincided with both increasing resistance without acquisition of carbapenemase genes as well as the convergence of mutations towards a host-adapted lifestyle.

Strengths:

The convincing genomic analyses indicate spread throughout the hospital since the beginning of the century and provide important benchmark findings for future comparison.

The sampling was based on all organisms sent to the Multidrug-resistant Organism Repository and Surveillance Network across the U.S. Military Health System.

Using sequencing data from patient and environmental samples for phylogenetic and transmission analyses as well as determining recurring mutations in outbreak isolates allows for insights into the evolution of potentially harmful pathogens with the ultimate aim of reducing their spread in hospitals.

Weaknesses:

The epidemiological information was limited and the sampling methodology was inconsistent, thus complicating the inference of exact transmission routes. Epidemiological data relevant to this analysis include information on the reason for sampling, patient admission and discharge data, and underlying frequency of sampling and sampling results in relation to patient turnover.

We thank the reviewer for their thoughtful feedback on our manuscript and for highlighting the quality of the genomic analyses. We agree that the lack of patient epi data (e.g. date of admission and discharge) and the inconsistent sampling through the years are limitations of this study. We have revised the manuscript to acknowledge these limitations and discuss how not having this data complicates the inference of exact transmission routes. Finally, we have positively answered all the specific recommendations suggested by the reviewer and modified the manuscript accordingly.

Reviewer #3 (Public Review):

Summary:

This paper by Stribling and colleagues sheds light on a decade-long P. aeruginosa outbreak of the high-risk lineage ST-621 in a US Military hospital. The origins of the outbreak date back to the late 90s and it was mainly caused by two distinct subclones SC1 and SC2. The data of this outbreak showed the emergence of antibiotic resistance to cephalosporin, carbapenems, and colistin over time highlighting the emerging risk of extensively resistant infections due to P. aeruginosa and the need for ongoing surveillance.

Strengths:

This study overall is well constructed and clearly written. Since detailed information on floor plans of the building and transfers between facilities was available, the authors were able to show that these two subclones emerged in two separate buildings of the hospital. The authors support their conclusions with prospective environmental sampling in 2021 and 2022 and link the role of persistent environmental contamination to sustaining nosocomial transmission. Information on resistance genes in repeat isolates for the same patients allowed the authors to detect the emergence of resistance within patients. The conclusions have broader implications for infection control at other facilities. In particular, the paper highlights the value of real-time surveillance and environmental sampling in slowing nosocomial transmission of P. aeruginosa.

Weaknesses:

My major concern is that the authors used fixed thresholds and definitions to classify the origin of an infection. As such, they were not able to give uncertainty measures around transmission routes nor quantify the relative contribution of persistent environmental contamination vs patient-to-patient transmission. The latter would allow the authors to quantify the impact of certain interventions. In addition, these results represent a specific US military facility and the transmission patterns might be specific to that facility. The study also lacked any data on antibiotic use that could have been used to relate to and discuss the temporal trends of antimicrobial resistance.

We thank the reviewer for their evaluation of our work and for highlighting the broad implications of our findings regarding the application of real-time surveillance to suppress nosocomial transmission. We agree with the reviewer that fixed thresholds and definitions are imperfect to classify the origin of an infection. The design of this study (e.g. inconsistent sampling through time) was not conducive to provide a comprehensive/quantitative measurement of transmission routes. Thus, we decided to apply conservative thresholds of genetic relatedness and strict conditions (e.g. time between isolate collection, shared hospital location etc.) to favor specificity as our goal was simply to establish that cases of environmentto-patient transmission did happen. In the absence of a truth set, we have not performed sensitivity analysis, but we are conducting a follow-up study to compare inferences from MCMC models to our original fixed-thresholds predictions. This limitation is now discussed in the revised manuscript. Finally, we have positively answered all the specific recommendations suggested by the reviewer and modified the manuscript accordingly including the addition of Figure S3.

Reviewer #1 (Recommendations For The Authors):

The definitions used on lines 391-396 are necessarily somewhat arbitrary, but it would be helpful to have a little bit more justification for the choices made, particularly for the definition of environmental involving the "3x the number of years they were separated". It seems a little hard to square this with the more relaxed 10 SNP cutoff for a patient-to-patient designation. Are there reasons for thinking SNP differences associated with environmental transmission should be smaller than for patient-to-patient, or is the aim here just to set the bar higher for assuming an environmental source? Because these definitions are quite arbitrary, there could also be some value in exploring the sensitivity of the results to these assumptions.

Thank you. We agree with the reviewers that SNP thresholds, albeit necessarily, are arbitrary and that more discussion/justification was needed to put the genomic inferences in context. We have revised the manuscript to indicate that: 1/ the 10 SNP cutoff for a patient-to-patient designation was set to account for the known evolution rate of P. aeruginosa (inferred by BEAST at 2.987E-7 subs/site/year in this study and similar to previous estimates PMID: 24039595) and the observed within host variability (now displayed in revised Fig. 1E). We note that this SNP distance was not sufficient and that an epi link (patients on the same ward at the same time) needed to be established. 2/ the environment-to-patient definition was indeed set to be most conservative (nearly identical isolates in two patients from the same ward with no known temporal overlap for > 365 days). This was indeed done to favor high specificity as this inference relied solely on clinical isolates (i.e. the identical environmental strain in the patientenvironment-patient chain was not sampled). For these clinical isolates to have acquired no/very little mutation in that much time, no/low replication is expected and, although unsampled, we propose this most likely happened on hospital surfaces.

While the term "core genome" should be familiar to most readers, "shell genome" and "cloud genome" are less widely known, and an explanation of what these terms mean here would be helpful.

Thank you. We have revised the manuscript to define the core, shell, and cloud genomes as genes sets found in ≥ 99%, ≥ 95% and ≥ 15% of isolates, respectively.

In the first paragraph of the discussion, it could be added that in many cases for clinically important Gram negatives short read sequencing alone will fail to detect transmission events as outbreaks can be driven by plasmid spread with only very limited clonal spread (see, for example, https://www.nature.com/articles/s41564-021-00879-y )

Thank you. We agree this is an important/emerging aspect of surveillance. However, the goal of this discussion point was to explain why such a large outbreak was missed prior to implementing WGS (short read) surveillance. We feel that discussing “plasmid outbreaks” (which is not at play here, and relatively rare in P. aeruginosa compared to the Enterobacteriaceae) and the need for long read will distract from the narrative. 

line 599 What does "Mock" mean here? Would it be more accurate to say it is a simplified floor plan?

Thank you. “Mock” was changed to “simplified”

IPAC abbreviation is only used once - spelling it out in full would increase readability.

Revised manuscript was edited as suggested.

MHS is only used twice.

Revised manuscript was edited to spell out Military Health System

Line 364: full stop missing.

Revised manuscript was edited as suggested.

Line 401: Bayesian rather than bayesian.

Revised manuscript was edited as suggested.

Reviewer #2 (Recommendations For The Authors):

Thank you for giving me the opportunity to review this interesting manuscript.

The conclusions of this paper are mostly well supported by the data presented, but epidemiological information was limited and the sampling methodology was inconsistent, thus complicating inference of exact transmission routes.

Major issues:

What was the baseline frequency of clinical and/or screening samples of Pseudomonas aeruginosa at the hospital? Neither Figure 1D nor Table S1 allows for differentiating between clinical and screening samples. Most isolates were cultured from clinical materials, and there is no information about the patients' length of stay and their respective sampling dates. Is there any possibility of finding out whether the samples were collected for clinical or screening purposes? Would it be possible to include the patients' admission data to determine whether the strains were imported into the hospital or related to a previous stay, e.g. among known carriers? Also, the issue of sampling dates vs. patient stay on the ward should be addressed, as there may be an overlap in patients' stay on the ward but no overlap in terms of sampling dates or even missing samples (missing links).

We have revised the manuscript to address this important point: i) 16 isolates were from surveillance swabs and are labelled “Surveillance” in Table S1. The remaining 237 were clinical isolates; ii) unfortunately, because the sampling was done under a public health surveillance framework, we do not have access to historical patient data (admission/discharge date, wards, rooms, etc.) and we can not calculate length of stay or better identify patient overlap. These limitations are now acknowledged in the discussion of the revised manuscript.

In order to evaluate the extent of the outbreak, more epidemiological data would be useful What is the size of the hospital, what is the average patient turnover, and what is the average length of stay in ICU and non-ICU? Is there any specialization besides the military label?

We have revised the manuscript to indicate that facility A is 425-bed medical center and is the only Level 1 trauma center in the Military Health System. Unfortunately, the data to calculate length of stay, throughout the years, in ICU and non-ICU, was not available to us. This limitation is now also acknowledged in the discussion.

Perhaps the authors could attempwt to discuss the extent to which large outbreaks like these may be considered as part of unavoidable evolutionary processes within the hospital microbiome as opposed to accumulation and transmission of potentially harmful genes/clones, and differentiate between the putative community spread without any epidemiological links on the one hand, and hospital outbreaks that could be targeted by local infection prevention activities on the other hand.,

We respectfully disagree with the suggestion that this large outbreak “may be considered as part of unavoidable evolutionary processes within the hospital microbiome” and should be opposed to “transmission of potentially harmful genes/clones”. As a matter of fact, our data showed that infection control staff at Facility A responded with multiple interventions, including closing sinks, replacing tubing, and using foaming detergents. This resulted in slowing the spread of the ST621 outbreak with just 3 cases identified in 2022, 0 cases in 2023 and 1 case in 2024. This is now discussed in the revised manuscript.

Page 5, lines 88-92 lines 101-104. It seems as if the outbreak was identified only by the means of genomic surveillance. This raises questions as to the rationale for sampling and sequencing, especially prior to 2020. Considering 11 cases per year between 2011 and 2016, one could assume such an outbreak would have been noticed without sequencing data.

The MRSN was created in 2010, in response to the outbreak of MDR Acinetobacter baumannii in US military personnel returning from Iraq and Afghanistan. Between 2011 and 2017, the MRSN collected MDR isolates (mandate for all MDR ESKAPE but compliance varied between years and facilities) from across the Military Health System and, for select isolates (e.g. high-risk isolates carrying ESBLs or carbapenemases) performed molecular typing by PFGE. In 2017 the MRSN started to perform whole genome sequencing of its entire repository. In 2020, a routine prospective sequencing service was started and first detected the ST621 outbreak. A retrospective analysis of historical isolate genomes (2011-2019) identified additional cases. The first paragraph of the discussion lists possible factors to explain why the ST621 escaped detection by traditional approaches. We believe 11 cases per year is not a strong signal when stratified by month, wards, or both, especially for a clone lacking a carbapenemase and without a remarkable antibiotic susceptibility profile. 

Did the infection control personnel suspect transmission? If yes, was the sampling and submission of samples to the MRSN adapted based on the epidemiologic findings?

The ST621 outbreak was unsuspected before the initial genomic detection in 2020. Until that point, MDR isolates only (Magiorakos et al PMID: 21793988) were collected but compliance was variable through time. Quickly thereafter (starting in 2021), complete sampling of all clinical P. aeruginosa (MDR or not) from Facility A was started. The manuscript was revised to clarify those details of the sampling strategy.

Is there any information about how many environmental sites were sampled without evidence of ST621 / screening samples were cultured without evidence of Pseudomonas aeruginosa?

For patient isolates, only 16 isolates were from surveillance swabs. The remaining 237 were clinical isolates. No denominator data was available to calculate P. aeruginosa and ST-621 positivity rate in surveillance swabs throughout the time period. For environmental isolates, a total of 159 swabs were taken from 55 distinct locations in 8 wards/units including the ER. This data is now included in the revised manuscript. However, a complete analysis of these swabs (positivity rate for ESKAPE pathogens, P. aeruginosa, per ward/floor/room, per swab type (sink drain, bed rail etc.) etc.) is beyond the scope of this study and is being performed as a follow up investigation.

Page 5 lines 89 and 39 Figure S1B. Please describe how the allelic distance for the cluster threshold was selected.

As indicated in the legend of Figure S1B, no thresholds were applied. All ST621 isolates ever sequenced by the MRSN were included. All except 3 isolates shared between 023 cgMLST allelic differences. The remaining 3 were distant by 88-89 allelic differences. The text was revised to clarify this point.

Page 5 lines 99-100. Could the authors please provide some distribution measures (e.g. IQR).

Done as requested. The revised manuscript now reads “…of just 38 single nucleotide polymorphisms (SNPs), and an IQR of 19 (Fig. 1A, Table S1).”

Page 5 line 102. Could the authors please provide some distribution measures (e.g. IQR).

Please see above. A chart was created and is now included as Fig. S2.

Page 6 line 107 and page 34 figure 1c. In the text it is stated that isolates were collected in 27 wards, the figure 1C depicts 26 wards and n/a.

Thank you for spotting this inconsistency. This has been fixed in the revised manuscript.

Page 6 lines 117-118. Samples collected in the emergency room would imply samples collected on admission, already addressed previously. Did the authors investigate a potential import into the hospital from community reservoirs or were all these isolates collected among patients who had been previously admitted to the hospital and/or tested positive for the outbreak strain?

We agree that samples collected in the ER imply samples collected on admission. Of the 29 ER isolates only 9 (31%) were primary isolates (first detection in a new patient) which suggests a majority were from returning patients at Facility A. Because the sampling was done under a public health surveillance framework, we do not have access to historical patient data (admission/discharge date, wards, rooms, etc.) to investigate/confirm that these 9 patients had previous visits at Facility A. This point is now discussed in the revised manuscript.

Page 6 line 128. This could also represent increased selective pressure. However, according to Table S1, the 28 isolates collected in 2011 (the number does not match with Figure 1D) were from many different wards, thus indicating earlier spread throughout the hospital.

Yes, we agree. Please note that table S1 lists all isolates for 2011 whereas Figure 1D focuses on primary (first isolate from each patients) only.  

Page 7 line 133. Both Figure 2 and the discussion section, page 13 line 296 suggest the year 2005 instead of 2004?

Thank you for catching this typographical error. This was corrected to 2004 in the revised manuscript.

Figure 1E. The figure should also depict intra-patient diversity for comparison.

Thank you for this great suggestion. We have revised Figure 1E accordingly.

Page 7, lines 146-147 Could the authors attempt explaining the upper part of the bimodal peaks?

This is an all-vs-all SNP analysis for all inter-patient isolates. For each isolates all distances to other isolates are reported, not only the smallest. The upper peaks represent comparisons to isolates from a different outbreak subclone (SC1 vs SC2).

Page 7, line 150 This is a very small number considering the extent of the outbreak and suggests a large number of missing links. Or does this rather imply continuous import and evolution over time that does not necessarily represent transmission within the hospital?

We believe all cases were due to transmission happening within the hospital. Based on conservative thresholds (genetic relatedness and epi link, or lack thereof) the precise origin from another patient (n=10) or a contaminated surface (n=12) can be inferred. For the remaining 60 patients, with the available sampling, the conditions we chose are not met and we simply do not conclude whether a direct patient-to-patient or an environmental origin was more likely.

Page 8 line 155. What does the temporal overlap refer to - sampling date versus patient's stay on the ward? Please specify.

The temporal overlap was investigated from sampling dates, as dates of patient admission/discharged were not available.

Page 8, line 157: What does primary/serial isolate mean - first and follow-up samples of ST621 per patient?

Yes. Primary isolate is used to designate the first isolate from a patient. Serial isolates designate follow-up samples of ST621.

Page 8 line 165: Table S3 and Figure 3 only refer to environmental samples from three wards. Ward 20 rooms 2 and 18 as well as ward 1 rooms 1 and 6 were hotspots - is there any information on the specific infection control/disinfection measures? Addressed in discussion page 12, lines 273-275, but no information on what was actually done.

The manuscript was revised to indicate the precise disinfection measures that were taken. A follow-up study is ongoing to assess long-term efficacy and monitor possible retrograde growth from previously contaminated sinks.

Page 8 line 175: Evaluation of change in resistance fraction over time - There may have been a selection bias with an inconsistent number of strains sequenced per year.

Yes, incomplete sampling and possible selection bias are now listed with other limitations of this study in the discussion of the revised manuscript.

Page 9 line 183: The referral to Table S1 is unclear, I could not find the number and the specific isolates selected for long-read sequencing.

Thank you. This has been added to the revised Table S1.

Page 10 lines 217-225 and Figure 4C: Perhaps it is possible to better align what is written in the text and the caption of the figure. The caption does not clarify that only one patient develops colistin resistance (what was the reason to include the other patients?).

Thank you. We have revised the text and the caption of the figure to clarify that only isolates from one patient developed colistin resistance. The isolates from the other patients on Fig. 4C are shown to provide context and accurately map the emergence of the PhoQE77fs mutation.  

Page 10, lines 228-229 and Table S5: How is it possible to identify those 64 genes in Table S5?

We have revised Table S5 to facilitate the identification of the 64 genes with ≥ 2 independently acquired mutations (excluding SYN). Specifically, we have added column E labeled “Counts independent mutations per locus (excluding SYN)”. A total of 205 rows (in this table each row is a variant) have a value ≥ 2 and these represent 64 genes (upon deduplication of locus tags).  

Page 13, lines 280-281: Where is the information on chronic infection presented? Serial cultures would not necessarily mean chronic infection.

Authors response: Yes, we agree this was not the appropriate characterization and this was revised to ‘long-term’ infections.

Page 14 line 306: Emergence of colistin resistance in a single patient, correct?

Yes. This was further clarified in the text.

Page 14 lines 315-320: This should go to the results section. In particular disinfection, closing, and replacing of tubing should be mentioned in the results section in reference to the results presented in Table S3.

Thank you. We have considered this suggestion and have decided to leave this discussion as the closing paragraph of this publication. A follow-up study is ongoing to assess long-term efficacy of these interventions on the ST-621 bur also other outbreak clones at Facility A.

Methods

Page 15 lines 330-333: Perhaps it is possible to avoid redundancy.

Thank you. We have revised the text accordingly.

Page 15 lines 341: Information on which isolates were subjected to long-read sequencing is missing.

Thank you. This has been added to the revised Table S1.

Page 16 line 345: Was there a particular reason why Newbler was chosen?

No. At the time Newbler was the default assembler built in the MRSN bacterial genome analysis pipeline and QC processes.

Page 16, line 357-358: What was the rationale for selecting this isolate as reference genome?

This isolate was chosen because it was collected early in the outbreak and phylogenetic analysis revealed it had low root to tip divergence.

Page 16 line 361: Why 310 isolates, if only 253 were assigned to the outbreak clone and only a subset of those were collected in facility A?

This was a typographical error that has corrected (it now reads “…set of 253 isolates.”) in the revised manuscript.  

Page 17 lines 387-395: What is the reason that intra-patient diversity was not included in the set of criteria for SNP distances?

The observed within host variability (now displayed in revised Fig. 1E) was taken into consideration when setting SNP thresholds for categorizing patient-to-patient transmission or environment-to-patient event. This is now clarified in the revised manuscript.

Page 17 line 392: How was the threshold of <=10 SNPs determined?

The 10 SNP cutoff to infer a patient-to-patient transmission event was set to account for the known evolution rate of P. aeruginosa (inferred by BEAST at 2.987E-7 subs/site/year in this study, and similar to previous estimates PMID: 24039595) and the observed within host variability (now displayed in revised Fig. 1E). We note that this SNP distance was not sufficient and that an epi link (patients on the same ward within the same month) needed to be established.

Page 17 line 395 and Figure 2: What was the assumed average mutation rate per genome per year?

Thank you. The mean substitution rate inferred by BEAST was 2.987E-7 similar to estimate from previous studies on P. aeruginosa outbreaks (e.g. PMID: 24039595).

Reviewer #3 (Recommendations For The Authors):

Please find (line-by-line comments) on each section of the manuscript below:

Introduction

Line 86: I am wondering why the authors state ">28 facilities" instead of the exact number of facilities from which these lineages were recovered.

Thank you. Manuscript was revised to provide the exact number of facilities. It now reads “…recovered from 37 and 28 facilities, respectively.”

Methods

It's not clear to me which criteria were used for collecting these isolates (both prospective and retrospective). I understand that some of the data are described in more detail in Lebreton et al but I did not find the specific criteria for the collection of the isolates and I imagine that these might differ if different facilities. Would it be possible to comment on that and add a short paragraph in the Methods section?

Thank you. This lack of clarity was also raised by other reviewers, and we have revised the manuscript to indicate that: 1/MDR isolates only (Magiorakos et al PMID: 21793988) were collected from 2011-2020 with the same criteria for all facilities although compliance was variable through time and between facilities; and 2/ starting in 2021 all P. aeruginosa isolates, irrespective of their susceptibility profile, were collected from Facility A

The data comes from a US Military hospital. Is this related to the US Veterans Affairs Healthcare system? Is there more detailed information about the demographics of the patient population?

Facility A is part of the Military Health System (MHS) which provides care for active service members and their families. This is distinct from the US Veterans Affairs Healthcare system. Only limited patient data was accessible to us as this study was done as part of our public health surveillance activities. Patient age (avg. 57.2 +/- 21.0) and gender (ratio male/female 1.7) are provided in the revised manuscript. 

Line 384ff: The origin of infection was inferred based on the SNP threshold and epidemiological links. However, recombination events can complicate the interpretation of SNP data. Have the authors attempted to account for this?

Thank you. We agree that recombination events can complicate the interpretation of SNP data. We used Gubbins v2.3.1 to filter out recombination from the core SNP alignment, as indicated in the revised manuscript.

The authors' definition of environment-to-patient transmission seems conservative (nearly identical strain and no known temporal overlap for > 365 days). Have the authors changed the threshold, performed sensitivity analyses, and tested how this would affect their results?

Indeed, acknowledging that fixed thresholds have limitations in their ability to accurately predict the origin of infections, we took a conservative approach to favor specificity as our goal was simply to establish that cases of environment-to-patient transmission did happen. In the absence of a truth set, we have not performed sensitivity analysis, but we are conducting a follow-up study to compare inferences from MCMC models to our original predictions. This limitation is now discussed in the revised manuscript.

The authors don't seem to incorporate the role of healthcare workers in the transmission process. Could they comment on this? I am assuming that environment-to-patient transmission could either be directly from the environment to the patient or via a healthcare worker. I think it's fine to make simplifying assumptions here but it would be great if this was explicitly described.

Thank you for this suggestion. We have not sampled the hands of healthcare workers in this study. As a result, the reviewer is correct to say that we made the simplifying assumption that healthcare workers would be possible intermediates in either environment-topatient or patient-to-patient transmissions, as previously described by others (PMID: 8452949). This limitation is now discussed in the revised manuscript.

Page 5, line 100: What does "all vs all" mean? Based on the supplement, I assume it's the pairwise distance and then averaged across all of those. It would improve the readability of the manuscript if the authors could briefly define this term and then maybe refer to Table S1.

Thank you. We have created Fig.S2 and revised the manuscript to state that ST-621 isolates from facility A belonged to the same outbreak clone with a distance (averaged all vs all pairwise comparison) of just 38 single nucleotide polymorphisms (SNPs), and an IQR of 19 (Fig. S2, Table S1).

Figure 1D: It would be interesting to see additional figures in the supplement on the percentage of sequenced isolates per year and whether it varies across the different sources/sites. Is there any information on which isolates were chosen for sequencing?

Lack of clarity in the sampling/sequencing scheme was raised by multiple reviewers and we have provided a thorough response to earlier comments. We also have revised the material and methods section accordingly. Finally, we have created Fig. S3 to show the percentage of sequenced isolates per year across different sources/sites, as suggested by the reviewer. No noticeable patterns were observed. 

It seems like only a subset of all clinical isolates were sequenced. Would it be possible that SC2 was present already earlier but not picked up until a certain date?

Although all isolates received by the MRSN were sequenced, compliance varied through time so it is true that not all clinical isolates were sequenced between 2011-2019. As such, we fully agree with this hypothesis and discuss this possibility as BEAST analysis placed the origin of SC2 in 2004 while the first detection of an SC2 isolate was in December 2012. This limitation is now discussed in the revised manuscript.

Could the authors elaborate on whether the isolates resulted from single-colony picks? Is it possible that the different absence of a subclone is due to the fact that they picked only a colony?

Yes, the isolates resulted from single-colony picks except when the presence of different colony morphologies was noted. In the latter, representative isolates for each colony morphologies were processed. We have revised the methods to make that clear.

Figure 2: It is difficult to see which nodes belong to which patient due to the small font size. I wonder if it was possible to color the nodes for each patient, to make it more readable.

We tried coloring the nodes but with > 60 distinct patients/colors we decided it did not improve clarity. We have revised figure 2 to increase the font size.  

Page 7-8, lines 154-155: Did the authors check whether there were isolates of the same strain (that were found in the environment) present in other patients elsewhere in the ward?

Yes. In rare cases, we observed virtually genetically identical isolates from two patients collected in different wards. Because we only have access to clinical isolate data (collected from patient X in ward Y) and do not have access to patient data (admission/discharge date, wards, rooms, etc.), we do not know but cannot exclude that patients overlap in a room prior to the sampling of their P. aeruginosa isolates. We designed our fixed thresholds to be conservative. As a result, in this analysis, these cases are labelled as “undetermined”.  

Page 8: Do the authors have any information on antibiotic use during this timeframe? From the discussion, it seems like there is no patient-level prescription data. Is there any data on overall trends? How were trends in antibiotic use correlated with trends in antibiotic resistance?

Unfortunately, patient-level prescription data (or any other data not linked to the bacterial specimens) was not accessible to us as this study was done as part of our public health surveillance activities.

To infer the origin of infection, the authors used a static method with fixed thresholds and definitions. This study does not provide any uncertainty with their estimates. Maybe the authors could add a sentence in the discussion section that MCMC methods to infer transmission trees incorporating WGS could provide these estimates. These methods have not been applied to PA a lot but two examples where MCMC methods have been used without WGS (though the definition of environmental contamination may differ between these studies and this study).

https://doi.org/10.1186/s13756-022-01095-x

https://doi.org/10.1371/journal.pcbi.1006697

Thank you for this great suggestion. We have revised the manuscript to include a discussion on the limitations of fixed thresholds to infer transmission chains/origins, and to discuss existing alternatives including MCMC methods. 

Line 322-323: This sentence is a bit vague since not all of these HAI are due to P. aeruginosa. I would suggest citing a number that is specific to PA.

Thank you. While our paper shows a particular example of protracted P. aeruginosa outbreak, the roll-out of routine WGS surveillance in the clinic will help prevent hospital-associated drug-resistant infections for more than this species. We believe that broadening the scope in the last sentence of the manuscript is important and we decline to revise as suggested.

It's interesting to me how Eliot ends this section of The Waste Land with Ophelia's last words before she commits suicide. Lines before, we get references to "Bill," "Lou," and "May," indicating that the speaker is bidding farewell from the pub setting. Ophelia's line, on the other hand, bids farewell on behalf of not just Lil and the woman in the pub, but all the "sweet ladies" of the waste land. This idea of death as a fate is super interesting. The women have their emotional and spiritual deaths connected to Ophelia's physical death. This is yet another instance where we see suicide in a female in The Waste Land. If I think about what Eliot is trying to get at with women x waste land, especially with this Ophelia connection, I'd say the waste land is a world where the modes of expressing experiences like song, symbol, and even madness have been stripped of their meaning and beauty, leaving only bad nerves, dirty gossip, and the last call of the pub. This is obviously not the ideal place for women; hence, modern society is not fit for women to flourish.

I agree with this. I am privileged to often forget about the exclusion of certain groups in "universal" designs. An example of this that I thought of was pens. I found out recently that a lot of left-handed people have a hard time with ink pens as there palms tend to smear the wet ink immediately after writing. Another example I could think of were the original Band-Aid colors, and how they did a poor job of representing people of all skin tones. Any design that leaves out a certain group of people should always have a substitute version for those people or should not be designed altogether.

Author response:

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

Reviewer #1 (Public review): 

Summary: 

In this manuscript entitled "Molecular dynamics of the matrisome across sea anemone life history", Bergheim and colleagues report the prediction, using an established sequence analysis pipeline, of the "matrisome" - that is, the compendium of genes encoding constituents of the extracellular matrix - of the starlet sea anemone Nematostella vectensis. Re-analysis of an existing scRNA-Seq dataset allowed the authors to identify the cell types expressing matrisome components and different developmental stages. Last, the authors apply time-resolved proteomics to provide experimental evidence of the presence of the extracellular matrix proteins at three different stages of the life cycle of the sea anemone (larva, primary polyp, adult) and show that different subsets of matrisome components are present in the ECM at different life stages with, for example, basement membrane components accompanying the transition from larva to primary polyp and elastic fiber components and matricellular proteins accompanying the transition from primary polyp to the adult stage. 

Strengths: 

The ECM is a structure that has evolved to support the emergence of multicellularity and different transitions that have accompanied the complexification of multicellular organisms. Understanding the molecular makeup of structures that are conserved throughout evolution is thus of paramount importance. 

The in-silico predicted matrisome of the sea anemone has the potential to become an essential resource for the scientific community to support big data annotation efforts and understand better the evolution of the matrisome and of ECM proteins, an important endeavor to better understand structure/function relationships. This study is also an excellent example of how integrating datasets generated using different -omic modalities can shed light on various aspects of ECM metabolism, from identifying the cell types of origins of matrisome components using scRNA-Seq to studying ECM dynamics using proteomics. 

We greatly appreciate the positive feedback regarding the design of our study and the evolutionary significance of our findings.

Weaknesses: 

My concerns pertain to the three following areas of the manuscript: 

(1) In-silico definition of the anemone matrisome using sequence analysis: 

a) While a similar computational pipeline has been applied to predict the matrisome of several model organisms, the authors fail to provide a comprehensive definition of the anemone matrisome: In the text, the authors state the anemone matrisome is composed of "551 proteins, constituting approximately 3% of its proteome (see page 6, line 14), but Figure 1 lists 829 entries as part of the "curated" matrisome, Supplementary Table S1 lists the same 829 entries and the authors state that "Here, we identified 829 ECM proteins that comprise the matrisome of the sea anemone Nematostella vectensis" (see page 17, line 10). Is the sea anemone matrisome composed of 551 or 829 genes? If we refer to the text, the additional 278 entries should not be considered as part of the matrisome, but what is confusing is that some are listed as glycoproteins and the "new_manual_annotation" proposed by the authors and that refer to the protein domains found in these additional proteins suggest that in fact, some could or should be classified as matrisome proteins. For example, shouldn't the two lectins encoded by NV2.3951 and NV2.3157 be classified as matrisome-affiliated proteins? Based on what has been done for other model organisms, receptors have typically been excluded from the "matrisome" but included as part of the "adhesome" for consistency with previously published matrisome; the reviewer is left wondering whether the components classified as "Other" / "Receptor" should not be excluded from the matrisome and moved to a separate "adhesome" list. 

In addition to receptors, the authors identify nearly 70 glycoproteins classified as "Other". Here, does other mean "non-matrisome" or "another matrisome division" that is not core or associated? If the latter, could the authors try to propose a unifying term for these proteins? Unfortunately, since the authors do not provide the reasons for excluding these entries from the bona fide matrisome (list of excluding domains present, localization data), the reader is left wondering how to treat these entries. 

Overall, the study would gain in strength if the authors could be more definitive and, if needed, even propose novel additional matrisome annotations to include the components for now listed as "Other" (as was done, for example, for the Drosophila or C. elegans matrisomes). 

The reviewer is correct to point out the confusing terminology used throughout our manuscript, where both the total of 829 proteins constituting the curated list of ECM domain proteins and the actual matrisome (excluding "others") were referred to as "matrisomes". In general, we followed the example set by Naba & Hynes in their 2012 paper (Mol Cell Proteomics. 2012 Apr;11(4):M111.014647. doi: 10.1074/mcp.M111.014647), where they define the "matrisome" as encompassing all components of the extracellular matrix ("core matrisome") and those associated with it ("matrisome-associated" proteins). This corresponds to our group of 551 proteins, comprising both core matrisome and matrisomeassociated proteins. The Naba & Hynes paper also contains the inclusive and exclusive domain lists for the matrisome that we applied for our dataset. In the revised manuscript, we have now labelled the group of 829 proteins as "curated ECM domain proteins/genes", which includes all proteins positively selected for containing a bona fide ECM domain. After excluding non-matrisomal proteins such as receptors, we arrive at the 551 proteins that constitute the "Nematostella matrisome". We have maintained this terminology throughout the revised manuscript and have revised Figures 1B and 4B accordingly.

Regarding the category of "other" proteins, which by definition are not part of the matrisome although containing ECM domains, we have taken the reviewer's advice and classified these in more detail. We categorized all receptors as "adhesome" (202 proteins).  The remaining group of “other” secreted ECM domain proteins were then further subcategorized. Those exhibiting significant matches in the ToxProt database were subclassified as "putative venoms" (15 proteins). This group also includes the two lectins (NV2.3951 and NV2.3157), which had been originally shifted to the “other” category due to their classification as venoms. We categorized as “adhesive proteins” (28 proteins) factors such as coadhesins that due to their domain architecture resemble bioadhesive proteins described in proteomic studies of other invertebrate species, such as corals or sponges (see also https://doi.org/10.1016/j.jprot.2022.104506). Further sub-categories are stress/injury response proteins (9 proteins) and ion channels (6 proteins). The remaining 17 proteins were categorized as “uncharacterized ECM domain proteins”. These include highly diverse proteins possessing either single ECM domains or novel domain combinations. We decided to retain those in our dataset as candidates for future functional characterization.

b) It is surprising that the authors are not providing the full currently accepted protein names to the entries listed in Supplementary Table S1 and have used instead "new_manual_annotation" that resembles formal protein names. This liberty is misleading. In fact, the "new_manual_annotation" seems biased toward describing the reason the proteins were positively screened for through sequence analysis, but many are misleading because there is, in fact, more known about them, including evidence that they are not ECM proteins. The authors should at least provide the current protein names in addition to their "new_manual_annotations". 

c) To truly serve as a resource, the Table should provide links to each gene entry in the Stowers Institute for Medical Research genome database used and some sort of versioning (this could be added to columns A, B, or D). Such enhancements would facilitate the assessment of the rigor of the list beyond the manual QC of just a few entries. 

d) Since UniProt is the reference protein knowledge database, providing the UniProt IDs associated with the predicted matrisome entries would also be helpful, giving easy access to information on protein domains, protein structures, orthology information, etc. 

e) In conclusion, at present, the study only provides a preliminary draft that should be more rigorously curated and enriched with more comprehensive and authoritative annotations if the authors aspire the list to become the reference anemone matrisome and serve the community. 

Table S1 has been updated to include links to the respective Stowers Institute IDs (first two columns), as well as SwissProt IDs and current descriptions from both the Stowers Institute (SI) and Swissprot.

In our manual annotations, we prioritized these over automated ones due to the considerable effort invested in examining each sequence individually. The cnidaria-specific minicollagens and NOWA proteins might serve as an example. According to the SI descriptions, the minicollagens are annotated as “keratin-associated protein, predicted or hypothetical protein, collagen-like protein and pericardin”. We classified these as minicollagens on the basis of overall domain architecture and of signature domains and sequence motifs, such as minicollagen cysteine-rich domains (CRDs) and polyproline stretches (doi: 10.1016/j.tig.2008.07.001). NOWA is a CTLD/CRD-containing protein that is part of nematocyst tubules (doi:10.1016/j.isci.2023.106291). The first two NOWA isoforms, according to Si descriptions, were annotated as aggrecan and brevican core proteins, which is very misleading. We therefore feel that our manual annotations better serve the cnidarian research community in classifying these proteins.

Automated annotations of ECM proteins often rely on similarities between individual domains, neglecting overall domain composition. For example, Swissprot descriptions annotate 31 TSP1 domain-containing proteins in our list as "Hemicentin-1", but closer inspection reveals that only one sequence (NV2.24790) qualifies as Hemicentin-1 due to its characteristic vWFA, Ig-like, TSP1, G2 nidogen, and EGF-like domain architecture. Regarding novel protein annotations, NV2.650 might serve as an example. While SI descriptions annotate this protein as "epidermal growth factor" based on the presence of several EGF-like domains, our analysis reveals two integrin alpha N-terminal domains that classify this sequence as integrin-related. We have therefore assigned a description (Secreted integrin-N-related protein) that references this defining domain and avoids misclassification within the EGF family.

In cases where the automated annotation (including those in Genbank) matched our own findings, we adopted the existing description, as seen with netrin-1 (NV2.7734). We acknowledge that our manual annotations are not flawless and will be refined by future research. Nonetheless, we offer them as an approximation to a more accurate definition of the identified protein list.

(2) Proteomic analysis of the composition of the mesoglea during the sea anemone life cycle: 

a) The product of 287 of the 829 genes proposed to encode matrisome components was detected by proteomics. What about the other ~550 matrisome genes? When and where are they expressed? The wording employed by the authors (see line 11, page 13) implies that only these 287 components are "validated" matrisome components. Is that to say that the other ~550 predicted genes do not encode components of the ECM? This should be discussed. 

Obviously, our wording was not sufficiently accurate here. In the revised Fig. 1B we indicated that 210 of the 551 matrisome (core and associated) proteins were confirmed by mass spectrometry. In total, 287 proteins were identified by mass spectrometry, meaning that 77 of those are non-matrisomal proteins belonging to the “adhesome” (47) and “other” (30) groups. The fact that the remaining 542 proteins of the matrisome predicted by our in silico analysis could not be identified has two major reasons: (1) Our study was focussed on the molecular dynamics of the mesoglea. Therefore, only mesogleas were isolated for the mass spectrometry analysis and nematocysts were mostly excluded by extensive washing steps. As nematocysts contribute significantly to the predicted matrisome, this group of proteins is underrepresented in the mass spectrometry analysis. (2) A significant fraction of the predicted ECM proteins constitutes soluble factors and transmembrane receptors. These might not be necessarily part of the mesoglea isolates. In addition, the isolation and solubilization method we applied might have technical limitations. Although we used harsh conditions for solubilizing the mesoglea samples (90°C and high DTT concentrations), we cannot exclude that we missed proteins which resisted solubilization and thus trypsinization. We confirmed that all genes predicted by the in silico analysis have transcriptomic profiles as demonstrated in supplementary table S4. We have clarified these points in the revised results part (p.6) and also revised the statement in line 16, page 13.

b) Can the authors comment on how they have treated zero TMT values or proteins for which a TMT ratio could not be calculated because unique to one life stage, for example? 

We did not include these proteins in the analysis of the respective statistical comparison. This involved only very few proteins (about 10).  

c) Could the authors provide a plot showing the distribution of protein abundances for each matrisome category in the main figure 4? In mammals, the bulk of the ECM is composed of collagens, followed by fibrillar ECM glycoproteins, the other matrisome components being more minor. Is a similar distribution observed in the sea anemone mesoglea? 

We have included such a plot showing protein abundances across life stages and protein categories (Fig. 4A). Collagens and basement membrane proteoglycans (perlecan) are the most abundant protein categories in the core matrisome while secreted factors dominate in the matrisome-associated group.

d) Prior proteomic studies on the ECM of vertebrate organisms have shown the importance of allowing certain post-translational modifications during database search to ensure maximizing peptide-to-spectrum matching. Such PTMs include the hydroxylation of lysines and prolines that are collagen-specific PTMs. Multiple reports have shown that omitting these PTMs while analyzing LC-MS/MS data would lead to underestimating the abundance of collagens and the misidentification of certain collagens. The authors may want to reanalyze their dataset and include these PTMs as part of their search criteria to ensure capturing all collagen-derived peptides. 

Thank you for this suggestion. We have re-analyzed our dataset including lysine and proline hydroxylation as PTM. While we obtained in total 70 more proteins using this approach, this additional group did not contain any large collagen or minicollagen we had not detected before. We only obtained two additional collagen-like proteins with very short triple helical domains (V2t013973001.1, NV2t024002001.1), one being a fragment. We don’t feel this justifies implementing a re-analysis of the proteome in our study.

e) The authors should ensure that reviewers are provided with access to the private PRIDE repository so the data deposited can also be evaluated. They should also ensure that sufficient meta-data is provided using the SRDF format to allow the re-use of their LCMS/MS datasets. 

We apologize for not providing the reviewer access in our initial submission and have asked the editorial office to forward the PRIDE repository link to all reviewers immediately after receiving the reviews. We did upload a metadata.csv file with the proteomics dataset. This file contains an annotation of all TMT labels to the samples and conditions and replicates used in the manuscript. It contains similar information as an SRDF format file. In addition, the search output files on protein and psm level have been provided. So, from our point of view, we provided all necessary information to reproduce the analysis.

(3) Supplementary tables: 

The supplementary tables are very difficult to navigate. They would become more accessible to readers and non-specialists if they were accompanied by brief legends or "README" tabs and if the headers were more detailed (see, for example, Table S2, what does "ctrl.ratio_Larvae_rep2" exactly refer to? Or Table S6 whose column headers using extensive abbreviations are quite obscure). Similarly, what do columns K to BX in Supplementary Table S1 correspond to? Without more substantial explanations, readers have no way of assessing these data points. 

We have revised the tables and removed any redundant data columns. We also included detailed explanations of the used abbreviations, both in the headers and in a separate README file. Some of the information was apparently lost during the conversion to pdf files. We will therefore upload the original .xls files when submitting the revised manuscript.

Reviewer #2 (Public review): 

This work set out to identify all extracellular matrix proteins and associated factors present within the starlet sea anemone Nematostella vectensis at different life stages. Combining existing genomic and transcriptomic datasets, alongside new mass spectometry data, the authors provide a comprehensive description of the Nematostella matrisome. In addition, immunohistochemistry and electron microscopy were used to image whole mount and decellularized mesoglea from all life stages. This served to validate the de-cellularization methods used for proteomic analyses, but also resulted in a very nice description of mesoglea structure at different life stages. A previously published developmental cell type atlas was used to identify the cell type specificity of the matrisome, indicating that the core matrisome is predominantly expressed in the gastrodermis, as well as cnidocytes. The analyses performed were rigorous and the results were clear, supporting the conclusions made by the authors. 

Thank you. We greatly appreciate the positive assessment of our study.

Reviewer #3 (Public review): 

Summary: 

This manuscript by Bergheim et al investigates the molecular and developmental dynamics of the matrisome, a set of gene products that comprise the extracellular matrix, in the sea anemone Nematostella vectensis using transcriptomic and proteomic approaches. Previous work has examined the matrisome of the hydra, a medusozoan, but this is the first study to characterize the matrisome in an anthozoan. The major finding of this work is a description of the components of the matrisome in Nematostella, which turns out to be more complex than that previously observed in hydra. The authors also describe the remodeling of the extracellular matrix that occurs in the transition from larva to primary polyp, and from primary polyp to adult. The authors interpret these data to support previously proposed (Steinmetz et al. 2017) homology between the cnidarian endoderm with the bilaterian mesoderm. 

Strengths: 

The data described in this work are robust, combining both transcriptome and proteomic interrogation of key stages in the life history of Nematostella, and are of value to the community. 

Thank you for your positive assessment of our dataset. 

Weaknesses: 

The authors offer numerous evolutionary interpretations of their results that I believe are unfounded. The main problem with extending these results, together with previous results from hydra, into an evolutionary synthesis that aims to reconstruct the matrisome of the ancestral cnidarian is that we are considering data from only two species. I agree with the authors' depiction of hydra as "derived" relative to other medusozoans and see it as potentially misleading to consider the hydra matrisome as an exemplar for the medusozoan matrisome. Given the organismal and morphological diversity of the phylum, a more thorough comparative study that compares matrisome components across a selection of anthozoan and medusozoan species using formal comparative methods to examine hypotheses is required. 

Specifically, I question the author's interpretation of the evolutionary events depicted in this statement: 

"The observation that in Hydra both germ layers contribute to the synthesis of core matrisome proteins (Epp et al. 1986; Zhang et al. 2007) might be related to a secondary loss of the anthozoan-specific mesenteries, which represent extensions of the mesoglea into the body cavity sandwiched by two endodermal layers." 

Anthozoans and medusozoans are evolutionary sisters. Therefore, the secondary loss of "anthozoan-like mesenteries" in hydrozoans is at least as likely as the gain of this character state in anthozoans. By extension, there is no reason to prefer the hypothesis that the state observed in Nematostella, where gastroderm is responsible for the synthesis of the core matrisome components, is the ancestral state of the phylum. Moreover, the fossil evidence provided in support of this hypothesis (Ou et al. 2022) is not relevant here because the material described in that work is of a crown group anthozoan, which diversified well after the origin of Anthozoa. The phylogenetic structure of Cnidaria has been extensively studied using phylogenomic approaches and is generally well supported (Kayal et al. 2018; DeBiasse et al. 2024). Based on these analyses, anthozoans are not on a "basal" branch, as the authors suggest. The structure of cnidarian phylogeny bifurcates with Anthozoa forming one clade and Medusozoa forming the other. From the data reported by Bergheim and coworkers, it is not possible to infer the evolutionary events that gave rise to the different matrisome states observed in Nematostella (an anthozoan) and hydra (a medusozoan). Furthermore, I take the observation in Fig 5 that anthozoan matrisomes generally exhibit a higher complexity than other cnidarian species to be more supportive of a lineage-specific expansion of matrisome components in the Anthozoa, rather than those components being representative of an ancestral state for Cnidaria. Whatever the implication, I take strong issue with the statement that "the acquisition of complex life cycles in medusozoa, that are distinguished by the pelagic medusa stage, led to a secondary reduction in the matrisome repertoire." There is no causal link in any of the data or analyses reported by Bergheim and co-workers to support this statement and, as stated above, while we are dealing with limited data, insufficient to address this question, it seems more likely to me that the matrisome expanded in anthozoans, contrasting with the authors' conclusions. While the discussion raises many interesting evolutionary hypotheses related to the origin of the cnidarian matrisome, which is of vital interest if we are to understand the origin of the bilaterian matrisome, a more thorough comparative analysis, inclusive of a much greater cnidarian species diversity, is required if we are to evaluate these hypotheses. 

DeBiasse MB, Buckenmeyer A, Macrander J, Babonis LS, Bentlage B, Cartwright P, Prada C, Reitzel AM, Stampar SN, Collins A, et al. 2024. A Cnidarian Phylogenomic Tree Fitted With Hundreds of 18S Leaves. Bulletin of the Society of Systematic Biologists [Internet] 3. Available from: https://ssbbulletin.org/index.php/bssb/article/view/9267

Epp L, Smid I, Tardent P. 1986. Synthesis of the mesoglea by ectoderm and endoderm in reassembled hydra. J Morphol [Internet] 189:271-279. Available from: https://pubmed.ncbi.nlm.nih.gov/29954165/ 

Kayal E, Bentlage B, Sabrina Pankey M, Ohdera AH, Medina M, Plachetzki DC, Collins AG, Ryan JF. 2018. Phylogenomics provides a robust topology of the major cnidarian lineages and insights on the origins of key organismal traits. BMC Evol Biol [Internet] 18:1-18. Available from: https://bmcecolevol.biomedcentral.com/articles/10.1186/s12862-018-1142-0

Ou Q, Shu D, Zhang Z, Han J, Van Iten H, Cheng M, Sun J, Yao X, Wang R, Mayer G. 2022. Dawn of complex animal food webs: A new predatory anthozoan (Cnidaria) from Cambrian. The Innovation 3:100195 

Steinmetz PRH, Aman A, Kraus JEM, Technau U. 2017. Gut-like ectodermal tissue in a sea anemone challenges germ layer homology. Nature Ecology & Evolution 2017 1:10 [Internet] 1:1535-1542. Available from: https://www.nature.com/articles/s41559-017-0285-5

Zhang X, Boot-Handford RP, Huxley-Jones J, Forse LN, Mould AP, Robertson DL, Li L, Athiyal M, Sarras MP. 2007. The collagens of hydra provide insight into the evolution of metazoan extracellular matrices. J Biol Chem [Internet] 282:6792-6802. Available from: https://pubmed.ncbi.nlm.nih.gov/17204477/ 

We agree with the reviewer that only the analysis of several additional anthozoan and medusozoan representatives will yield a valid basis for a reconstruction of the ancestral cnidarian matrisome and allow statements about ancestral or novel features within the phylum. We have therefore revised our statements in the discussion part of the manuscript by implementing the cited literature and also findings from medusozoan genome analysis (e.g. Gold et al., 2018) demonstrating that changes in gene content are as common in the anthozoans as in medusozoans, which questioned the previously stated “basal” state of Nematostella or of anthozoans in general.

Reviewer #1 (Recommendations for the authors): 

(1) In Figure 2A, an "o" is missing in the labeling of the "developing cnidcytes" population. 

Thank you, we have corrected the typo.

(2) It would be helpful to have the different life stages indicated as headers of the heat maps presented in Figure 4. 

We have included symbolic representations for the different life stages on top of the heat maps in addition to the respective labels at the bottom.

Reviewer #2 (Recommendations for the authors): 

Important changes: 

(1) Figure 2B The x-axis tissue names should be changed to something more easily readable/understandable - some are clear, but others are not. Perhaps abbreviations could be expanded in the legend. 

We have expanded the legend in Fig. 2B to render it more easily readable. We have also rotated the maps in A to have them aligned with the ones in Fig.3B.

(2) Figure 3B This figure would be improved by the inclusion of cluster names, to understand better the mapping. 

We have added relevant cluster names to Fig. 3B and as stated above aligned the orientation of the maps in Fig. 2B and Fig. 3B.

(3) Figure 3C As with 2B, I find the y-axis cnidocyte cell state names to be unclear at times. Perhaps abbreviations could be expanded in the legend. 

All abbreviations were expanded in Fig.3C axis labels.

(4) Many of the supplementary tables are not well exported or easily readable as is (gene names are truncated, headers truncated, etc), which means that they may not be easily usable by researchers in the field interested in following up on this work in other contexts. Indeed, to be more usable, please consider sharing these supplementary data as .csv files, for example, instead of as .pdfs. 

We are sorry for this inconvenience, which was obviously caused by the conversion to pdf files. We will upload the original csv files when submitting the revised manuscript.

Smaller nitpicky comments: 

(5) Page 2 line 4 & page 3 line 7: Please consider a term other than "pre-bilaterian". The drawing/ordering of a phylogeny of extant species is not meaningful in terms of more or less ancestral. e.g. if the tips are flipped in the drawing of the tree, can we say that bilaterians are pre-cnidarians? What does that mean? 

We have used that term on the basis that cnidarians existed before the appearance of bilaterians according to the fossil record and molecular phylogenies (McFadden et al., 2021; Adoutte et al., 2000;Cavalier-Smith et al., 1996; Collins, 1998; Kim et al., 1999; Medina et al., 2001; Wainright et al., 1993). To acknowledge remaining uncertainties in the timing of origin of animals, we will use the term “early-diverging metazoans” instead, which is widely accepted in the cnidarian community. 

(6) Page 3 line 9 I was confused by the use of "gastrula-shaped body" to describe cnidarians, which are on the whole very morphologically diverse and don't all resemble gastrulae (that can also be quite diverse). 

This term is sometimes used to refer to the diploblastic cnidarian body plan (outer ectoderm, inner endoderm) with a mouth that corresponds to the blastopore. To avoid misunderstandings, we changed it in the revised manuscript to “Cnidarians, the sister group to bilaterians, are characterized by a simple body plan with a central body cavity and a mouth opening surrounded by tentacles.”

Reviewer #3 (Recommendations for the authors): 

(1) In general, I felt there was a lot of discussion about protein structure and diversity that is difficult to follow without a figure. I think some of the information in Supplementary Figures S5, S9, and S11 should be in the main figures. 

Following the reviewer’s suggestion, we have integrated Fig. S5 (collagens) into the main Fig. 2 and Fig. S9 (polydoms) into Fig. 4. As metalloproteases are not extensively discussed in the manuscript (and also due to the large size of the figure) we have kept Fig. S11 as a supplementary figure.

(2) Page 3, Line 7: The use of the term "pre-bilaterian" is inappropriate. Cnidarians and bilaterians are evolutionary sisters. Therefore, each lineage derives from the same split and is the same age. The cnidarian lineage is not older than the bilaterian lineage. 

Following a similar request by reviewer 2 we have replaced this term by “early diverging metazoans”.

(3) Page 5, Line 10. How were in silico matrisomes from early-branching metazoan species predicted? 

We applied the same bioinformatic pipeline as for the Nematostella matrisome. We clarified this in the respective methods part.

(4) Page 16, Line 8: This should be Thus. 

Obviously, the wording of this sentence was ambiguous. We changed it to ”In contrast, the adult mesoglea is significantly enriched in elastic fiber components, such as fibrillins and fibulin. This compositional shift likely adds to the visco-elastic properties (Gosline 1971a, b) of the growing body column (Fig. 4B,D, supplementary table S7).”

Author response:

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

Reviewer 1:

While BAP1 mutant UM cell lines were included for some of the experiments, it seems the in-vivo data mentioned in the response to the reviewers comment is missing? The authors stated that "MP46 (Supplementary Fig. 3a) is BAP1-null uveal melanoma cell line with no detectable protein expression (Amirouchene-Angelozzi et al., Mol Oncol 2014), and we have observed strong tumor growth inhibition in this CDX model with our BAF ATPase inhibitor." But the CDX model data shown in Figure 4 is from 92.1 cells. If this data is available, then the manuscript would benefit from its addition.

We thank the reviewer for bringing this to our attention. As the reviewer mentioned, we show 92-1 CDX model in our manuscript. Additionally, strong tumor growth inhibition in MP-46  CDX model treated with our BAF ATPase inhibitor can be found in Vaswani et al., 2025 (PMID:39801091, https://pubmed.ncbi.nlm.nih.gov/39801091/).

Reviewer 3:<br /> Supplementary Figure 2C<br /> Is the T910M mutation in the parental MP41 cells heterozygous? If so, the authors should indicate this in the figure legend. If this is a homozygous mutation, the authors should explain how the inhibitors suppress SMARCA4 activity in cells that have a LOF mutation.

We thank the reviewer for bringing this to our attention. We updated the figure legend accordingly to reflect the genotype of the mutations highlighted in the table.

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

Reviewer #1 (Public Review):

Summary:

The presented study by Centore and colleagues investigates the inhibition of BAF chromatin remodeling complexes. The study is well-written, and includes comprehensive datasets, including compound screens, gene expression analysis, epigenetics, as well as animal studies. This is an important piece of work for the uveal melanoma research field, and sheds light on a new inhibitor class, as well as a mechanism that might be exploited to target this deadly cancer for which no good treatment options exist.

Strengths:

This is a comprehensive and well-written study.

Weaknesses:

There are minimal weaknesses.

We thank the reviewer for the positive comments.

Reviewer #2 (Public Review):

Summary:

The authors generate an optimized small molecule inhibitor of SMARCA2/4 and test it in a panel of cell lines. All uveal melanoma (UM) cell lines in the panel are growth-inhibited by the inhibitor making the focus of the paper. This inhibition is correlated with the loss of promoter occupancy of key melanocyte transcription factors e.g. SOX10. SOX10 overexpression and a point mutation in SMARCA4 can rescue growth inhibition exerted by the SMARCA2/4 inhibitor. Treatment of a UM xenograft model results in growth inhibition and regression which correlates with reduced expression of SOX10 but not discernible toxicity in the mice. Collectively the data suggest a novel treatment of uveal melanoma.

Strengths:

There are many strengths of the study including the strong challenge of the on-target effect, the assays used, and the mechanistic data. The results are compelling as are the effects of the inhibitor. The in vivo data is dose-dependent and doses are low enough to be meaningful and associated with evidence of target engagement.

Weaknesses:

The authors introduce the field stating that SMARCA4 inhibitors are more effective in SMARCA2 deficient cancers and the converse. Since the desirable outcome of cancer therapy would be synthetic lethality it is not clear why a dual inhibitor is desirable. Wouldn't this be associated with more side effects? It is not known how the inhibitor developed here impacts normal cells, in particular T cells which are essential for any durable response to cancer therapies in patients. Another weakness is that the UM cell lines used do not molecularly resemble metastatic UM. These UM most frequently have mutations in the BAP1 tumor suppressor gene. It is not clear if the described SMARCA2/4 inhibitor is efficacious in BAP1 mutant UM cell lines in vitro or BAP1 mutant patient-derived xenografts in vivo.

We thank the reviewer for their insightful and constructive comments. As we demonstrate in Fig. 1d, uveal melanoma cells are selectively and deeply sensitive to BAF ATPase inhibition, and provides a therapeutic window. This is confirmed in Fig. 4a-c, as we demonstrated robust tumor growth inhibition, achieved at a dose well-tolerated in xenograft study. FHD-286, a dual BRM/BRG1 inhibitor similar to FHT-1015 with optimized physical properties, has been evaluated in a Phase I trial in patients with metastatic uveal melanoma (NCT04879017) and manuscript describing results of this clinical trial is currently in preparation.

As the reviewer mentioned, BAP1 loss is a signature of metastatic uveal melanoma. MP38 is a BAP1 mutant uveal melanoma cell line, and we demonstrated growth inhibition and robust caspase 3/7 activity in response to FHT-1015 (Supplementary Fig. 3a and 3f). MP46 (Supplementary Fig. 3a) is BAP1-null uveal melanoma cell line with no detectable protein expression (Amirouchene-Angelozzi et al., Mol Oncol 2014), and we have observed strong tumor growth inhibition in this CDX model with our BAF ATPase inhibitor.

Reviewer #3 (Public Review):

Summary:

This manuscript reports the discovery of new compounds that selectively inhibit SMARCA4/SMARCA2 ATPase activity that work through a different mode as previously developed SMARCA4/SMARCA2 inhibitors. They also demonstrate the anti-tumor effects of the compounds on uveal melanoma cell proliferation and tumor growth. The findings indicate that the drugs exert their effects by altering chromatin accessibility at binding sites for lineage-specific transcription factors within gene enhancer regions. In uveal melanoma, altered expression of the transcription factor, SOX10, and SOX10 target gene underlies the anti-proliferative effects of the compounds. This study is significant because the discovery of new SMARCA4/SMARCA2 inhibitory compounds that can abrogate uveal melanoma tumorigenicity has therapeutic value. In addition, the findings provide evidence for the therapeutic use of these compounds in other transcription factor-dependent cancers.

Strengths:

The strengths of this manuscript include biochemical evidence that the new compounds are selective for SMARCA4/SMARCA2 over other ATPases and that the mode of action is distinct from a previously developed compound, BRM014, which binds the RecA lobe of SMARCA2. There is also strong evidence that FHT1015 suppresses uveal melanoma proliferation by inducing apoptosis. The in vivo suppression of tumor growth without toxicity validates the potential therapeutic utility of one of the new drugs. The conclusion that FHT1015 primarily inhibits SMARCA4 activity and thereby suppresses chromatin accessibility at lineage-specific enhancers is substantiated by ATAC-seq and ChIP-seq studies.

Weaknesses:

The weaknesses include a lack of more precise information on which SMARCA4/SMARCA2 residues the drugs bind. Although the I1173M/I1143M mutations are evidence that the critical residues for binding reside outside the RecA lobe, this site is conserved in CHD4, which is not affected by the compounds. Hence, this site may be necessary but not sufficient for drug binding or specifying selectivity. A more precise evaluation of the region specifying the effect of the new compounds would strengthen the evidence that they work through a novel mode and that they are selective. Another concern is that the mechanisms by which FHT1015 promotes apoptosis rather than simply cell cycle arrest are not clear. Does SOX10 or another lineage-specific transcription factor underlie the apoptotic effects of the compounds?

We thank the reviewer for the valuable comments.

We believe that our dual ATPase inhibitor is selective and additional insights into binding specificity and selectivity for earlier stage compounds of this series were recently published in Vaswani et al., 2025 (PMID:39801091, https://pubmed.ncbi.nlm.nih.gov/39801091/).

The reviewer also poses a great question regarding the mechanism of apoptosis. The mechanism of apoptosis is extremely complex, but we observed a decrease in pro-survival BCL-2 protein expression in response to FHT-1015, in the experiment corresponding to Supplementary Fig. 5e. In the experiment described in Fig. 3k, we also monitored caspase 3/7 activity over time, and SOX10 overexpression rescued 92-1 cells from FHT-1015 induced apoptosis. This suggests the role of SOX10 as an important mediator of response to BAF ATPase inhibition, including apoptosis induced by FHT-1015.

Additional Reviews:

The referees would like to draw the authors' attention to the following issues that would best benefit from additional revision. 

The clinical relevance of the study would be strengthened by the use of uveal melanoma cell lines with BAP1 mutations that better represent metastatic uveal melanoma. The use of patient-derived xenografts would also be pertinent and would be a useful addition. Similarly, attention to the effects of the inhibitor on non-cancerous proliferative cells such as blood/T/immune cells would also strengthen the manuscript. As the study reports the administration of one of the inhibitors in mice for the xenograft experiments, it would be important to assess any potential effects on blood cell counts and better discuss the eventual toxicity or lack of toxicity and how it was assessed. 

The authors should better explain how SOX10 over expression can rescue viability in the presence of the inhibitor. Similarly given the critical roles of BRG1, SOX10, and MITF in cutaneous melanoma some specific discussion on the sensitivity of cutaneous melanoma cells to the inhibitor should be considered, and potential differences with uveal melanoma highlighted. 

Aside from these issues, the authors are urged to consider the other points mentioned below. 

Reviewer #1 (Recommendations For The Authors): 

Figure 1d, as well as the text in the manuscript referring to this figure, would benefit from indicating specific cell lines used for UM. The same for the sentence in line 153. 

We thank the reviewer for bringing this to our attention. We have added the cell line names and updated the manuscript accordingly.

For any of the studies conducted, is there any link with the genetics of UM? E.g. BAP1 wildtype/BAP1 mutant? 

As addressed above in the public review section, MP38 is a BAP1 mutant uveal melanoma cell line, and we demonstrated growth inhibition and robust caspase 3/7 activity in response to FHT-1015 (Supplementary Fig. 3a and 3f). MP46 (Supplementary Fig. 3a) is BAP1-null uveal melanoma cell line with no detectable protein expression (Amirouchene-Angelozzi et al., Mol Oncol 2014), and we have observed strong tumor growth inhibition in this CDX model with our BAF ATPase inhibitor.

Row 191 - How were peaks classified as enhancer-occupied? 

We used annotatePeaks function of HOMER package to annotate genomic locations, as well as H3K27ac ChIP-seq to annotate peaks as enhancer-occupied. We thank the reviewer to pointing it out and have updated the manuscript accordingly to include this information.

Row 259, the two cell lines should be named, also in Figure 3i. 

We have added the cell line names and updated the manuscript accordingly.

Reviewer #2 (Recommendations For The Authors): 

As a proof of concept, this study is truly excellent and the authors should be commended. However, it is desirable that new knowledge in cancer is translated to the clinic. To this end there are a few things needed to strengthen the study. 

I am rephrasing my statements from the public review to say that I would recommend testing the inhibitor in T cells (side effects) and BAP1 mutant cell lines (for clinical relevance). 

As addressed in the public review section, MP38 is a BAP1 mutant uveal melanoma cell line, and we demonstrated growth inhibition and robust caspase 3/7 activity in response to FHT-1015 (Supplementary Fig. 3a and 3f). MP46 (Supplementary Fig. 3a) is BAP1-null uveal melanoma cell line with no detectable protein expression (Amirouchene-Angelozzi et al., Mol Oncol 2014), and we have observed strong tumor growth inhibition in this CDX model with our BAF ATPase inhibitor.

Regarding concerns for any potential side effect on T cells, we observed an increase in both CD4 and CD8 T-cell populations in the peripheral blood and the spleen, when naïve, non-tumor bearing CD-1 mice were dosed with SMARCA2/4 dual ATPase inhibitor FHD-286 once daily for 14 days. FHD-286 is a compound similar to FHT-1015 described in Vaswani et al., 2025 (PMID:39801091, https://pubmed.ncbi.nlm.nih.gov/39801091/). In addition, FHD-286 has been tested in tumor bearing syngeneic models. When B16F10 tumor bearing C57BL/6 were dosed with FHD-286 for 10 days, we observed an increase in CD69+ activated CD8 T-cell infiltration in the tumor microenvironment (doi:10.1136/jitc-2022-SITC2022.0888).

Reviewer #3 (Recommendations For The Authors): 

(1) Determine drug binding by crystal structure or generate additional SMARCA4 or SMARCA2 mutations in the region near I1173/I1143 that are not conserved in CHD4 and test them in an ATPase assay for effects on drug inhibition. For example, Q1166 in SMARCA4 and Q1136 in SMARCA4 could be changed to Alanine as in CHD4. Would this abrogate drug inhibition? 

We believe that our dual ATPase inhibitor is selective and additional insights into binding specificity and selectivity for earlier stage compounds of this series were recently published in Vaswani et al., 2025 (PMID:39801091, https://pubmed.ncbi.nlm.nih.gov/39801091/).

(2) The finding that SOX10 can rescue the antiproliferative effects of FHT1015 suggests that SMARCA4 is primarily needed for SOX10 expression. However, the co-occupancy of SMARCA4 and SOX10 at enhancers suggests that they cooperate to promote chromatin accessibility. It is unclear how over-expression of SOX10 can promote chromatin accessibility in drug-inhibited cells since SOX10 does not have chromatin remodeling activity. ATAC-seq in cells over-expressing SOX10 and treated with the drug could identify SOX10-dependent targets that do not require SMARCA4 activity and clarify the mechanism. It would also be informative to determine if SOX10 over-expression abrogates the effects of FHT1015 on both cell cycle and apoptosis, helping to resolve whether it is a partial or complete rescue of proliferation. 

We agree that running ATAC-seq in cells overexpressing SOX10 would clarify this mechanism. However, shifts in corporate strategy deprioritized any further experiments for this project. One potential mechanism that SOX10 overexpression can partially rescue BAF inhibition phenotype is through overexpressed SOX10 localizing to open chromatin regions (mostly promoters) across the genome. We know from our ATAC-seq data (Fig. 2) that BAF inhibition leads to loss of chromatin accessibility at SOX10 enhancer sites, while promoter regions are only partially affected. Therefore, we think that overexpression of SOX10 would allow upregulation of its target genes via binding to the promoter regions. In this model, the enhancer-driven SOX10 target genes are likely to remain silenced.  

(3) Although the in vivo studies indicate that the drugs are well-tolerated, additional in vitro studies to determine the effects of the drug on the proliferation/survival of non-cancerous cells would further validate their therapeutic utility.

Author Response: The reviewer raises a critical question. FHD-286, a dual BRM/BRG1 inhibitor similar to FHT-1015 with optimized physical properties, has been evaluated in a Phase I trial in patients with metastatic uveal melanoma (NCT04879017), and it was well tolerated at continuous daily dose of up to 7.5 mg QD and at intermittent dose of up to 17.5 mg QD.  Manuscript describing results of this clinical trial is currently in preparation.

Author response:

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_max 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_max  is set, or would be set, by the procedure of Siljestam and Rueffler for different parameter values.  In another section of this response I will describe how to do this with the simulation code written and used by Siljestam and Rueffler; doing so confirms the value that I obtained with my own code.  Furthermore, I will now give a theoretical derivation of this factor.

As specified by Siljestam and Rueffler, the positions of the m pathogens in (m-1)-dimensional antigenic space correspond to the vertices of a regular simplex centered at the origin, with distance between vertices equal to 1.  The squared distance from the origin to each of the m vertices of such a simplex is (m-1)/2m (https://polytope.miraheze.org/wiki/Simplex).  Thus, the sum of the m squared distances is (m-1)/2.  For the (0, 0) homozygote, condition is multiplied by a factor of exp(-(vr)²/2) for each pathogen, where r is the distance from the origin.  It follows that, with v=20, all the pathogens together decrease condition by a factor of exp(20²∙(m-1)/4) = exp(100∙(m-1)).  Thus, increasing or decreasing m by 1 changes this value by a factor of exp(100) = 2.7∙10⁴³.

This begs the conclusion that the branching remains robust to changes in c_max that span 4 decades as well.

That shows only that the results are not extremely sensitive to c_max 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_max a change large enough to have a major effect on the results.

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.

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 will therefore describe how my conclusions about sensitivity to parameter values can be verified using the simulation code provided by Siljestam and Rueffler themselves, with only small, easily understood modifications.  I will consider adding this description as a supplement when I revise the manuscript.

The starting point is the Matlab file MHC_sim_Dryad.m, available at https://doi.org/10.5061/dryad.69p8cz98j.  First, we can add a line that prints the value of the variable logcmax, which represents the natural logarithm of cmax determined and used by the code.  Below line 116 (‘prework’), add the line ‘logcmax’ (with no semicolon).

Now, at the Matlab prompt, execute MHC_sim_Dryad(false, 8, 20, 1) to run the simulation for the Gaussian model with m=8, v=20, and K=1.  The output will indicate that logcmax=700, in accord with the theoretical factor exp(100*(m-1)) derived above.  The allelic diversity, n_e, will rise to a steady state-level of about 140, as in the red curve of my Fig. 2.

Now lower m to 7, i.e,  run MHC_sim_Dryad(false, 7, 20, 1).  The output will indicate that logcmax=600.  This confirms that lowering m by 1 causes the code to lower the value of c_max by a factor exp(100)=2.7∙10⁴³, which must also be the factor by which the condition of the most fit homozygote would increase without this adjustment.

With the change of m to 7 and the compensatory change in c_max, steady-state allelic diversity remains high.  But what if m changes but c_max remains the same, as it would in reality?

To find out, we can fix the value of c_max to the value used with m=8 by adding the following line below the line previously added: ‘logcmax = 700’.  With this additional modification in place, executing MHC_sim_Dryad(false, 7, 20, 1) confirms that without a compensatory change to c_max, lowering m from 8 to 7 mostly eliminates allelic diversity, in accord with the corresponding curve in my Fig. 2.  Similarly, raising m from 8 to 9, or changing v from 20 to 19.5 or 20.5 (executing MHC_sim_Dryad(false, 8, 19.5, 1) or MHC_sim_Dryad(false, 8, 20.5, 1)), largely eliminates diversity, confirming the other results in my Fig. 2.  Results for the bitstring model can also be confirmed, though this requires additional changes to the code.

Thus, the extreme sensitivity of the results of Siljestam and Rueffler to parameter values can be verified with 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”.

Response to 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, 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_max.  Rather, they describe the adjustment of c_max (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_max 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 had hoped that the final paragraph of the Discussion would make the basis for the title clear.  I will consider whether this can be clarified in a revision.

The key to this is there are different types of writing assignments that has in the common writing assignments.

Author response:

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

Reviewer #1 (Public review):

This work computationally characterized the threat-reward learning behavior of mice in a  recent study (Akiti et al.), which had prominent individual differences. The authors  constructed a Bayes-adaptive Markov decision process model and fitted the behavioral data  by the model. The model assumed (i) hazard function starting from a prior (with free mean  and SD parameters) and updated in a Bayesian manner through experience (actually no real  threat or reward was given in the experiment), (ii) risk-sensitive evaluation of future  outcomes (calculating lower 𝛼 quantile of outcomes with free 𝛼 parameter), and (iii) heuristic  exploration bonus. The authors found that (i) brave animals had more widespread hazard  priors than timid animals and thereby quickly learned that there was in fact little real threat,  (ii) brave animals may also be less risk-aversive than timid animals in future outcome  evaluation, and (iii) the exploration bonus could explain the observed behavioral features,  including the transition of behavior from the peak to steady-state frequency of bout. Overall,  this work is a novel interesting analysis of threat-reward learning, and provides useful  insights for future experimental and theoretical work. However, there are several issues that I  think need to be addressed.

Strengths:

(1) This work provides a normative Bayesian account for individual differences in  braveness/timidity in reward-threat learning behavior, which complements the analysis by  Akiti et al. based on model-free threat reinforcement learning.

(2) Specifically, the individual differences were characterized by (i) the difference in the  variance of hazard prior and potentially also (ii) the difference in the risk-sensitivity in the  evaluation of future returns.

Weakness:

(1) Theoretically the effect of prior is diluted over experience whereas the effect of biased  (risk-aversive) evaluation persists, but these two effects could not be teased apart in the  fitting analysis of the current data.

(2) It is currently unclear how (whether) the proposed model corresponds to neurobiological ( rather than behavioral) findings, different from the analysis by Akiti et al.

We thank reviewer #1 for their useful feedback which we’ve used to improve the discussion,  formatting and clarity of the paper, and for highlighting important questions for future  extensions of our work.

Major points:

(1) Line 219

It was assumed that the exploration bonus was replenished at a steady rate when the animal  was at the nest. An alternative way would be assuming that the exploration bonus slowly  degraded over time or experience, and if doing so, there appears to be a possibility that the  transition of the bout rate from peak to steady-state could be at least partially explained by  such a decrease in the exploration bonus.

Section 2.2.3 explains the mechanism of the exploration bonus which motivates approach.  We think that the mechanism suggested by the reviewer is, in essence, what is happening in  the model. The exploration pool is indeed depleted over time or bouts of experience at the  object. In the peak confident phase for brave animals and the peak cautious phase for timid  animals, the rate of depletion exceeds the rate of regeneration, since the agent spends only  a single turn at the nest between bouts. In the steady-state phase, the exploration pool has  depleted so much previously that the agent must wait multiple turns at the nest for the pool  to regenerate to a sufficiently high value to justify approaching the object again.

We have updated section 2.2.3 to explain that agents spend one turn at the nest during peak  phase but multiple turns during steady-state phase. Hopefully, this makes our mechanism  clear:

“In simulations, when 𝐺(𝑡) is high, the agent has a high motivation to explore the object,  spending only a single turn in the nest state between bouts. In other words, the depletion  from 𝐺0 substantially influences the time point at which approach makes a transition from  peak to steady-state; the steady-state time then depends on the dynamics of depletion  (when at the object) and replenishment (when at the nest). In particular, in the steady-state  phases, the agent must wait multiple turns at the nest for 𝐺(𝑡)  to regenerate so that  informational reward once again exceeds the potential cost of hazard.“

(2) Line 237- (Section 2.2.6, 2.2.7, Figures 7, 9)

I was confused by the descriptions about nCVaR. I looked at the cited original literature  Gagne & Dayan 2022, and understood that nCVaR is a risk-sensitive version of expected  future returns (equation 4) with parameter α (α-bar) (ranging from 0 to 1) representing risk  preference. Line 269-271 and Section 4.2 of the present manuscript described (in my  understanding) that α was a parameter of the model. Then, isn't it more natural to report  estimated values of α, rather than nCVaR, for individual animals in Section 2.2.6, 2.2.7,  Figures 7, 9 (even though nCVaR monotonically depends on α)? In Figures 7 and 9, nCVaR  appears to be upper-bounded to 1. The upper limit of α is 1 by definition, but I have no idea why nCVaR was also bounded by 1. So I would like to ask the authors to add more detailed  explanations on nCVaR. Currently, CVaR is explained in Lines 237-243, but actually, there is  no explanation about nCVaR rather than its formal name 'nested conditional value at risk' in  Line 237.

Thank you for pointing out this error. We have corrected the paper to use nCVaR to refer to  the objective and nCVaR's α, or sometimes just α, to refer to the risk sensitivity parameter  and thus the degree of risk sensitivity.

(3) Line 333 (and Abstract)

Given that animals' behaviors could be equally well fitted by the model having both nCVaR ( free α) and hazard prior and the alternative model having only hazard prior (with α = 1), may  it be difficult to confidently claim that brave (/timid) animals had risk-neutral (/risk-aversive)  preference in addition to widespread (/low-variance) hazard prior? Then, it might be good to  somewhat weaken the corresponding expression in the Abstract (e.g., add 'potentially also'  to the result for risk sensitivity) or mention the inseparability of risk sensitivity and prior belief  pessimism (e.g., "... although risk sensitivity and prior belief pessimism could not be teased  apart").

Thank you for this suggestion, we have duly weakened the wording in the Abstract to say  “potentially more risk neutral”:

“Some animals begin with cautious exploration, and quickly transition to confident approach  to maximize exploration for reward; we classify them as potentially more risk neutral, and  enjoying a flexible hazard prior. By contrast, other animals only ever approach in a cautious  manner and display a form of  self-censoring; they are characterized by potential risk  aversion and high and inflexible hazard priors.”

Reviewer #2 (Public Review):

Shen and Dayan build a Bayes adaptive Markov decision process model with three key  components: an adaptive hazard function capturing potential predation, an intrinsic reward  function providing the urge to explore, and a conditional value at risk (CvaR, closely related  to probability distortion explanations of risk traits). The model itself is very interesting and  has many strengths including considering different sources of risk preference in generating  behavior under uncertainty. I think this model will be useful to consider for those studying  approach/avoid behaviors in dynamic contexts.

The authors argue that the model explains behavior in a very simple and unconstrained  behavioral task in which animals are shown novel objects and retreat from them in various  manners (different body postures and patterns of motor chunks/syllables). The model itself  does capture lots of the key mouse behavioral variability (at least on average on a  mouse-by-mouse basis) which is interesting and potentially useful. However, the variables in  the model - and the internal states it implies the mice have during the behavior - are  relatively unconstrained given the wide range of explanations one can offer for the mouse  behavior in the original study (Akiti et al). This reviewer commends the authors on an original  and innovative expansion of existing models of animal behaviour, but recommends that the  authors  revise their study to reflect the obvious  challenges . I would also recommend a  reduction in claiming that this exercise gives a normative-like or at least quantitative account  of mental disorders.

We thank reviewer #2 for highlighting some of the strengths of our paper as well as pointing  out important limitations of Akiti et al’s original study which we’ve inherited as well as some  limitations of our own method. We address their concerns below.

We have added a paragraph to the discussion discussing the limitations of the state  representation we adopted from Akiti’s study.

(Reviewer #1 had the same concern, see above) “Motivated by tail-behind versus  tail-exposed in Akiti et al. (2022), we model approach using a dichotomy between cautious  and confident approach states [...]”

We have reduced the suggestion that our model provides an account of mental disorders in  the abstract.

Before:

“On the other hand, “timid” animals, characterized by risk aversion and high and inflexible  hazard priors, display self-censoring that leads to the sort of asymptotic maladaptive  behavior that is often associated with psychiatric illnesses such as anxiety and depression.”

After:

“By contrast, other animals only ever approach in a cautious manner and display a form of  self-censoring; they are characterized by potential risk aversion and high and inflexible  hazard priors. “

My main comment is that this paper is a very nice model creation that can characterize the  heterogeneity rodent behavior in a very simple approach/avoid context (Akiti et al; when a  novel object is placed in an arena) that itself can be interpreted in a multitude of ways. The  use of terms like "exploration", "brave", etc in this context is tricky because the task does not  allow the original authors (Akiti et al) to quantify these "internal states" or "traits" with the  appropriate level of quantitative detail to say whether this model is correct or not in capturing  the internal states that result in the rodent behavior. That said, the original behavioral setup  is so simple that one could imagine capturing the behavioral variability in multiple ways ( potentially without evoking complex computations that the original authors never showed  the mouse brain performs). I would recommend reframing the paper as a new model that  proposes a set of internal states that could give rise to the behavioral heterogeneity  observed in Akiti et al, but nonetheless is at this time only a hypothesis. Furthermore, an  explanation of what would be really required to test this would be appreciated to make the  point clearer.

We thought very hard about using terms that might be considered to be anthropomorphic  such as ‘timid’ and ‘brave’. We are, of course, aware, of the concerns articulated by  investigators such as LeDoux about this. However, we think that, provided that we are clear  on the first appearance (using ‘scare’ quotes) that we are using them as indeed labels for  latent characteristics that capture correlations in various aspects of behaviour, they are more  helpful than harmful in making our descriptions understandable.

Reviewer #3 (Public Review):

Summary:

The manuscript presents computational modelling of the behaviour of mice during  encounters with novel and familiar objects, originally reported by Akiti et al. (Neuron 110, 2022)          . Mice typically perform short bouts of approach followed by a retreat to a safe  distance, presumably to balance exploration to discover possible rewards with the potential  risk of predation. However, there is considerable heterogeneity in this exploratory behaviour,  both across time as an individual subject becomes more confident in approaching the object,  and across subjects; with some mice rapidly becoming confident to closely explore the  object, while other timid mice never become fully confident that the object is safe. The  current work aims to explain both the dynamics of adaptation of individual animals over time,  and the quantitative and qualitative differences in behaviour between subjects, by modelling  their behaviour as arising from model-based planning in a Bayes adaptive Markov Decision  Process (BAMDP) framework, in which the subjects maintain and update probabilistic  estimates of the uncertain hazard presented by the object, and rationally balance the  potential reward from exploring the object with the potential risk of predation it presents.

In order to fit these complex models to the behaviour the authors necessarily make  substantial simplifying assumptions, including coarse-graining the exploratory behaviour into  phases quantified by a set of summary statistics related to the approach bouts of the animal.  Inter-individual variation between subjects is modelled both by differences in their prior  beliefs about the possible hazard presented by the object and by differences in their risk  preference, modelled using a conditional value at risk (CVaR) objective, which focuses the  subject's evaluation on different quantiles of the expected distribution of outcomes.  Interestingly these two conceptually different possible sources of inter-subject variation in  brave vs timid exploratory behaviour turn out not to be dissociable in the current dataset as  they can largely compensate for each other in their effects on the measured behaviour.  Nonetheless, the modelling captures a wide range of quantitative and qualitative differences  between subjects in the dynamics of how they explore the object, essentially through  differences in how subject's beliefs about the potential risk and reward presented by the  object evolve over the course of exploration, and are combined to drive behaviour.

Exploration in the face of risk is a ubiquitous feature of the decision-making problem faced  by organisms, with strong clinical relevance, yet remains poorly understood and  under-studied, making this work a timely and welcome addition to the literature.

Strengths:

(1) Individual differences in exploratory behaviour are an interesting, important, and  under-studied topic.

(2) Application of cutting-edge modelling methods to a rich behavioural dataset, successfully  accounting for diverse qualitative and qualitative features of the data in a normative  framework.

(3) Thoughtful discussion of the results in the context of prior literature.

Limitations:

(1) The model-fitting approach used of coarse-graining the behaviour into phases and fitting  to their summary statistics may not be applicable to exploratory behaviours in more complex  environments where coarse-graining is less straightforward.

(2) Some aspects of the work could be more usefully clarified within the manuscript.

We thank reviewer #3 for their positive feedback and helping us to improve the clarity of our  paper. We have added discussion they thought was missing.

Reviewer #1 (Recommendations for the authors):

(1) Line 25-28

This part of the Abstract might give an impression that timidity (but not braveness) is  potentially associated with psychiatric illness and even that timidity is thus inferior to  braveness. However, even though extreme timidity might indeed be associated with anxiety  or depression, extreme braveness could also be associated with other psychiatric or  behavioral problems. Moreover, as a population, the existence of both timid and brave  individuals could be advantageous, and it could be a reason why both types of individuals  evolutionarily survived in the case of wild animals (although Akiti et al. used mice, which may  have no or very limited genetic varieties, and so things may be different). So I would like to  encourage the authors to elaborate on the expression of this part of the Abstract and/or  enrich the related discussion in the Discussion.

This is an important point. We note on line 38 that excessive novelty seeking (potentially  caused by excessive braveness) could also be maladaptive.

Additionally, we have added a paragraph to the discussion discussing heterogeneity in risk  sensitivity within a population.

“Our data show that there is substantial variation in the degrees of risk sensitivity across the  mice.  Previous works have reported substantial interpopulation and intrapopulation  differences in risk-sensitivity in humans which depend on gender, age, socioeconomic  status, personality characteristics, wealth and culture (Rieger et al., 2015; Frey et al., 2017).  Despite the normative appeal of 𝛼 = 1, it is possible that a population may benefit from  including individuals with $\alpha$ different from 1.0 or highly negative priors. For example,  more cautious individuals could learn from merely observing the risky behavior of less  cautious individuals. Furthermore, we have only considered risk-sensitivity under epistemic  uncertainty in our work. Risk averse individuals, for instance with 𝛼 < 1 may be more  successful than risk-neutral agents in environments where there are unexpected dangers ( unknown unknowns). Risk-aversion is thus a temperament of ecological and evolutionary  significance (Réale et al., 2007).”

(2) Line 149

Section 2.2 consists of eight subsections. I think this organization may not be very  appealing, because there are a bit too many subsections, and their relations are not  immediately clear to readers. So I would like to encourage the authors to make an  elaboration. For example, since 2.2.1 - 2.2.5 describes a summary of model construction  and model fitting whereas 2.2.6-2.2.8 shows the results, it could be good to divide these into  separate sections (2.2.1 - 2.2.5 and 2.3.1 - 2.3.3).

Thank you for pointing this out. We’ve renumbered the sections as you’ve suggested.

(3) Line 347-8

Theoretically, the effect of prior is diluted over experience whereas the effect of biased  (risk-aversive) evaluation persists, as the authors mentioned in Lines 393-394. Then isn't it  possible to consider environments/conditions in which the two effects can be separated?

We appreciate this suggestion. Indeed, our original thought in modeling this experiment was  that this would be exactly the case here - with epistemic uncertainty reducing as the object  became more familiar. However, proving to an animal that a single environment is  completely stationary/fixed is hard - reflected in our conclusion here that the exploration  bonus pool replenishes. Thus, we argued in the discussion that a series of environments  would be necessary to separate risk sensitivity from priors.

(4) Line 407

It would be nice to add a brief phrase explaining how (in what sense) this model's  assumption was consistent with the reported behavior. Also, should the assumption of  having two discrete approach states (cautious and confident) itself be regarded as a  limitation of the model? If the tail-behind and tail-exposure approaches were not merely  operationally categorized but were indicated to be two qualitatively distinct behaviors in the  experiment by Akiti et al., it is reasonable to model them as two discrete states, but  otherwise, the assumption of two discrete states would need to be mentioned as a  simplification/limitation.

We have now removed line 407, and now have an additional  paragraph in the discussion  discussing the limitations of the tail-behind and tail-exposure state representation: “Motivated by tail-behind versus tail-exposed in Akiti et al. (2022), we model approach using  a dichotomy between cautious and confident approach states. This is likely a crude  approximation to the continuous and multifaceted nature of animal approach behavior. For  example, during approach animals likely adjust their levels of vigilance continuously (or  discretely; Lloyd and Dayan (2018)) to  monitor threat, and choose different velocities for  movement, and different attentional strategies for inspecting the novel object. We hope  future works will model these additional behavioral complexities, perhaps with additional  internal states, and corroborate these states with neurobiological data.”

(5) Line 418

The authors contrasted their model-based analyses with the model-free analyses of Akiti et  al. Another aspect of differences between the authors' model and the model of Akiti et al. is  whether it is normative or mechanistic: while how the model of Akiti et al. can be biologically  implemented appears to be clear (TS dopamine represents threat TD error, and TS  dopamine-dependent cortico-striatal plasticity implements TD error-based update of  model-free threat prediction), biological implementation of the authors' model seems more  elusive. Given this, it might be a fruitful direction to explore how these two models can be  integrated in the future.

We enthusiastically agree that it would be most interesting in the future to explore the  integration of the two models - and, in the discussion ( Lines 537-548, 454-461) , point to  some first steps that might be fruitful along these lines. There are two separate  considerations here: one is that our account is mostly computational and algorithmic,  whereas Akiti’s model is mostly algorithmic and implementational; the second is, as noted by  the reviewer, that our account is model-based, whereas Akiti’s model is model-free (in the  sense of reinforcement learning; RL). These are related - thanks in no small part to the work  from the group including Akiti, we know a lot more about the implementation of model-free  than model-based RL. However, our model-based account does reach additional features of  behavior not captured in Akiti et al.’s model such as bout duration, frequency, and approach  type. Thus, the temptation of unification.

(6) Line 426

Related to the previous point, it would be nice to more specifically describe what variable TS  dopamine can represent in the authors' model if possible.

In the discussion  (Lines 454-461) , we speculate that  TS dopamine could still respond to the  physical salience of the novel object and affect choices by determining the potential cost of  the encountered threat or the prior on the hazard function. For example, perhaps ablating TS  dopamine reduces the hazard priors which leads to faster transition from cautious to  confident approach and longer bout durations, consistent with the optogenetics behavioral  data reported in Akiti et al.

Reviewer #2 (Recommendations for the authors):

My guess is simpler versions of the model would not fit the data well. But this does not mean  for example that the mice have probability distortions (CvaR) or that even probabilistic  reasoning and the internal models necessary to support them are acting in the behavioral  context studied by Akiti. So related to the above, I would ask what other models would fit and  would not fit the data? And what does this mean?

These are good points. Our model provides an approximately normative account of the  animals’ behavior  in terms of what it achieves relative to a utility function. In practice, the  animals could deploy a precompiled model-free policy (which does not rely on probabilistic  computations) that is exactly equivalent to our model-based policy. With the current  experiment, we cannot conclude whether or not the animals are performing the prospective  calculations in an online manner. Of course, the extent to which animals or humans are  performing probabilistic computations online and have internal models are on-going  questions of study.

Model comparison is difficult because currently we do not know of any other risk-sensitive  exploration models. We cannot directly compare to the model in Akiti et al. since our model  explains additional features of behavior: bout duration, frequency, and approach type.  Indeed, our model is as simple as it can be in the sense with the exception of nCVaR,  removing any of the other parameters makes it difficult to fit some animals in our dataset. In the future, our model could be used to fit other datasets of risk-sensitive exploration and,  ideally,  be compared to other models.

Explaining why animals avoid the novel object in what the offers call benign environment is a  very tricky issue. In Akiti et al, the readers are not yet convinced that the mice know that this  environment is benign. Being placed in an arena with a novel object presents mice with a  great uncertainty and we do not know whether they treat this as benign. Therefore, the  alternative explanations in this study need to be carefully discussed in lieu of the limitations  of the initial study.

It is certainly true that it is unclear if the arena is  completely  benign to the animals. However,  the amount of time the animal spends in the center of the arena decreases significantly from  habituation to novelty days. This suggests that the animals avoid the novel object largely  because of the object itself, rather than the potential danger associated with the arena.  Furthermore, the animals are not reported as exhibiting more extreme behaviours such as  freezing. In any case, our account is relative in the sense that we are comparing the time the  animal spends at the object versus elsewhere in the environment, driven by the relative  novelty and relative risk of the environment versus the object. Trying to get more absolute  measures of these quantities would require a richer experimental set-up, for instance with  different degree of habituation or experience of the occurrence of (other) novel objects, in  general.

We added a short note to the discussion to explain this:

“Fourth, we modeled the relative amount of time the animal spends at the object versus  elsewhere in the environment which depends on the differential risk in the two states.  However, it is likely the animals avoid the novel object largely because of the object itself,  rather than the potential danger associated with the arena since they spend much less time  at the center of the arena during novelty than habituation days.”

Figure 2 - how confident are the authors that each mouse differs from y=1? Related to this,  the behavior in Akiti is very noisy and changes across time. I am not sure if the authors fully  describe at what levels their model captures the behavior vs not in a detailed enough  fashion.

We have performed a random permutation test on the minute-to-minute data. We have  updated Figure 2 so that brave animals that pass the Benjamini–Hochberg procedure y>1 at  level q=0.05 are represented with solid green dots and animals that don’t pass are  represented with hollow dots. 8 out of 11 brave animals passed Benjamini–Hochberg.

Reviewer #3 (Recommendations for the authors):

(1) I could not find information in the preprint about code availability. Please consider making  the code public to help others apply these modelling methods.

We have released code and included the url in the paper in the Methods section.

(2) Though the manuscript was generally clearly written, there were a number of places  where some additional information or clarification would be useful:

a) Please define and explain the terms 'tail-behind' and 'tail-exposed' (used to describe  approach bout types) when first used.

We have added definitions when we first mention these terms:

“[...] 'tail-behind' (bouts where the animal's nose was closer to the object than the tail for the  entire bout) and 'tail-exposed' (bouts where the animal's tail is closer to the object than the  nose at some point during the bout), associated respectively with cautious risk-assessment  and engagement”

b) At lines 57-58 when contrasting the 'model-free' account of Akiti et al with the 'model-based' account of the current work, it would be worth clarifying that these terms are  being used in the RL sense rather than e.g. a model-based analysis of the data.  

We have updated the relevant lines to say “model-free/based reinforcement learning”.

c) Line 61, the phrase 'the significant long-run approach of timid animals despite having  reached the "avoid" state' is unclear as the 'avoid' state has not been defined.

We updated the terminology to “avoidance behavior” to be consistent with Akiti et al.  Avoidance refers to the animal routinely avoiding the object and therefore being unable to  learn whether it is safe.

d) It was not completely clear to me how the coarse-graining of the behaviour was  implemented. Specifically, how were animals assigned to the brave, intermediate, or timid  group, and how were the parameters of the resulting behavioural phases fit?

Sorry that this was not clear. Section 2.1 explains how the minute-to-minute behavioral data  was coarse-grained and how animal groups were assigned. We have added further  explanation of Figure 2 to the main text:

“Fig 2 summarizes our categorization of the animals into the three groups: brave,  intermediate, and timid based on the phases identified in the animal's exploratory  trajectories. Timid animals spend no time in confident approach and are plotted in orange at  the origin of Fig 2. Brave animals differ from intermediate animals in that their approach time  during the first ten minutes of the confident phase is greater than the last ten minutes ( steady-state phase). Brave animals are plotted in green above and intermediate animals  are plotted in black below the y=1 line in Fig 2.”

We also added extra information to outline the goal, and methodology of coarse-graining and  animal grouping:

“We sought to capture  these qualitative differences (cautious versus confident) as well as  aspects of the quantitative changes in bout durations and frequencies as the animal learns  about their environment. To make this readily possible, we abstracted the data in two ways:

averaging  bout statistics over time, and clustering the animals into three groups with  operationally distinct behaviors.”

e) What purpose does the 'retreat' state serve in the BAMDP model (as opposed to  transitioning directly from 'object' to 'nest' states), and why do subjects not pass through it  following 'detect' states?

Thank you for pointing this out. We have updated Figure 3 to note that the two “detected  states” also point to the “retreat” state. The reviewer is correct that there could be alternative  versions of the state diagram, and the ‘retreat’ state could indeed have been eliminated.  However, we thought that it was helpful to structure the animal’s progress through state  space.

f) Why was the hazard function parameterised via the mean and SD at each time step rather  than with a parametric form of the mean and SD as a function of time?

Since the agent can only spend 2, 3, or 4 turns at the object states, we didn’t see a need to  parameterize the mean and SD as a function of time. Doing so is a good solution to scaling  up the hazard function to more time-steps.

(3) There were also a couple of points that could potentially be usefully touched on in the  discussion:

a) What, if any, is the relationship between the CVaR objective and distributional RL? They  seem potentially related due to both focussing on quantiles of the outcome distribution.

We have added a paragraph to the discussion discussing the connection between  distributional RL and CVaR:

“CVaR is known to come in different flavors in the case of temporally-extended behavior.  Gagne and Dayan (2021) introduces two alternative time-consistent formulations of CVaR:  nested CVaR (nCVaR) and precommitted CVaR (pCVaR). nCVaR and pCVaR both enjoy  Bellman equations which make it possible to compute approximately optimal policies without  directly computing whole distributions of the outcomes. We use nCVaR in this study for its  computational efficiency. There is, of course, great current interest in distributional  reinforcement learning (Bellemare et al., 2023b) which does acquire such whole  distributions, not the least because of prominent observations linking non-linearities in the  response functions of dopamine neurons to methods for learning distributions of outcomes ( Dabney et al., 2020; Masset et al., 2023; Sousa et al., 2023). One functional motivation for  considering entire outcome distributions is the possibility of using them to determine  risk-sensitive policies (Gagne and Dayan, 2021).

While it is possible to compute CVaR directly from return distributions, Gagne and Dayan  (2021) showed that this can lead to temporally inconsistent policies where the agent  deviates from its original plans (the authors called this the fixed CVaR or fCVaR measure).

Rather further removed from our model-based methods is work from Antonov and Dayan  (2023), who consider a model-free exploration strategy which exploits full return distributions  to compute the value of perfect information which is used as a heuristic for trying actions  with uncertain consequences. Future works can examine risk-sensitive versions of Antonov  and Dayan (2023)'s computationally efficient model-free algorithm as one solution to the  burdensome computations in our model-based method.”

b) Why normatively might subjects have non-neutral risk preference as captured by the  CvaR?

We also added a paragraph to the discussion discussing the advantage of heterogeneity in  risk sensitivity within a population:

(Reviewer #1 had the same question, see above) “Our data show that there is substantial  variation in the degrees of risk sensitivity across the mice.  Previous works have reported  substantial interpopulation and intrapopulation differences in risk-sensitivity in humans which  depend on gender, age, socioeconomic status, personality characteristics, wealth and culture [...]”

c) Relevance of the current modelling work to clinical conditions characterised by  dysregulation of risk assesment (e.g. anxiety or PTSD).

We’ve added a paragraph to the discussion:

“Inter-individual differences in risk sensitivity are also of critical importance in psychiatry,  reflected in a panoply of anxiety disorders (Butler and Mathews, 1983; Giorgetta et al., 2012;  Maner et al., 2007; Charpentier et al., 2017), along with worry and rumination (Gagne and  Dayan, 2022). Understanding the spectrum of   extreme priors and extreme values of 𝛼  could have therapeutic implications, adding significance to the search for tasks that can  more cleanly separate them.”

d) Is it surprising to see differences in risk preference (nCVaR) between the familiar object  and novel object condition, given that risk preference might be conceptualised as a trait  rather than a state variable?

Thank you for raising this point. You are right that we expected risk sensitivity (nCVaR alpha)  to be the same between FONC and UONC animals on average. It is difficult to know if alpha  is higher for FONC than UONC animals due to the non-identifiability between alpha and  hazard priors. We have added this discussion to the paper:

“This is surprising if we interpret 𝛼 as a trait that is stable through time. Unfortunately, due to  the non-identifiability between 𝛼 and hazard priors, we cannot verify whether 𝛼 is actually  higher for FONC animals than UONC animals.”

Author response:

Reviewer #1 (Public review):

Summary:

The study is methodologically solid and introduces a compelling regulatory model. However, several mechanistic aspects and interpretations require clarification or additional experimental support to strengthen the conclusions.

Strengths:

(1) The manuscript presents a compelling structural and biochemical analysis of human glutamine synthetase, offering novel insights into product-induced filamentation.

(2) The combination of cryo-EM, mutational analysis, and molecular dynamics provides a multifaceted view of filament assembly and enzyme regulation.

(3) The contrast between human and E. coli GS filamentation mechanisms highlights a potentially unique mode of metabolic feedback in higher organisms.

Weaknesses:

(1) The mechanism underlying spontaneous di-decamer formation in the absence of glutamine is insufficiently explored and lacks quantitative biophysical validation.

(2) Claims of decamer-only behavior in mutants rely solely on negative-stain EM and are not supported by orthogonal solution-based methods.

We thank the reviewer for the summary and noting of the strengths. We agree that the evolutionary divergence of metabolic feedback in GS homologs is a fruitful avenue for future studies. With regard to the weaknesses, the di-decamer in the absence of glutamine only forms under high (higher than physiological) concentrations of enzyme. Our primary evidence for the mutant behavior was the lack of crosslinking (Figure 1E), with supplementary support from the negative stain. In the revised version we will soften the language to say “reduced” rather than “did not support” filament formation.

Reviewer #2 (Public review):

The authors set out to resolve the high-resolution structure of a glutamine synthetase (GS) decamer using cryo-EM, investigate glutamine binding at the decamer interface, and validate structural observations through biochemical assays of ATP hydrolysis linked to enzyme activity. Their work sits at the intersection of structural and functional biology, aiming to bridge atomic-level details with biological mechanisms - a goal with clear relevance to researchers studying enzyme catalysis and metabolic regulation.

Strengths and weaknesses of methods and results:

A key strength of the study lies in its use of cryo-EM, a technique well-suited for resolving large, dynamic macromolecular complexes like the GS decamer. The reported resolutions (down to 2.15 Å) initially suggest the potential for detailed structural insights, such as side-chain interactions and ligand density. However, several methodological limitations significantly undermine the reliability of the results:

(1) Cryo-EM data processing: The absence of critical details about B-factor sharpening - a standard step to enhance map interpretability - is a major concern. For high-resolution maps (<3 Å), sharpening is typically applied to resolve side-chain features, yet the submitted maps (e.g., those in Figures 1D, 2D, and supplementary figures) appear unprocessed, with density quality inconsistent with the claimed resolutions. This makes it difficult to evaluate whether observed features (e.g., glutamine binding) are genuine or artifacts of unsharpened data.

(2) Modeling and density consistency: The structural models, particularly for glutamine binding at the decamer interface, do not align with the reported resolution. The maps shown in Figure 2D and Supplementary Figure S7 lack sufficient density to confidently place glutamine or even surrounding residues, conflicting with claims of 2.15 Å resolution. Additionally, fitting a non-symmetric ligand (glutamine) into a symmetry-refined map requires justification, as symmetry constraints may distort ligand placement.

(3) Biochemical assay controls: While the enzyme activity assays aim to link structure to function, they lack essential controls (e.g., blank reactions without GS or substrates, substrate omission tests) to confirm that ATP hydrolysis is GS-dependent. The use of TCEP, a reducing agent, is also not paired with experiments to rule out unintended effects on the PK/LDH system, further limiting confidence in activity measurements.

Achievement of aims and support for conclusions:

The study falls short of convincingly achieving its goals. The claimed high-resolution structural details (e.g., side-chain densities, ligand binding) are not supported by the provided maps, which lack sharpening and show inconsistencies in density quality. Similarly, the biochemical data do not robustly validate the structural claims due to missing controls. As a result, the evidence is insufficient to confirm glutamine binding at the decamer interface or the functional relevance of the observed structural features.

Likely impact and utility:

If these methodological gaps are addressed, the work could make a meaningful contribution to the field. A well-resolved GS decamer structure would advance understanding of enzyme assembly and ligand recognition, while validated biochemical assays would strengthen the link between structure and function. Improved data processing and clearer reporting of validation steps would also make the structural data more reliable for the community, providing a resource for future studies on GS or related enzymes.

We disagree with the reviewer’s overall assessment.

With regard to sharpening and resolution: we examined sharpened maps and in a revised version will present additional supplementary figures showing these maps side by side. We note that the resolutions reported are global and that the most interesting features are, of course, in the periphery and subject to conformational and compositional heterogeneity. We will include supplementary figures of core side chain densities that are more like what are expected by the reviewer in the revision. 

With regard to modeling: the apo filament and turnover filament datasets were handled nearly identically. The additional density is therefore likely not artefactual to the symmetry operator - however, the lower resolution in this region noted by the reviewer is worthy of further exploration. The maps are public and we think this is the most plausible interpretation of the density, which we based primarily on the biochemical data and will include more speculation in the version.

With regard to the biochemical controls: we point the reviewer to Figure S1, which shows that omission of ammonia or glutamate in the wild-type (tagless) system removes any coupling of the reactions. We will perform the additional controls to publication quality in the revised version along with the TCEP control. We note that the reducing agent is present across all experiments, ruling out an effect on any specific result. The inclusion of TCEP is also very standard in other published uses of the Coupled ATPase assay (e.g. PMID: 31778111 and PMID: 32483380 by our first author)

Additional context:

Cryo-EM has transformed structural biology by enabling high-resolution analysis of large complexes, but its success hinges on rigorous data processing and validation steps that are critical to ensuring reproducibility. The challenges highlighted here are not unique to this study; they reflect broader issues in the field where incomplete reporting of methods can obscure the reliability of results. By addressing these points, the authors would not only strengthen their current work but also set a positive example for transparent and rigorous structural biology research.

All the data is public and the reviewer or anyone is free to reinterpret the maps and models - and we encourage that rather than just an interpretation of our static figures. In addition, we will upload the raw micrograph data for the apo filament and turnover filament datasets to EMPIAR prior to submitting the revision.

Reviewer #3 (Public review):

In this manuscript, the authors propose a product-dependent negative-feedback mechanism of human glutamine synthetase, whereby the product glutamine facilitates filament formation, leading to reduced catalytic specificity for ammonia. Using time-resolved cryo-EM, the authors demonstrate filament formation under product-rich conditions. Multiple high-quality structures, including decameric and di-decameric assemblies, were resolved under different biochemical states and combined with MD simulations, revealing that the conformational space of the active site loop is critical for the GS catalysis. The study also includes extensive steady-state kinetic assays, supporting the view that glutamine regulates GS assembly and its catalytic activity. Overall, this is a detailed and comprehensive study. However, I would advise that a few points be addressed and clarified.

(1) In Figure 2D and Supplementary Figure 7, the extra density observed between the two decamers does not appear to have the defining features of a glutamine. A less defined density may be expected given the nature of the complex, but even though mutagenesis assays were performed to support this assignment, none of these results constitutes direct and conclusive evidence for glutamine binding at this site. I would thus suggest showing the density maps at multiple contour thresholds to allow readers to also better evaluate the various small molecules under turnover conditions that cannot be well fitted based on this density map, helping to provide a more balanced interpretation of the results.

(2) On the same point regarding the density for the enzyme under turnover conditions, more details should be provided about the symmetry expansion and classification performed, and also show the approximate ratio of reconstructions that include this density. Did you try symmetry expansion followed by focused classification, especially on the interface region?

(3) The interface between the two decamers of the model needs to be double-checked and reassigned, especially for the residues surrounding the fitted glutamine. For example, the side chain of the Lys residue shown in the attached figure is most likely modeled incorrectly.

We thank the reviewer for the feedback. As noted above, we will include supplemental figures that show maps at multiple thresholds and sharpening schemes. We noted in the manuscript and above that our interpretation here is based on integrating biochemical evidence alongside the density and will make that even more clear in the revised manuscript. The filaments +/- the putative glutamine density were processed nearly identically, but we will attempt various schemes of focused classification/symmetry expansion in the revision as well. However, we point out that there is extensive averaging there that makes modeling a bit trickier than expected given the global resolution.

This is something I agree with wholeheartedly. And I think it is because I see this in my job, we have an "Employee of the Quarter" program and it sounds wonderful on the surface level but the unfortunate reality is that every single person will eventually get this award even if they don't deserve it. This will cause employees to think "Oh I can get this extra special recognition and this award just for being here/doing below the bare minimum/doing the bare minimum,,."

Group G Ben Braniff, Kim Maynard, Nick Devic, Maria Echeverri Solis, Sam Yalda

1. Design has a major impact on the world and society. Even the little things can add up to a lot. Sustainability is a revolutionary Idea that should be at the core of every design now.

2. Society is another bottom line meaning all design inherently affects humans and/or is designed for humans. It's important to design for the extremes and the edge cases like people with disabilities.

3. Corporations output a lot of waste. When they make small changes to be more sustainable, it results in big changes and saving a lot of material. Small changes can include anything from using 2% less plastic per water bottle to using wood buttons instead of plastic ones.

4. A lot of people don't consider themselves disabled, but it's very common at some point in people's lives to have a certain level of impairment. It's important to keep this in mind when designing as you're designing for the general population--not just a specific individual.

5. Addressing issues like world hunger may require rethinking the way we design food production. As they stated for example, choosing kangaroo meat over beef as a more environmentally sustainable option.

6. Thoughtful design choices per the example in the video such as adding white circles inside letters to reduce ink use, can improve efficiency and conserve resources.

7. It is interesting how he opens up his discussion to slowly introduce that design isn't just about doing it for marketing or 'profit' as he pointed out. When watching this it helps a person realize that design is so much more powerful than that if you put it towards another cause. Design could end up being the solution to some of the biggest problems in society.

8. A very important point he made was that improving accessibility is beneficial to many more people than just the people that initially needed it such as people with disabilities. From this i think a good takeaway is that design should always be considerate of any disabilities/needs that the audience might have because sometimes that design is just better for everyone in general.

9. My first take is design should go beyond money and aesthetics. By thinking about sustainability and accessibility the designers can create solutions that are socially responsible and environmentally friendly.

10. My second take is when you design with people with disabilities you end up with solutions that are more usable and inclusive

Author response:

Public Reviews:

Reviewer #1 (Public review):

Summary:

This work aims to elucidate the molecular mechanisms affected in hypoxic conditions, causing reduced cortical interneuron migration. They use human assembloids as a migratory assay of subpallial interneurons into cortical organoids and show substantially reduced migration upon 24 hours of hypoxia. Bulk and scRNA-seq show adrenomedullin (ADM) up-regulation, as well as its receptor RAMP2, confirmed atthe protein level. Adding ADM to the culture medium after hypoxic conditions rescues the migration deficits, even though the subtype of interneurons affected is not examined. However, the authors demonstrate very clearly that ineffective ADM does not rescue the phenotype, and blocking RAMP2 also interferes with the rescue. The authors are also applauded for using 4 different cell lines and using human fetal cortex slices as an independent method to explore the DLXi1/2GFP-labelled iPSC-derived interneuron migration in this substrate with and without ADM addition (after confirming that also in this system ADM is up-regulated). Finally, the authors demonstrate PKA-CREB signalling mediating the effect of ADM addition, which also leads to up-regulation of GABAreceptors. Taken together, this is a very carefully done study on an important subject - how hypoxia affects cortical interneuron migration. In my view, the study is of great interest.

Strengths:

The strengths of the study are the novelty and the thorough work using several culture methods and 4 independent lines.

Weaknesses:

The main weakness is that other genes regulated upon hypoxia are not confirmed, such that readers will not know until which fold change/stats cut-off data are reliable.

Reviewer #2 (Public review):

Summary

The manuscript by Puno and colleagues investigates the impact of hypoxia on cortical interneuron migration and downstream signaling pathways. They establish two models to test hypoxia, cortical forebrain assembloids, and primary human fetal brain tissue. Both of these models provide a robust assay for interneuron migration. In addition, they find that ADM signaling mediates the migration deficits and rescue using exogenous ADM.

Strengths:

The findings are novel and very interesting to the neurodevelopmental field, revealing new insights into how cortical interneurons migrate and as well, establishing exciting models for future studies. The authors use sufficient iPSC lines including both XX and XY, so the analysis is robust. In addition, the RNAseq data with re-oxygenation is a nice control to see what genes are changed specifically due to hypoxia. Further, the overall level of validation of the sequencing data and involvement of ADM signaling is convincing, including the validation of ADM at the protein level. Overall, this is a very nice manuscript.

Weaknesses:

I have a few comments and suggestions for the authors. See below.

Reviewer #3 (Public review):

Summary:

The authors aimed to test whether hypoxia disrupts the migration of human cortical interneurons, a process long suspected to underlie brain injury in preterm infants but previously inaccessible for direct study. Using human forebrain assembloids and ex vivo developing brain tissue, they visualized and quantified interneuron migration under hypoxic conditions, identified molecular components of the response, and explored the effect of pharmacological intervention (specifically ADM) on restoring the migration deficits.

Strengths:

The major strength of this study lies in its use of human forebrain assembloids and ex vivo prenatal brain tissue, which provide a direct system to study interneuron migration under hypoxic conditions. The authors combine multiple approaches: long-term live imaging to directly visualize interneuron migration, bulk and single-cell transcriptomics to identify hypoxia-induced molecular responses, pharmacological rescue experiments with ADM to establish therapeutic potential, and mechanistic assays implicating the cAMP/PKA/pCREB pathway and GABA receptor expression in mediating the effect. Together, this rigorous and multifaceted strategy convincingly demonstrates that hypoxia disrupts interneuron migration and that ADM can restore this defect through defined molecular mechanisms.

Overall, the authors achieve their stated aims, and the results strongly support their  conclusions. The work has a significant impact by providing the first direct evidence of hypoxia-induced interneuron migration deficits in the human context, while also nominating a candidate therapeutic avenue. Beyond the specific findings, the methodological platform - particularly the combination of assembloids and live imaging - will be broadly useful to the community for probing neurodevelopmental processes in health and disease.

Weaknesses:

The main weakness of the study lies in the extent to which forebrain assembloids

recapitulate in vivo conditions, as the migration of interneurons from hSO to hCO does not fully reflect the native environment or migratory context of these cells. Nevertheless, this limitation is tempered by the fact that the work provides the first direct observation of human interneuron migration under hypoxia, representing a major advance for the field. In addition, while the transcriptomic analyses are valuable and highlight promising candidates, more in-depth exploration will be needed to fully elucidate the molecular mechanisms governing neuronal migration and maturation under hypoxic conditions.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

(1) The authors should examine if all cortical interneurons are affected by ADM or only subtypes (Parvalbumin/Somatostatin).

We thank the reviewer for raising this important question. In our study, we utilized the Dlx1/2b::eGFP reporter to broadly label cortical interneurons; however, this system does not distinguish specific interneuron subtypes. To address this, in the revised version of the manuscript we will use the single-cell RNA sequencing data and immunostainings to provide this information. Based on previous analyses from Birey et al (Cell Stem Cell, 2022), we expect interneurons within assembloids to express mostly calbindin (CALB2) and somatostatin (SST) at this in vitro stage of development; parvalbumin subtype appears later based on data from Birey et al (Nature, 2017) and more recently from Varela et al, (bioRxiv, 2025).

In parallel, we will analyze available scRNA-seq data from developing human primary brain tissue a similar age as the one used in the manuscript, and check whether these subtypes of interneurons are similar to the ones within assembloids.

(2) The authors should test more candidates from their bulk RNA-seq data with different fold changes for regulation after hypoxia, to allow the reader to judge at which cut-off the DEGs may be reproducible. This would make this database much more valuable for the field of hypoxia research.

We appreciate the reviewers’ thoughtful suggestion. In addition to the bulk RNA-seq analysis, we did validate several upregulated hypoxia-responsive genes with varying fold changes by qPCR; these include PDK1, PFKP, VEGFA (Figure S1). 

We go agree that in-depth investigation of specific cut-offs would be interesting, however, this could be the focus of a different manuscript.

Reviewer #2 (Recommendations for the authors):

(1) Can the authors comment on the possibility of inflammatory response pathways being activated by hypoxia? Has this been shown before? While not the focus of the manuscript, it could be discussed in the Discussion as an interesting finding and potential involvement of other cells in the Hypoxic response.

We thank the reviewer this important comment about inflammation. Indeed, hypoxia has been shown to activate the inflammatory response pathways. In various studies, it was found that HIF-1a can interact with NF-κB signaling, leading to the upregulation of pro-inflammatory cytokines such as IL-1β, IL-6, and TNF-α (Rius et al., Cell, 2008; Hagberg et al., Nat Rev Neurol, 2015).

In our transcriptomics data (Figure 2D), and to the reviewers’ point, we identified enrichment of inflammatory signaling response following the hypoxic exposure. Since hSO at the time of analyses do contain astrocytes, we think these glia contribute to the observed pro-inflammatory changes. Based on these results and because ADM is known to have strong anti-inflammatory properties, the effects of ADM on hypoxic astrocytes should be investigated in future studies focused on hypoxia-induced inflammation. In the revision, we will address this comment in the discussion section and cite the appropriate papers.

(2) Could the authors comment on the mechanism at play here with respect to ADM and binding to RAMP2 receptors - is this a potential autocrine loop, or is the source of ADM from other cell types besides inhibitory neurons? Given the scRNA-seq data, what cell-to-cell mechanisms can be at play? Since different cells express ADM, there could be different mechanisms in place in ventral vs dorsal areas.

Based on our scRNA-seq data in hSOs showing significant upregulation of ADM expression in astrocytes and progenitors, we speculate that the primary mechanism is likely to involve paracrine interactions. However, we cannot exclude autocrine mechanisms with the included experiments. Dissecting these interactions in a cell-type specific manner could be an important focus for future ADM-related studies.

To address the question about the possible different mechanisms in ventral versus dorsal areas, in the revision we will plot and include in the figures the data about the cell-type expression of ADM and its receptors in hCOs.

(3) For data from Figure 6 - while the ELISA assays are informative to determine which pathways (PKA, AKT, ERK) are active, there is no positive control to indicate these assays are "working" - therefore, if possible, western blot analysis from assembloid tissue could be used (perhaps using the same lysates from Figure 3) as an alternative to validate changes at the protein level (however, this might prove difficult); further to this, is P-CREB activated at the protein level using WB?

We thank the reviewer for this comment and the observation. Although we did not include a traditional positive control in these ELISA assays, several lines of evidence indicate that the measurements are reliable. First, the standard curves behaved as expected, and all sample values fell within the assay’s dynamic range. Second, technical replicates showed low variability, and the observed changes across experimental conditions (e.g., hypoxia vs. control) were consistent with the expected biological responses based on previous literature. We agree that including western blot validation would strengthen the findings, and we will note this for our future studies focused on CREB and ADM.

(4) Could the authors comment further on the mechanism and what biological pathways and potential events are downstream of ADM binding to RAMP2 in inhibitory neurons? What functional impact would this have linked to the CREB pathway proposed? While the link to GABA receptors is proposed, CREB has many targets beyond this.

We appreciate the reviewers’ insightful question. Currently, not much is known about the molecular pathways and downstream cellular events triggered by ADM binding to RAMP2 in inhibitory neurons, and in general in brain cells. The data from our study brings the first information about the cell-type specific expression of ADM in baseline and hypoxic conditions and is one of the key novelties of our study.

While the signaling landscape of ADM in interneurons is largely unexplored, several studies in other (non-brain) cell types have demonstrated that ADM binding to RAMP2 can activate downstream cascades such as the cAMP/PKA/CREB pathway, PI3K/AKT, and ERK/MAPK, all of which are also known to be critical regulators of neuronal development and survival. These previously published data along with our CREB-targeted findings in hypoxic interneurons, suggest ADM–RAMP2 signaling could influence multiple aspects of interneuron biology, but these remain to be evaluated in future studies.

We agree with the reviewer that CREB has a wide range of transcriptional targets. We decided to focus on GABA as a target of CREB for two main reasons, including: (i) GABA signaling has been previously shown to play an important role in the migration of cortical interneurons, and (ii) a previous study by Birey et al. (Cell Stem Cell, 2022) demonstrated that CREB pathway activity is essential for regulating interneuron migration in assembloid models of Timothy Syndrom, thus further providing evidence that dysregulation of CREB activity disrupts migration dynamics.

While our study provides a first step toward uncovering the mechanisms of interneuron migration protection by ADM, we fully acknowledge that future work will be needed to delineate the full spectrum of ADM–RAMP2 downstream signaling events in inhibitory neurons and other brain cells.

(5) Does hypoxia cause any changes to inhibitory neurogenesis (earlier stages than migration?) - this might always be known, but was not discussed.

We appreciate this question from the reviewer; however, this was not something that we focused on in this manuscript due to the already large amount of data included. A separate study focusing on neurogenesis defects and the molecular mechanisms of injury for that specific developmental process would be an important next step.

(6) In the Discussion section, it might be worth detailing to the readers what the functional impact of delayed/reduced migration of inhibitory neurons into the cortex might result in, in terms of functional consequences for neural circuit development.

We thank the Reviewer for the suggestion of detailing the functional impact of reduced inhibitory neuron migration. We will revise the manuscript by incorporating a paragraph about this in the Discussion section.

Reviewer #3 (Recommendations for the authors):

Most of the evidence presented is convincing in supporting the conclusions, and I have only minor suggestions for improvement:

(1) The bulk RNA-seq was performed in hSOs only, which may not fully capture the phenotypes of migrating or migrated interneurons. It would be valuable, if feasible, to sort migrated cells from hSO-hCO assembloids and specifically examine their molecular mediators.

We thank the reviewer for this suggestion. While it is likely that the cellular environment will have some influence on a subset of the molecular changes, based on all the data from the manuscript and our specific target, the RNA-sequencing on hCOs was sufficient to capture essential changes like ADM upregulation. The in-depth exploration on differential responses of migrated versus non-migrated interneurons to hypoxia could be the focus of a different project.

(2) In Figure 3, it is striking that cell-type heterogeneity dominates over hypoxia vs. control conditions. A joint embedding of hSO and hCO cells could provide further insight into molecular differences between migrated and non-migrated interneurons.

We thank the reviewer for this observation and opportunity to clarify. Since we manually separated the assembloids before the analyses, we processed these samples separately. That is why they separate like this. In the revision, we will add data about ADM expression and its receptors’ expression in the hCOs.

(3) It would be helpful to expand the discussion on how closely the migration observed in hSO-hCO assembloids reflects in vivo conditions, and what environmental aspects are absent from this model. This would better frame the interpretation and translational relevance of the findings.

We thank the Reviewer for bringing up this important point. Although the assembloid model offers the unique advantage of allowing the direct investigation of migration patterns of hypoxic interneurons, we fully agree it does not fully recapitulate the in vivo environment. While there are multiple aspects that cannot be recapitulated in vitro at this time (e.g. cellular complexity, vasculature, immune response, etc), we are encouraged by the validation of our main findings in ex vivo developing human brain tissue, which strongly supports the validity of our findings for in vivo conditions.

We will expand our discussion to include more details and the need to validate these findings using in vivo models, while also acknowledging that different species (e.g. rodents versus non-human primates versus humans) might have different responses to hypoxia.

(4) The authors suggest that hypoxia is also associated with delayed interneuron maturation, yet the bulk RNA-seq data primarily reveal stress and hypoxia-related genes. A more detailed discussion of why genes linked to interneuron maturation and function were not strongly affected would clarify this point.

We thank the Reviewer for the opportunity to clarify.

The RNAseq data was performed during the acute stages of hypoxia/reoxygenation and we think a maturation phenotype might be difficult to capture at this point and would require analysis at later in vitro assembloid maturation stages.

Our speculation about a possible maturation defect is based on data from previous studies from developmental biology that showed failure of interneurons to reach their final cortical location within a specified developmental window will impair their integration within the neuronal network, and thus lead to maturation defects and possible elimination by apoptosis.

Since preterm infants suffer from countless hypoxic events over multiple months, we suggest these repetitive events are likely to induce cumulative delays in migration, inability of interneurons to reach their target in time, followed by abnormal integration within the excitatory network, and eventual elimination of some of these interneurons through apoptosis. However, the direct demonstration of this effect following a hypoxic insult would require prolonged in vivo experiments in rodents to follow the migration, network integration and apoptosis of interneurons; to our knowledge this experimental design is not technically feasible at this time.

(5) Relatedly, while the focus on interneuron migration is well justified, acknowledging how hypoxia might also impact other aspects of cortical development (e.g., progenitor proliferation, neuronal maturation, or circuit integration) would place the findings in a broader developmental framework and strengthen their relevance.

We appreciate the Reviewer’s suggestion to discuss the role of hypoxia on other processes during cortical development. In the revised manuscript, we will include citations about the effects of hypoxia on interneuron proliferation, maturation and circuit integration as available, and also expand to other cell types known to be affected.

(6) Very minor: in Figure S3C and D, it was not stated what the colors mean (grey: control, yellow: hypoxia)

Thank you for pointing out this error and we will correct it in our revision.

This manuscript examines preprint review services and their role in the scholarly communications ecosystem.  It seems quite thorough to me. In Table 1 they list many peer-review services that I was unaware of e.g. SciRate and Sinai Immunology Review Project.

To help elicit critical & confirmatory responses for this peer review report I am trialling Elsevier’s suggested “structured peer review” core questions, and treating this manuscript as a research article.

Introduction

1. Is the background and literature section up to date and appropriate for the topic?

   Yes.

2. Are the primary (and secondary) objectives clearly stated at the end of the introduction?

   No. Instead the authors have chosen to put the two research questions on page 6 in the methods section. I wonder if they ought to be moved into the introduction – the research questions are not methods in themselves. Might it be better to state the research questions first and then detail the methods one uses to address those questions afterwards? [as Elsevier’s structured template seems implicitly to prefer.

Methods

1. Are the study methods (including theory/applicability/modelling) reported in sufficient detail to allow for their replicability or reproducibility?

   I note with approval that the version number of the software they used (ATLAS.ti) was given.

   I note with approval that the underlying data is publicly archived under CC BY at figshare.

   The Atlas.ti report data spreadsheet could do with some small improvement – the column headers are little cryptic e.g. “Nº  ST “ and “ST” which I eventually deduced was Number of Schools of Thought and Schools of Thought (?)   

   Is there a rawer form of the data that could be deposited with which to evidence the work done? The Atlas.ti report spreadsheet seemed like it was downstream output data from Atlas.ti. What was the rawer input data entered into Atlas.ti? Can this be archived somewhere in case researchers want to reanalyse it using other tools and methods.

   I note with disapproval that Atlas.ti is proprietary software which may hinder the reproducibility of this work. Nonetheless I acknowledge that Atlas.ti usage is somewhat ‘accepted’ in social sciences despite this issue.

   I think the qualitative text analysis is a little vague and/or under-described: “Using ATLAS.ti Windows (version 23.0.8.0), we carried out a qualitative analysis of text from the relevant sites, assigning codes covering what they do and why they have chosen to do it that way.” That’s not enough detail. Perhaps an example or two could be given? Was inter-rater reliability performed when ‘assigning codes’ ? How do we know the ‘codes’ were assigned accurately?

2. Are statistical analyses, controls, sampling mechanism, and statistical reporting (e.g., P-values, CIs, effect sizes) appropriate and well described?

   This is a descriptive study (and that’s fine) so there aren’t really any statistics on show here other than simple ‘counts’ (of Schools of Thought) in this manuscript. There are probably some statistical processes going on within the proprietary qualitative analysis of text done in ATLAS.ti but it is under described and so hard for me to evaluate. 

Results

1. Is the results presentation, including the number of tables and figures, appropriate to best present the study findings?

   Yes. However, I think a canonical URL to each service should be given.  A URL is very useful for disambiguation, to confirm e.g. that the authors mean this Hypothesis (www.hypothes.is) and NOT this Hypothesis (www.hyp.io). I know exactly which Hypothesis is the one the authors are referring to but we cannot assume all readers are experts 😊

   Optional suggestion: I wonder if the authors couldn’t present the table data in a slightly more visual and/or compact way? It’s not very visually appealing in its current state. Purely as an optional suggestion, to make the table more compact one could recode the answers given in one or more of the columns 2, 3 and 4 in the table e.g. "all disciplines = ⬤ , biomedical and life sciences = ▲, social sciences =  ‡  , engineering and technology = † ". I note this would give more space in the table to print the URLs for each service that both reviewers have requested.

   ———————————————————————————————

   | Service name | Developed by | Scientific disciplines | Types of outputs |

   | Episciences | Other | ⬤ | blah blah blah. |

   | Faculty Opinions | Individual researcher | ▲ | blah blah blah. |

   | Red Team Market | Individual researcher | ‡ | blah blah blah. |

   ———————————————————————————————

   The "Types of outputs" column might even lend themselves to mini-colour-pictograms (?) which could be more concise and more visually appealing? A table just of text, might be scientifically 'correct' but it is incredibly dull for readers, in my opinion.

2. Are additional sub-analyses or statistical measures needed (e.g., reporting of CIs, effect sizes, sensitivity analyses)?

   No / Not applicable. 

Discussion

1. Is the interpretation of results and study conclusions supported by the data and the study design?

   Yes.

2. Have the authors clearly emphasized the limitations of their study/theory/methods/argument?

   No. Perhaps a discussion of the linguistic/comprehension bias of the authors might be appropriate for this manuscript. What if there are ‘local’ or regional Chinese, Japanese, Indonesian or Arabic language preprint review services out there? Would this authorship team really be able to find them?

Additional points:

• Perhaps the points made in this manuscript about financial sustainability (p24) are a little too pessimistic. I get it, there is merit to this argument, but there is also some significant investment going on there if you know where to look. Perhaps it might be worth citing some recent investments e.g. Gates -> PREreview (2024) https://content.prereview.org/prereview-welcomes-funding/  and Arcadia’s $4 million USD to COAR for the Notify Project which supports a range of preprint review communities including Peer Community In, Episciences, PREreview and Harvard Library.  (source: https://coar-repositories.org/news-updates/coar-welcomes-significant-funding-for-the-notify-project/ ) 

• Although I note they are mentioned, I think more needs to be written about the similarity and overlap between ‘overlay journals’ and preprint review services. Are these arguably not just two different terms for kinda the same thing? If you have Peer Community In which has it’s overlay component in the form of the Peer Community Journal, why not mention other overlay journals like Discrete Analysis and The Open Journal of Astrophysics.   I think Peer Community In (& it’s PCJ) is the go-to example of the thin-ness of the line the separates (or doesn’t!) overlay journals and preprint review services. Some more exposition on this would be useful.

Thank you very much for the opportunity to review the preprint titled “Preprint review services: Disrupting the scholarly communication landscape?” (https://doi.org/10.31235/osf.io/8c6xm) The authors review services that facilitate peer review of preprints, primarily in the STEM (science, technology, engineering, and math) disciplines. They examine how these services operate and their role within the scholarly publishing ecosystem. Additionally, the authors discuss the potential benefits of these preprint peer review services, placing them in the context of tensions in the broader peer review reform movement. The discussions are organized according to four “schools of thought” in peer review reform, as outlined by Waltman et al. (2023), which provides a useful framework for analyzing the services. In terms of methodology, I believe the authors were thorough in their search for preprint review services, especially given that a systematic search might be impractical.

As I see it, the adoption of preprints and reforming peer review are key components of the move towards improving scholarly communication and open research. This article is a useful step along that journey, taking stock of current progress, with a discussion that illuminates possible paths forward. It is also well-structured and easy for me to follow. I believe it is a valuable contribution to the metaresearch literature.

On a high level, I believe the authors have made a reasonable case that preprint review services might make peer review more transparent and rewarding for all involved. Looking forward, I would like to see metaresearch which gathers further evidence that these benefits are truly being realised.

In this review, I will present some general points which merit further discussion or clarification to aid an uninitiated reader. Additionally, I raise one issue regarding how the authors framed the article and categorised preprint review services and the disciplines they serve. In my view, this problem does not fundamentally undermine the robust search, analyses, and discussion in this paper, but it risks putting off some researchers and constrains how broadly one should derive conclusions.

General comments

Some metaresearchers may be aware of preprints, but not all readers will be familiar with them. I suggest briefly defining what they are, how they work, and which types of research have benefited from preprints, similar to how “preprint review service” is clearly defined in the introduction.

Regarding Waltman et al.’s (2023) “Equity & Inclusion” school of thought, does it specifically aim for “balanced” representation by different groups as stated in this article? There is an important difference between “balanced” versus “equitable” representation, and I would like to see it addressed in this text.

Another analysis I would like to see is whether any of the 23 services reviewed present any evidence that their approach has improved research quality. For instance, the discussion on peer review efficiency and incentives states that there is currently “no hard evidence” that journals want to utilise reviews by Rapid Reviews: COVID-19, and that “not all journals are receptive” to partnerships. Are journals skeptical of whether preprint review services could improve research quality? Or might another dynamic be at work?

The authors cite Nguyen et al. (2015) and Okuzaki et al. (2019), stating that peer review is often “overloaded”. I would like to see a clearer explanation by what “overloaded” means in this context so that a reader does not have to read the two cited papers.

To the best of my understanding, one of the major sticking points in peer review reform is whether to anonymise reviewers and/or authors. Consequently, I appreciate the comprehensive discussion about this issue by the authors.

However, I am only partially convinced by the statement that double anonymity is “essentially incompatible” with preprint review. For example, there may be, as yet not fully explored, ways to publish anonymous preprints with (a) a notice that it has been submitted to, or is undergoing, peer review; and (b) that the authors will be revealed once peer review has been performed (e.g. at least one review has been published). This would avoid the issue of publishing only after review is concluded as is the case for Hypothesis and Peer Community In.

Additionally, the authors describe 13 services which aim to “balance transparency and protect reviewers’ interests”. This is a laudable goal, but I am concerned that framing this as a “balance” implies a binary choice, and that to have more of one, we must lose an equal amount of the other. Thinking only in terms of “balance” prevents creative, win-win solutions. Could a case be made for non-anonymity to be complemented by a reputation system for authors and reviewers? For example, major misconduct (e.g. retribution against a critical review) would be recorded in that system and dissuade bad actors. Something similar can already be seen in the reviewer evaluation system of CrowdPeer, which could plausibly be extended or modified to highlight misconduct.

I also note that misconduct and abusive behaviour already occur even in fully or partially anonymised peer review, and they are not limited to the review or preprints. While I am not aware of existing literature on this topic, academics’ fears seem reasonable. For example, there is at least anecdotal testimonies that a reviewer would deliberately reject a paper to retard the progress of a rival research group, while taking the ideas of that paper and beating their competitors to winning a grant. Or, a junior researcher might refrain from giving a negative review out of fear that the senior researcher whose work they are reviewing might retaliate. These fears, real or not, seem to play a part in the debates about if and how peer review should (or should not) be anonymised. I would like to see an exploration of whether de-anonimisation will improve or worsen this behaviour and in what contexts. And if such studies exist, it would be good to discuss them in this paper.

I found it interesting that almost all preprint review services claim to be complementary to, and not compete with, traditional journal-based peer review. The methodology described in this article cannot definitely explain what is going on, but I suspect there may be a connection between this aversion to compete with traditional journals, and (a) the skepticism of journals towards partnering with preprint review services and (b) the dearth of publisher-run options. I hypothesise that there is a power dynamic at play, where traditional publishers have a vested interest in maintaining the power they hold over scholarly communication, and that preprint review services stress their complementarity (instead of competitiveness) as a survival mechanism. This may be an avenue for further metaresearch.

To understand preprints from which fields of research are actually present on the services categorised under “all disciplines,” I used the Random Integer Set Generator by the Random.org true random number service (https://www.random.org/integer-sets/) to select five services for closer examination: Hypothesis, Peeriodicals, PubPeer, Qeios, and Researchers One. Of those, I observed that Hypothesis is an open source web annotation service that allows commenting on and discussion of any web page on the Internet regardless of whether it is research or preprints. Hypothesis has a sub-project named TRiP (Transparent Review in Preprints), which is their preprint review service in collaboration with Cold Spring Harbor Laboratory. It is unclear to me why the authors listed Hypothesis as the service name in Table 1 (and elsewhere) instead of TRiP (or other similar sub-projects). In addition, Hypothesis seems to be framed as a generic web annotation service that is used by some as a preprint review tool. This seems fundamentally different from others who are explicitly set up as preprint review services. This difference seems noteworthy to me.

To aid readers, I also suggest including hyperlinks to the 23 services reviewed in this paper. My comments on disciplinary representation in these services are elaborated further below.

One minor point of curiosity is that several services use an “automated tool” to select reviewers. It would be helpful to describe in this paper exactly what those tools are and how they work, or report situations where services do not explain it.

Lastly, what did the authors mean by “software heritage” in section 6? Are they referring to the organisation named Software Heritage (https://www.softwareheritage.org/) or something else? It is not clear to me how preprint reviews would be deposited in this context.

Respecting disciplinary and epistemic diversity

In the abstract and elsewhere in the article, the authors acknowledge that preprints are gaining momentum “in some fields” as a way to share “scientific” findings. After reading this article, I agree that preprint review services may disrupt publishing for research communities where preprints are in the process of being adopted or already normalised. However, I am less convinced that such disruption is occurring, or could occur, for scholarly publishing more generally.

I am particularly concerned about the casual conflation of “research” and “scientific research” in this article. Right from the start, it mentions how preprints allow sharing “new scientific findings” in the abstract, stating they “make scientific work available rapidly.” It also notes that preprints enable “scientific work to be accessed in a timely way not only by scientists, but also…” This framing implies that all “scholarly communication,” as mentioned in the title, is synonymous with “scientific communication.” Such language excludes researchers who do not typically identify their work as “scientific” research. Another example of this conflation appears in the caption for Figure 1, which outlines potential benefits of preprint review services. Here, “users” are defined as “scientists, policymakers, journalists, and citizens in general.” But what about researchers and scholars who do not see themselves as “scientists”?

Similarly, the authors describe the 23 preprint review services using six categories, one of which is “scientific discipline”. One of those disciplines is called “humanities” in the text, and Table 1 lists it as a discipline for Science Open Reviewed. Do the authors consider “humanities” to be a “scientific” discipline? If so, I think that needs to be justified with very strong evidence.

Additionally, Waltman et al.’s four schools of thought for peer review reform works well with the 23 services analysed. However, at least three out of the four are explicitly described as improving “scientific” research.

Related to the above are how the five “scientific disciplines” are described as the “usual organisation” of the scholarly communication landscape. On what basis should they be considered “usual”? In this formulation, research in literature, history, music, philosophy, and many other subjects would all be lumped together into the “humanities”, which sit at the same hierarchical level as “biomedical and life sciences”, arguably a much more specific discipline. My point is not to argue for a specific organisation of research disciplines, but to highlight a key epistemic assumption underlying the whole paper that comes across as very STEM-centric (science, technology, engineering, and math).

How might this part of the methodology affect the categories presented in Table 1? “Biomedical and life sciences” appear to be overrepresented compared to other “disciplines”. I’d like to see a discussion that examines this pattern, and considers why preprint review services (or maybe even preprints more generally) appear to cover mostly the biomedical or physical sciences.

In addition, there are 12 services described as serving “all disciplines”. I believe this paper can be improved by at least a qualitative assessment of the diversity of disciplines actually represented on those services. Because it is reported that many of these service stress improving the “reproducibility” of research, I suspect most of them serve disciplines which rely on experimental science.

I randomly selected five services for closer examination, as mentioned above. Of those, only Qeios has demonstrated an attempt to at least split “arts and humanities” into subfields. The others either don’t have such categories altogether, or have a clear focus on a few disciplines (e.g. life sciences for Hypothesis/TRiP). In all cases I studied, there is a heavy focus on STEM subjects, especially biology or medical research. However, they are all categorised by the authors as serving “all disciplines”.

If preprint review services originate from, or mostly serve, a narrow range of STEM disciplines (especially experiment-based ones), it would be worth examining why that is the case, and whether preprints and reviews of them could (or could not) serve other disciplines and epistemologies.

It is postulated that preprint review services might “disrupt the scholarly communication landscape in a more radical way”. Considering the problematic language I observed, what about fields of research where peer-reviewed journal publications are not the primary form of communication? Would preprint review services disrupt their scholarly communications?

To be clear, my concern is not just the conflation of language in a linguistic sense but rather inequitable epistemic power. I worry that this conflation would (a) exclude, minoritise, and alienate researchers of diverse disciplines from engaging with metaresearch; and (b) blind us from a clear pattern in these 23 services, that is their strong focus on the life sciences and medical research and a discussion of why that might be the case. Critically, what message are we sending to, for example, a researcher of 18th century French poetry with the language and framing of this paper? I believe the way “disciplines” are currently presented here poses a real risk of devaluing and minoritising certain subject areas and ways of knowing. In its current form, I believe that while this paper is a very valuable contribution, one should not derive from it any conclusions which apply to scholarly publishing as a whole.

The authors have demonstrated inclusive language elsewhere. For example, they have consciously avoided “peer” when discussing preprint review services, clearly contrasting them to “journal-based peer review”. Therefore, I respectfully suggest that similar sensitivity be adopted to avoid treating “scientific research” and “research” as the same thing. A discussion, or reference to existing works, on the disciplinary skew of preprints (and reviews of them) would also add to the intellectual rigour of this already excellent piece.

Overall, I believe this paper is a valuable reflection on the state of preprints and services which review them. Addressing the points I raised, especially the use of more inclusive language with regards to disciplinary diversity, would further elevate its usefulness in the metaresearch discourse. Thank you again for the chance to review.

Signed:

Dr Pen-Yuan Hsing (ORCID ID: 0000-0002-5394-879X)

University of Bristol, United Kingdom

Data availability

I have checked the associated dataset, but still suggest including hyperlinks to the 23 services analysed in the main text of this paper.

In "Researchers Are Willing to Trade Their Results for Journal Prestige: Results from a Discrete Choice Experiment", the authors investigate researchers’ publication preferences using a discrete choice experiment in a cross-sectional survey of international health and medical researchers. The study investigates publishing decisions in relation to negotiation of trade-offs amongst various factors like journal impact factor, review helpfulness, formatting requirements, and usefulness for promotion in their decisions on where to publish. The research is timely; as the authors point out, reform of research assessment is currently a very active topic. The design and methods of the study are suitable and robust. The use of focus groups and interviews in developing the attributes for study shows care in the design. The survey instrument itself is generally very well-designed, with important tests of survey fatigue, understanding (dominant choice task) and respondent choice consistency (repeat choice task) included. Respondent performance was good or excellent across all these checks. Analysis methods (pMMNL and latent class analysis) are well-suited to the task. Pre-registration and sharing of data and code show commitment to transparency. Limitations are generally well-described.

In the below, I give suggestions for clarification/improvement. Except for some clarifications on limitations and one narrower point (reporting of qualitative data analysis methods), my suggestions are only that – the preprint could otherwise stand, as is, as a very robust and interesting piece of scientific work.

1. Respondents come from a broad range of countries (63), with 47 of those countries represented by fewer than 10 respondents. Institutional cultures of evaluation can differ greatly across nations. And we can expect variability in exposure to the messages of DORA (seen, for example, in level of permeation of DORA as measured by signatories in each country, https://sfdora.org/signers/)..%3B!!NVzLfOphnbDXSw!HdeyeHHei6yWQHFjhN3deSSfp82ur9i9JNOLEVOYZN0BvyslUO2S8DlvjBbautmafJEvlUsxQZbT0JLQX7lO8EcOYtZsJkA%24&data=05%7C02%7Ca.l.brasil.varandas.pinto%40cwts.leidenuniv.nl%7C9f47a111adec49d04bb608dd0614ae94%7Cca2a7f76dbd74ec091086b3d524fb7c8%7C0%7C0%7C638673408085242099%7CUnknown%7CTWFpbGZsb3d8eyJFbXB0eU1hcGkiOnRydWUsIlYiOiIwLjAuMDAwMCIsIlAiOiJXaW4zMiIsIkFOIjoiTWFpbCIsIldUIjoyfQ%3D%3D%7C0%7C%7C%7C&sdata=by5mhPfSM0MFFG9LE2iiYjdtSs5IhvpuukqVv%2FLak2s%3D&reserved=0 "https://eur03.safelinks.protection.outlook.com/?url=https%3A%2F%2Furldefense.com%2Fv3%2F__https%3A%2F%2Fsfdora.org%2Fsigners%2F).%3B!!NVzLfOphnbDXSw!HdeyeHHei6yWQHFjhN3deSSfp82ur9i9JNOLEVOYZN0BvyslUO2S8DlvjBbautmafJEvlUsxQZbT0JLQX7lO8EcOYtZsJkA%24&data=05%7C02%7Ca.l.brasil.varandas.pinto%40cwts.leidenuniv.nl%7C9f47a111adec49d04bb608dd0614ae94%7Cca2a7f76dbd74ec091086b3d524fb7c8%7C0%7C0%7C638673408085242099%7CUnknown%7CTWFpbGZsb3d8eyJFbXB0eU1hcGkiOnRydWUsIlYiOiIwLjAuMDAwMCIsIlAiOiJXaW4zMiIsIkFOIjoiTWFpbCIsIldUIjoyfQ%3D%3D%7C0%7C%7C%7C&sdata=by5mhPfSM0MFFG9LE2iiYjdtSs5IhvpuukqVv%2FLak2s%3D&reserved=0") In addition, some contexts may mandate or incentivise publication in some venues using measures including IF, but also requiring journals to be in certain databases like WoS or Scopus, or having preferred journal lists). I would suggest the authors should include in the Sampling section a rationale for taking this international approach, including any potentially confounding factors it may introduce, and then adding the latter also in the limitations.

2. Reporting of qualitative results: In the introduction and methods, the role of the focus groups and interviews seems to have been just to inform the design of the experiment. But then, results from that qualitative work then appear as direct quotes within the discussion to contextualise or explain results. In this sense though, the qualitative results are being used as new data. Given this, I feel that the methods section should include description of the methods and tools used for qualitative data analysis (currently it does not). But in addition, to my understanding (and this may be a question of disciplinary norms – I’m not a health/medicine researcher), generally new data should not be introduced in the discussion section of a research paper. Rather the discussion is meant to interpret, analyse, and provide context for the results that have already been presented. I personally hence feel that the paper would benefit from the qualitative results being reported separately within the results section.

3. Impact factors – Discussion section: While there is interesting new information on the relative trade-offs amongst other factors, the most emphasised finding, that impact factors still play a prominent role in publication venue decisions, is hardly surprising. More could perhaps be done to compare how the levels of importance reported here differ with previous results from other disciplines or over time (I know a like-for-like comparison is difficult but other studies have investigated these themes, e.g., https://doi.org/10.1177/01655515209585). In addition, beyond the question of whether impact factors are important, a more interesting question in my view is why they still persist. What are they used for and why are they still such important “driver[s] of researchers’ behaviour”? This was not the authors’ question, and they do provide some contextualisation by quoting their participants, but still I think they could do more to contextualise what is known from the literature on that to draw out the implications here. The attribute label in the methods for IF is “ranking”, but ranking according of what and for what? Not just average per-article citations in a journal over a given time frame. Rather, impact factors are used as a proxy indicators of less-tangible desirable qualities – certainly prestige (as the title of this article suggests), but also quality, trust (as reported by one quoted focus group member “I would never select a journal without an impact factor as I always publish in journals that I know and can trust that are not predatory”, p.6), journal visibility, importance to the field, or improved chances of downstream citations or uptake in news media/policy/industry etc. Picking apart the interactions of these various factors in researchers’ choices to make use of IFs (which is not in all cases bogus or unjustified) could add valuable context. I’d especially recommend engaging at least briefly with more work from Science and Technology Studies - especially Müller and de Rijcke’s excellent Thinking with Indicators study (doi: 10.1093/reseval/rvx023), but also those authors other work, as well as work from Ulrike Felt, Alex Rushforth (esp https://doi.org/10.1007/s11024-015-9274-5), Björn Hammerfelt and others.

4. Disciplinary coverage: (1) A lot of the STS work I talk about above emphasises epistemic diversity and the ways cultures of indicator use differ across disciplinary traditions. For this reason, I think it should be pointed out in the limitations that this is research in Health/Med only, with questions on generalisability to other fields. (2) Also, although the abstract and body of the article do make clear the disciplinary focus, the title does not. Hence, I believe the title should be slightly amended (e.g., “Health and Medical Researchers Are Willing to Trade …”)

We’re constantly surrounded by media images so it’s easy to take them for granted. I think Hall is saying for us to take a step back and think critically about what they show and why.

Author response:

The following is the authors’ response to the previous 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 between different 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 high-throughput 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 re-testing, "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{degree sign}C and 32{degree sign}C are correlated by 0.263, which corresponds to an R2 of 0.069 i.e. just 7% of the 32{degree sign}C variance is predictable by the 23{degree sign}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 inter-individual 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 in-group 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 re-wording 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 open-hardware 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 interindividual 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 interindividual 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:  

I want to express my appreciation for the authors' responsiveness to the reviewer feedback. They appear to have addressed my previous concerns through various modifications including GLM analysis, however, some areas still require clarification for the benefit of an audience that includes geneticists.  

(1) GLM Analysis Explanation (Figure 9)  

While the authors state that their new GLM results support their original conclusions, the explanation of these results in the text is insufficient. Specifically:

The interpretation of coefficients and their statistical significance needs more detailed explanation. The audience includes geneticists and other nonstatistical people, so the GLM should be explained in terms of the criteria or quantities used to assess how well the results conform with the hypothesis, and to what extent they diverge.

The criteria used to judge how well the GLM results support their hypothesis are not clearly stated.

The relationship between the GLM findings and their original correlationbased conclusions needs better integration and connection, leading the reader through your reasoning.

We thank the reviewer for highlighting this important point. We have revised the Results section in the reviseed manuscript to include a more detailed explanation of the GLM analysis. Specifically, we now clarify the interpretation of the model coefficients, including the direction and statistical significance, in relation to the hypothesized effects. We also outline the criteria we used to assess how well the GLM supports our original correlation-based conclusions—namely, whether the sign and significance of the coefficients align with the expected relationships derived from our prior analysis. Finally, we explicitly describe how the GLM results confirm or extend the patterns observed in the correlation-based analysis, to guide readers through our reasoning and the integration of both approaches.

(2) Documentation of Changes  

One struggle with the revised manuscript is that no "tracked changes" version was included, so it is hard to know exactly what was done. Without access to the previous version of the manuscript, it is difficult to fully assess the extent of revisions made. The authors should provide a more comprehensive summary of the specific changes implemented, particularly regarding:

We thank the reviewer for bringing this to our attention. We were equally confused to learn that the tracked-changes version was not visible, despite having submitted one to eLife as part of our revision. 

Upon contacting the editorial office, they confirmed that we did submit a trackedchanges version, but clarified that it did not contain embedded figures (as they were added manually to the clean version).  The editorial response said in detail: “Regarding the tracked-changes file: it appears the version with markup lacked figures, while the figure-complete PDF had markup removed, which likely caused the confusion mentioned by the reviewers.” We hope this answer from eLife clarifies the reviewers’ concern.

(2)  Statistical Method Selection  

The authors mention using "ridge regression to mitigate collinearity among predictors" but do not adequately justify this choice over other approaches. They should explain:

Why ridge regression was selected as the optimal method  

How the regularization parameter (λ) was determined  

How this choice affects the interpretation of environmental parameters' influence on individuality

We appreciate the reviewer’s thoughtful question regarding our choice of statistical method. In response, we have expanded the Methods section in the revised manuscript to provide a more detailed justification for the use of a GLM, including ridge regression. Specifically, we explain that ridge regression was selected to address collinearity and to control for overfitting.

We now also describe how the regularization parameter (λ) was selected: we used 5-fold cross-validation over a log-spaced grid (10^⁻⁶ - 10<sup>⁶</sup) to identify the optimal value that minimized the mean squared error (MSE).

Finally, we clarify in both the Methods and Results sections how this modeling choice affects the interpretation of our findings. 

Reviewer #2 (Public review):  

Summary:  

The authors repeatedly 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 anti-conservative 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 within-individual 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 changed, 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

Reviewer #3 (Public review):  

This manuscript is a continuation of past work by the last author where they looked at stochasticity in developmental processes leading to inter-individual behavioural differences. In that work, the focus was on a specific behaviour under specific conditions while probing the neural basis of the variability. In this work, the authors set out to describe in detail how stable individuality of animal behaviours is in the context of various external and internal influences. They identify a few behaviours to monitor (read outs of attention, exploration, and 'anxiety'); some external stimuli (temperature, contrast, nature of visual cues, and spatial environment); and two internal states (walking and flying).

They then use high-throughput behavioural arenas - most of which they have built and made plans available for others to replicate - to quantify and compare combinations of these behaviours, stimuli, and internal states. This detailed analysis reveals that:

(1) Many individualistic behaviours remain stable over the course of many days.  

(2) That some of these (walking speed) remain stable over changing visual cues. Others (walking speed and centrophobicity) remain stable at different temperatures.

(3) All the behaviours they tested fail to remain stable over spatially varying environment (arena shape).

(4) and only angular velocity (a read out of attention) remains stable across varying internal states (walking and flying)

Thus, the authors conclude that there is a hierarchy in the influence of external stimuli and internal states on the stability of individual behaviours.

The manuscript is a technical feat with the authors having built many new high-throughput assays. The number of animals are large and many variables have been tested - different types of behavioural paradigms, flying vs walking, varying visual stimuli, different temperature among others.  

Comments on revisions:'  

The authors have addressed my previous concerns.  

We thank the reviewer for the positive feedback and are glad our revisions have satisfactorily addressed the previous concerns. We appreciate the thoughtful input that helped us improve the clarity and rigor of the manuscript.

Reviewer #1 (Recommendations for the authors):  

Comment on Revised Manuscript  

Recommendations for Improvement  

(1) Expand the Results section for Figure 9 with a more detailed interpretation of the GLM coefficients and their biological significance

(2) Provide explicit criteria (or at least explain in detail) for how the GLM results confirm or undermine their original hypothesis about environmental context hierarchy

While the claims are interesting, the additional statistical analysis appears promising. However, clearer explanation of these new results would strengthen the paper and ensure that readers from diverse backgrounds can fully understand how the evidence supports the authors' conclusions about individuality across environmental contexts. 

We thank the reviewer for these constructive suggestions. In response to these suggestions, we have expanded both the Methods and Results sections to provide a more detailed explanation of the GLM coefficients, including their interpretation and how they relate to our original correlation-based findings.

We now clarify how the direction, magnitude, and statistical significance of specific coefficients reflect the influence of different environmental factors on the persistence of individual behavioral traits. To make this accessible to readers from diverse backgrounds, we explicitly outline the criteria we used to evaluate whether the GLM results support our hypothesis about the hierarchical influence of environmental context, namely, whether the structure and strength of effects align with the patterns predicted from our prior correlation analysis.

These additions improve clarity and help readers understand how the new statistical results reinforce our conclusions about the context-dependence of behavioral individuality.

Reviewer #2 (Recommendations for the authors):  

Thanks for the revision of the paper! I updated my review to try and provide a little more guidance by what I mean about updating your analyses. I really think this is a super cool data set and I genuinely wish this were MY dataset so that way I could really dig into it to partition the variance. These variance partitioning methods are standard in my particular subfield (study of individual behavioral variation in ecology and evolution) and so I think employing them is 1) going to offer a MUCH more elegant and holistic view of the behavioral variation (e.g. you can report a single repeatability estimate for each behavior rather than 3 different correlations) and 2) improve the impact and readership for your paper as now you'll be using methods that a whole community of researchers are very familiar with. It's just a suggestion, but I hope you consider it!

We sincerely thank the reviewer for the insightful and encouraging feedback and for introducing us to this modeling approach. In response to this suggestion, we have incorporated a hierarchical linear mixed-effects model into our analysis (now presented in Figure 10), accompanied by a new supplementary table (Table T3). We also updated the Methods, Results, and Discussion sections to describe the rationale, implementation, and implications of the mixed-model analysis.

We agree with the reviewer that this approach provides a more elegant way to quantify behavioral variation and individual consistency across contexts. In particular, the ability to estimate repeatability directly aligns well with the core questions of our study. It facilitates improved communication of our findings to ecology, evolution, and behavior researchers. We greatly appreciate the suggestion; it has significantly strengthened both the analytical framework and the interpretability of the manuscript.

This is why I think it's important to survey your students at the beginning of the year in order to learn about their interests. Gaining insight into how your students learn best can help you, as the teacher, vary your teaching methods. Yes, habits can be good so students can know what the expectations are, but offering different sources, different instructional strategies, and diversifying your classroom layout can cover a wide range of learners. Keeping in mind that people learn through all of the major senses can truly help students retain information. For example, I am an auditory learner. I have to read aloud or talk things out. That's why I have to read things a few times to really grasp the material when it's a quiet setting. Therefore, timed tests really get my anxiety levels up. Not everyone has this problem or even recognizes it. Being an auditory learner may be great in the college setting during lectures, but it becomes very difficult in the test setting when everything is quiet. How could a teacher make an adjustment in the test setting for my scenario?

Author response:

The following is the authors’ response to the previous reviews

Reviewer #1 (Public review):

This work addresses an important question in the field of Drosophila aggression and mating. Prior social isolation is known to increase aggression in males, manifesting as increased lunging, which is suppressed by group housing (GH). However, it is also known that single housed (SH) males, despite their higher attempts to court females, are less successful. Here, Gao et al., develop a modified aggression assay to address this issue by recording aggression in Drosophila males for 2 hours, with a virgin female immobilized by burying its head in the food. They found that while SH males frequently lunge in this assay, GH males switch to higher intensity but very low frequency tussling. Constitutive neuronal silencing and activation experiments implicate cVA sensing Or67d neurons in promoting high frequency lunging, similar to earlier studies, whereas Or47b neurons promote low frequency but higher intensity tussling. Optogenetic activation revealed that three pairs of pC1SS2 neurons increase tussling. Cell-type-specific DsxM manipulations combined with morphological analysis of pC1SS2 neurons and side-by-side tussling quantification link the developmental role of DsxM to the functional output of these aggression-promoting cells. In contrast, although optogenetic activation of P1a neurons in the dark did not increase tussling, thermogenetic activation under visible light drove aggressive tussling. Using a further modified aggression assay, GH males exhibit increased tussling and maintain territorial control, which could contribute to a mating advantage over SH males, although direct measures of reproductive success are still needed.

Strengths:

Through a series of clever neurogenetic and behavioral approaches, the authors implicate specific subsets of ORNs and pC1 neurons in promoting distinct forms of aggressive behavior, particularly tussling. They have devised a refined territorial control paradigm, which appears more robust than earlier assays using a food cup (Chen et al., 2002). This new setup is relatively clutter-free and could be amenable to future automation using computer vision approaches. The updated Figure 5, which combines cell-type-specific developmental manipulation of pC1SS2 neurons with behavioral output, provides a link between developmental mechanisms and functional aggression circuits. The manuscript is generally well written, and the claims are largely supported by the data.

Thank you for the precise summary of the manuscript and acknowledgment of the novelty and significance of the study.

Weakness:

Although most concerns have been addressed, the manuscript still lacks a rigorous, objective method for quantifying lunging and tussling. Because scoring appears to have been done manually and a single lunge in a 30 fps video spans only 2-3 frames, the 0.2 s cutoff seems arbitrary, and there are no objective criteria distinguishing reciprocal lunging from tussling. Despite this, the study offers valuable insights into the neural and behavioral mechanisms of Drosophila aggression.

Thank you for this comment. The duration of each lunge was measured by analyzing the videos frame by frame—from the frame before the initiation of the lunge to the frame after its completion—resulting in an average span of 3–5 frames. Given a frame rate of 30 fps, this corresponds to approximately 0.1–0.17 seconds. We acknowledge that there are certain limitations for manually quantifying the two types of aggressive behaviors, which has now been stated in the newly added “Limitations of the Study” section in the revised manuscript.

Reviewer #2 (Public review):

Summary:

Gao et al. investigated the change of aggression strategies by the social experience and its biological significance by using Drosophila. Two modes of inter-male aggression in Drosophila are known: lunging, high-frequency but weak mode, and tussling, low-frequency but more vigorous mode. Previous studies have mainly focused on the lunging. In this paper, the authors developed a new behavioral experiment system for observing tussling behavior and found that tussling is enhanced by group rearing, while lunging is suppressed. They then searched for neurons involved in the generation of tussling. Although olfactory receptors named Or67d and Or65a have previously been reported to function in the control of lunging, the authors found that these neurons do not function in the execution of tussling and another olfactory receptor, Or47b, is required for tussling, as shown by the inhibition of neuronal activity and the gene knockdown experiments. Further optogenetic experiments identified a small number of central neurons pC1[SS2] that induce the tussling specifically. These neurons express doublesex (dsx), a sex-determination factor, and knockdown of dsx strongly suppresses the induction of tussling. In order to further explore the ecological significance of the aggression mode change in group-rearing, a new behavioral experiment was performed to examine the territorial control and the mating competition. And finally, the authors found that differences in the social experience (group vs. solitary rearing) and the associated change in aggression strategy are important in these biologically significant competitions. These results add a new perspective to the study of aggression behavior in Drosophila. Furthermore, this study proposes an interesting general model in which the social experience modified behavioral changes play a role in reproductive success.

Strengths:

A behavioral experiment system that allows stable observation of tussling, which could not be easily analyzed due to its low-frequency, would be very useful. The experimental setup itself is relatively simple, just the addition of a female to the platform, so it should be applicable to future research. The finding about the relationship between the social experience and the aggression mode change is quite novel. Although the intensity of aggression changes with the social experience was already reported in several papers (Liu et al., 2011 etc), the fact that the behavioral mode itself changes significantly has rarely been addressed, and is extremely interesting. The identification of sensory and central neurons required for the tussling makes appropriate use of the genetic tools and the results are clear. A major strength of this study in neurobiology is the finding that another group of neurons (Or47b-expressing olfactory neurons and pC1[SS2] neurons), distinct from the group of neurons previously thought to be involved in low-intensity aggression (i.e. lunging), function in the tussling behavior. Furthermore, the results showing that the regulation of aggression by pC1[SS2] neurons is based on the function of the dsx gene will bring a new perspective to the field. Further investigation of the detailed circuit analysis is expected to elucidate the neural substrate of the conflict between the two aggression modes. The experimental systems examining the territory control and the reproductive competition in Fig. 6 are novel and have advantages in exploring their biological significance. It is important to note that in addition to showing the effects of age and social experience on territorial and mating behaviors, the authors experimentally demonstrated that altered fighting strategy has effects with respect to these behaviors.

Thank you for your precise summary of our study and being very positive on the novelty and significance of the study.

Reviewer #3 (Public review):

In this revised manuscript, Gao et al. presented a series of well-controlled behavioral data showing that tussling, a form of high-intensity fighting among male fruit flies (Drosophila melanogaster) is enhanced specifically among socially experienced and relatively old males. Moreover, results of behavioral assays led authors to suggest that increased tussling among socially experienced males may increase mating success. They also concluded that tussling is controlled by a class of olfactory sensory neurons and sexually dimorphic central neurons that are distinct from pathways known to control lunges, a common male-type attack behavior.

A major strength of this work is that it is the first attempt to characterize behavioral function and neural circuit associated with Drosophila tussling. Many animal species use both low-intensity and high-intensity tactics to resolve conflicts. High-intensity tactics are mostly reserved for escalated fights, which are relatively rare. Because of this, tussling in the flies, like high-intensity fights in other animal species, have not been systematically investigated. Previous studies on fly aggressive behavior have often used socially isolated, relatively young flies within a short observation duration. Their discovery that 1) older (14-days old) flies tend to tussle more often than younger (2 to 7-days-old) flies, 2) group-reared flies tend to tussle more often than socially isolated flies, and 3) flies tend to tussle at later stage (mostly ~15 minutes after the onset of fighting), are the result of their creativity to look outside of conventional experimental settings. These new findings are key for quantitatively characterizing this interesting yet under-studied behavior.

Newly presented data have made several conclusions convincing. Detailed descriptions of methods to quantify behaviors help understand the basis of their claims by improving transparency. However, I remain concerned about authors' persistent attempt to link the high intensity aggression to reproductive success. The authors' effort to "tone down" the link between the two phenomena remains insufficient. There are purely correlational. I reiterate this issue because the overall value of the manuscript would not change with or without this claim.

Thank you for acknowledging the novelty and significance of the study. Regarding the relationship you mentioned between high-intensity aggression and reproductive success, we further toned down the statement between them throughout the manuscript in the revised manuscript. We also modified the title to “Social Experience Shapes Fighting Strategies in Drosophila”. In addition, we now added a ‘Limitations of the Study’ section to clearly state the correlation between tussling and reproductive success.

Reviewer #1 (Recommendations for the authors):

If possible, mention the EM-connectome data showing the minimal interneuronal path from Or47b ORNs to pC1SS2 neurons (even if derived from the female connectome), which can strengthen the model of parallel sensory-central pathways.

Thank you for this comment. According to data from the EM connectome, connecting Or47b ORNs to pC1d neurons requires at least two intermediate neurons. An example minimal pathway is: ORN_VA1v (L) → AL-AST1 (L) → PLP245 (L) → pC1d (R). We have added this point in the Discussion section of the revised manuscript.

I'm not convinced that labeling lunges as "gentle" combat behavior works, either in the abstract or elsewhere. While lunging is indeed a lower-intensity form of aggression compared to tussling, applying anthropomorphic descriptors risks misleading readers.

Thank you for this comment. We now use “low-intensity” instead of “gentle” to describe lunging.

In Materials & Methods, please cross-check all figure-panel references after the recent re-numbering (e.g. "Figure 5A6A" etc.).

Thank you for this comment. We have thoroughly verified the figure panel references in the Materials & Methods section.

Ensure that Table S1 is clearly cited in the main text where you first describe fly genotypes.

Thank you for this comment. We have now cited Table S1 in the main text.

There are multiple grammatical errors and typos throughout the manuscript. Please correct them. Some examples are below, but this is not an exhaustive list:

Line 98-102 requires rephrasing as the results are already published and not being observed by the authors.

Thank you for this comment. We have revised the manuscript to “we occasionally observed the high-intensity boxing and tussling behavior in male flies as previously reported (Chen et al., 2002; Nilsen et al., 2004), which….”

line 116- lower not 'lowed'.

Corrected.

line 942 & 945- knock-down males not 'knocking down males'.

Corrected. Thank you very much for these comments.

Reviewer #2 (Recommendations for the authors):

The authors have almost completely answered the major comments I have noted on the ver.1 manuscript: (1) They clearly show changes in fighting strategy in the territory control behavior experiment in Fig. 6-figure supplements. (2) A detailed description of how aggressive behavior is measured. Thus, I am convinced by this revision.

Thank you for these comments that make the manuscript a better version.

Furthermore, in Fig. 5, which examined the relationship of pC1[SS2] characteristics with the function of dsx, is a novel data and very interesting. I look forward to further developments.

Thank you. We will continue to explore this part in our future study.

However, one point still concerns me.

Line 192: Although the authors describe it as "usage-dependent," the trans-Tango technique is essentially a postsynaptic cell-labeling technique. It is possible that the labeling intensity in postsynaptic cells increases from the change in expression levels of the Or47b gene due to GH. However, there is no difference in the expression level of the Or47b gene labeled by GFP between SH and GH. Therefore, we cannot conclude that the expression of the Or47b gene is increased by rearing conditions.

The original paper on trans-TANGO (Talay et al., 2017) does not discuss the usage-dependency. A review of trans-synaptic labeling techniques (Ni, Front Neural Circuits. 2021) discusses that the increase in trans-TANGO signaling with aging may be related to synaptic strength, but there is no experimental evidence for this. In my opinion, the results in Figure 3-figure supplement 2 only weakly suggest that the increase in trans-TANGO signaling may be explained by an increase in synaptic strength due to group rearing.

We appreciate the reviewer’s insightful comment regarding the interpretation of the trans-Tango signal. Indeed, the original trans-Tango study (Talay et al., 2017) does not claim that the method is usage-dependent. The observed increase in trans-Tango labeling with age, as reported in their supplemental figures, may reflect accumulation over time, potentially influenced by synaptic maturation or increased component expression. To avoid overstating our results, we have revised the relevant statement in the manuscript to remove the term "usage-dependent" and now describe the change in trans-Tango signal more cautiously.  

Reviewer #3 (Recommendations for the authors):

Below are the cases where their professed attempts to "tone down the statement" appear ignored:

Lines 27-29:

"Our findings... suggest how social experience shapes fighting strategies to optimize reproductive success".

We have now revised the manuscript to “Our findings… suggest that social experience may shape fighting strategies to optimize reproductive success.”

Lines 85-86:

"... discover that this infrequent yet intense form of combat is... crucial for territory dominance and mating competition".

We have now revised the manuscript to “…discover that this infrequent yet intense form of combat is enhanced by social enrichment, while the low-intensity lunging is suppressed by social enrichment.” 

Lines 335-339:

"Here, we found that... GH males tend to... increase the high-intensity tussling, which enhances their territorial and mating competition."

We have removed “which enhances their territorial and mating competition” in the revised manuscript.

Lines 343-344:

"... presenting a paradox between social experience, aggression and reproductive success. Our result resolved this paradox..."

We have now revised the manuscript to “...Our results provide an explanation for this paradox…”

Lines 355-358:

"Interestingly, we found that the mating advantage gained through social enrichment can even offset the mating disadvantage associated with aging, further supporting the vital role of shifting fighting strategies in experienced, aged males."

We have removed “further supporting the vital role of shifting fighting strategies in experienced, aged males” in the revised manuscript.

Lines 361-362:

"These results separate the function of the two fighting forms and rectify out understanding of how social experiences regulate aggression and reproductive success."

We have removed this sentence in the revised manuscript.

Some may say that a speculative statement is harmless, but I think it indeed is harmful unless it is clearly indicated as a speculation. It is regrettable that authors remain reluctant to change their claim without providing any new supporting evidence. All three reviewers raised the same concern in the first round of review.

We apologize for not making the speculative nature of the statement clearer in the previous version. In the revised manuscript, we have now explicitly rephrased sentences to only suggest a correlation but not a causal link between tussling and reproductive success.

I have no choice but to keep my evaluation of the manuscript as "Incomplete" unless the authors thoroughly eliminate any attempt to link these two. This must go beyond changing a few words in the lines listed above.

Thank you for this comment. In addition to the lines listed above, we carefully checked all statements regarding the correlation between fighting strategies and reproductive success throughout the full text. Furthermore, we have also added a “Limitations of the Study” section to address the shortcomings of this study in the revised manuscript.

I do not have the same level of concern over the interpretation of Fig. 6A-C, because this is directly linked to aggressive interactions. Even if the socially isolated males do not engage in tussling, it is not a leap to assume that a different fighting tactic of socially experienced males can give them an advantage in defending a territory. To me, this is a sufficient ethological link with the observed behavioral change.

Thank you for this insightful comment.

The following are relatively minor, although important, concerns.

I beg to differ over the authors' definition of "tussling". Supplemental movies S1 and S2 appear to include "tussling" bouts in which 2 flies lunging at each other in rapid succession, and supplemental movie S3 appears to include bouts of "holding", in which one fly holds the opponent's wings and shakes vigorously. These cases suggest that the definition of "tussling" as opposed to "lunging" has a subjective element. However, I would not delve on this matter further because it is impossible to be completely objective over behavioral classification, even by using a computational method. An important point is that the definition is applied consistently within the publication. I have no reason to doubt that this was not the case.

Thank you for this comment. Since the analysis of tussling behavior was conducted manually, it is challenging to achieve complete objectivity. However, we made every effort to apply consistent criteria throughout the analysis. We have added a “Limitations of the Study” section in the revised manuscript to clearly state this caveat. We appreciate your understanding.

Authors now state that "all tester flies were loaded by cold anesthesia" (lines 432-433). I would like to draw attention to the well-known fact that anesthesia, whether by ice or by CO2, are long known to affect fly's subsequent behaviors (for aggression, see Trannoy S. et al., Learn. Mem. 2015. 22: 64-68). It will be prudent to acknowledge the possibility that this handling method could have contributed to unusually high levels of spontaneous tussling, which has not been reported elsewhere before.

Thank you for this comment. The increased tussling behavior observed in our study is unlikely due to cold anesthesia, as noted by Trannoy S. et al. (2015), cold anesthesia profoundly reduces locomotion and general aggressiveness in flies. We acknowledge that the use of cold anesthesia in behavioral experiments may have potential effects on aggression. To minimize this influence, we allowed the flies to recover and adapt for at least 30 minutes before behavioral recording. Moreover, both control and experimental groups were treated in exactly the same manner to ensure consistency.

It is intriguing that pC1SS2 neurons are dsx+ but fru-. Authors convincingly demonstrated that these neurons are clearly distinct from the P1a neurons, a well-characterized hub for male social behaviors. It is possible that pC1SS2 neurons overlap with previously characterized dsx+ neurons that are important for male aggressions (measured by lunges), such as in Koganezawa et al., Curr. Biol. 2016 and Chiu et al., Cell 2020, a point authors could have explicitly raised.

Thank you for this comment. We have added this point into the Discussion section of the revised manuscript, as follows: “That tussling-promoting… aggression (Koganezawa et al., 2016). Moreover, the anatomical features of pC1^SS2 neurons are highly similar to the male-specific aggression-promoting (MAP) neurons identified by another previous study (Chiu et al., 2021).

I acknowledge the authors' courage to initiate an investigation to a less characterized, high intensity fighting behavior. Tussling requires the simultaneous engagement of two flies. Even if there are confusion over the distinction between lunges and tussling, authors' conclusion that socially experienced flies and socially isolated flies employ distinct fighting strategy is convincing. The concern I raised above is about the interpretation of the data, not about the quality of data.

Thank you for your constructive comments to make this manuscript better.

brainstorm on how to wirte a narrative

its open, and able to move freely and merge with other genres or ideas

Author response:

Reviewer #1 (Public Review):

Summary:

The present study evaluates the role of visual experience in shaping functional correlations between extrastriate visual cortex and frontal regions. The authors used fMRI to assess "resting-state" temporal correlations in three groups: sighted adults, congenitally blind adults, and neonates. Previous research has already demonstrated differences in functional correlations between visual and frontal regions in sighted compared to early blind individuals. The novel contribution of the current study lies in the inclusion of an infant dataset, which allows for an assessment of the developmental origins of these differences.

The main results of the study reveal that correlations between prefrontal and visual regions are more prominent in the blind and infant groups, with the blind group exhibiting greater lateralization. Conversely, correlations between visual and somato-motor cortices are more prominent in sighted adults. Based on these data, the authors conclude that visual experience plays an instructive role in shaping these cortical networks. This study provides valuable insights into the impact of visual experience on the development of functional connectivity in the brain.

Strengths:

The dissociations in functional correlations observed among the sighted adult, congenitally blind, and neonate groups provide strong support for the study's main conclusion regarding experience-driven changes in functional connectivity profiles between visual and frontal regions.

In general, the findings in sighted adult and congenitally blind groups replicate previous studies and enhance the confidence in the reliability and robustness of the current results.

Split-half analysis provides a good measure of robustness in the infant data.

Weaknesses:

There is some ambiguity in determining which aspects of these networks are shaped by experience.

This uncertainty is compounded by notable differences in data acquisition and preprocessing methods, which could result in varying signal quality across groups. Variations in signal quality may, in turn, have an impact on the observed correlation patterns.

The study's findings could benefit from being situated within a broader debate surrounding the instructive versus permissive roles of experience in the development of visual circuits.

Reviewer #2 (Public Review):

Summary:

Tian et al. explore the developmental organs of cortical reorganization in blindness. Previous work has found that a set of regions in the occipital cortex show different functional responses and patterns of functional correlations in blind vs. sighted adults. In this paper, Tian et al. ask: how does this organization arise over development? Is the "starting state" more like the blind pattern, or more like the adult pattern? Their analyses reveal that the answer depends on the particular networks investigated; some functional connections in infants look more like blind than sighted adults; other functional connections look more like sighted than blind adults; and others fall somewhere in the middle, or show an altogether different pattern in infants compared with both sighted and blind adults. 

Strengths:

The question raised in this paper is extremely important: what is the starting state in development for visual cortical regions, and how is this organization shaped by experience? This paper is among the first to examine this question, particularly by comparing infants not only with sighted adults but also blind adults, which sheds new light on the role of visual (and cross-modal) experience. Another clear strength lies in the unequivocal nature of many results. Many results have very large effect sizes, critical interactions between regions and groups are tested and found, and infant analyses are replicated in split halves of the data. 

Weaknesses:

A central claim is that "infant secondary visual cortices functionally resemble those of blind more than sighted adults" (abstract, last paragraph of intro). I see two potential issues with this claim. First, a minor change: given the approaches used here, no claims should be made about the "function" of these regions, but rather their "functional correlations". Second (and more importantly), the claim that the secondary visual cortex in general resembles blind more than sighted adults is still not fully supported by the data. In fact, this claim is only true for one aspect of secondary visual area functional correlations (i.e., their connectivity to A1/M1/S1 vs. PFC). In other analyses, the infant secondary visual cortex looks more like sighted adults than blind adults (i.e., in within vs. across hemisphere correlations), or shows a different pattern from both sighted and blind adults (i.e., in occipito-frontal subregion functional connectivity). It is not clear from the manuscript why the comparison to PFC vs. non-visual sensory cortex is more theoretically important than hemispheric changes or within-PFC correlations (in fact, if anything, the within-PFC correlations strike me as the most important for understanding the development and reorganization of these secondary visual regions). It seems then that a more accurate conclusion is that the secondary visual cortex shows a mix of instructive effects of vision and reorganizing effects of blindness, albeit to a different extent than the primary visual cortex.

Relatedly, group differences in overall secondary visual cortex connectivity are particularly striking as visualized in the connectivity matrices shown in Figure S1. In the results (lines 105-112), it is noted that while the infant FC matrix is strongly correlated with both adult groups, the infant group is nonetheless more strongly correlated with the blind than sighted adults. I am concerned that these results might be at least partially explained by distance (i.e., local spread of the bold signal), since a huge portion of the variance in these FC matrices is driven by stronger correlations between regions within the same system (e.g., secondary-secondary visual cortex, frontal-frontal cortex), which are inherently closer together, relative to those between different systems (e.g., visual to frontal cortex). How do results change if only comparisons between secondary visual regions and non-visual regions are included (i.e., just the pairs of regions within the bold black rectangle on the figure), which limits the analysis to long-rang connections only? Indeed, looking at the off-diagonal comparisons, it seems that in fact there are three altogether different patterns here in the three groups. Even if the correlation between the infant pattern and blind adult pattern survives, it might be more accurate to claim that infants are different from both adult groups, suggesting both instructive effects of vision and reorganizing effects of blindness. It might help to show the correlation between each group and itself (across independent sets of subjects) to better contextualize the relative strength of correlations between the groups. 

It is not clear that differences between groups should be attributed to visual experience only. For example, despite the title of the paper, the authors note elsewhere that cross-modal experience might also drive changes between groups. Another factor, which I do not see discussed, is possible ongoing experience-independent maturation. The infants scanned are extremely young, only 2 weeks old. Although no effects of age are detected, it is possible that cortex is still undergoing experience-independent maturation at this very early stage of development. For example, consider Figure 2; perhaps V1 connectivity is not established at 2 weeks, but eventually achieves the adult pattern later in infancy or childhood. Further, consider the possibility that this same developmental progression would be found in infants and children born blind. In that case, the blind adult pattern may depend on blindness-related experience only (which may or may not reflect "visual" experience per se). To deal with these issues, the authors should add a discussion of the role of maturation vs. experience and temper claims about the role of visual experience specifically (particularly in the title). 

The authors measure functional correlations in three very different groups of participants and find three different patterns of functional correlations. Although these three groups differ in critical, theoretically interesting ways (i.e., in age and visual/cross-modal experience), they also differ in many uninteresting ways, including at least the following: sampling rate (TR), scan duration, multi-band acceleration, denoising procedures (CompCor vs. ICA), head motion, ROI registration accuracy, and wakefulness (I assume the infants are asleep).

Addressing all of these issues is beyond the scope of this paper, but I do feel the authors should acknowledge these confounds and discuss the extent to which they are likely (or not) to explain their results. The authors would strengthen their conclusions with analyses directly comparing data quality between groups (e.g., measures of head motion and split-half reliability would be particularly effective).

Response #1: We appreciate the reviewer’s comments. In response, we have revised the paper to provide a more balanced summary of the data and clarified in the introduction which signatures the paper focuses on and why. Additionally, we have included several control analyses to account for other plausible explanations for the observed group differences. Specifically, we randomly split the infant dataset into two halves and performed split-half cross-validation. Across all comparisons, the results from the two halves were highly similar, suggesting that the effects are robust (see Supplementary Figures S3 and S4).

Furthermore, we compared the split-half noise ceiling across the groups (infants, sighted adults, and blind adults) and found no significant differences between them (details in response #6). Finally, we repeated our analysis after excluding infants with a radiology score of 4 or 5, and the results remained consistent, indicating that our findings are not confounded by potential brain anomalies (details in response #2).

We hope these control analyses help strengthen our conclusions.

Reviewer #3 (Public Review):

Summary:

This study aimed to investigate whether the differences observed in the organization of visual brain networks between blind and sighted adults result from a reorganization of an early functional architecture due to blindness, or whether the early architecture is immature at birth and requires visual experience to develop functional connections. This question was investigated through the comparison of 3 groups of subjects with resting-state functional MRI (rs-fMRI). Based on convincing analyses, the study suggests that: 1) secondary visual cortices showed higher connectivity to prefrontal cortical regions (PFC) than to non-visual sensory areas (S1/M1 and A1) in sighted infants like in blind adults, in contrast to sighted adults; 2) the V1 connectivity pattern of sighted infants lies between that of sighted adults (stronger functional connectivity with non-visual sensory areas than with PFC) and that of blind adults (stronger functional connectivity with PFC than with non-visual sensory areas); 3) the laterality of the connectivity patterns of sighted infants resembled those of sighted adults more than those of blind adults, but sighted infants showed a less differentiated fronto-occipital connectivity pattern than adults.

Strengths:

The question investigated in this article is important for understanding the mechanisms of plasticity during typical and impaired development, and the approach considered, which compares different groups of subjects including, neonates/infants and blind adults, is highly original.

-Overall, the analyses considered are solid and well-detailed. The results are quite convincing, even if the interpretation might need to be revised downwards, as factors other than visual experience may play a role in the development of functional connections with the visual system.

Weaknesses:

While it is informative to compare the "initial" state (close to birth) and the "final" states in blind and sighted adults to study the impact of post-natal and visual experience, this study does not analyze the chronology of this development and when the specialization of functional connections is completed. This would require investigating when experience-dependent mechanisms are important for the setting- establishment of multiple functional connections within the visual system. This could be achieved by analyzing different developmental periods in the same way, using open databases such as the Baby Connectome Project. Given the early, "condensed" maturation of the visual system after birth, we might expect sighted infants to show connectivity patterns similar to those of adults a few months after birth.

The rationale for mixing full-term neonates and preterm infants (scanned at term-equivalent age) from the dHCP 3rd release is not understandable since preterms might have a very different development related to prematurity and to post-natal (including visual) experience. Although the authors show that the difference between the connectivity of visual and other sensory regions, and the one of visual and PFC regions, do not depend on age at birth, they do not show that each connectivity pattern is not influenced by prematurity. Simply not considering the preterm infants would have made the analysis much more robust, and the full-term group in itself is already quite large compared with the two adult groups. The current study setting and the analyses performed do not seem to be an adequate and sufficient model to ascertain that "a few weeks of vision after birth is ... insufficient to influence connectivity".

In a similar way, excluding the few infants with detected brain anomalies (radiological scores higher or equal to 4) would strengthen the group homogeneity by focusing on infants supposed to have a rather typical neurodevelopment. The authors quote all infants as "sighted" but this is not guaranteed as no follow-up is provided.

Response #2: We appreciate the reviewer’s suggestion. We re-analyzed the infant cohort after excluding all cases with radiological scores ≥4 (n =39 infants excluded). The revised analysis confirmed that the connectivity patterns reported in the main text remain statistically unchanged (see Supplementary Fig. S11). This demonstrates the robustness of our findings to potential confounding effects from potential brain anomalies. We have explicitly clarified this in the revised Methods section (page 14, line 391in the manuscript).

In our dataset, newborns (average age at scan = 2.79 weeks) have very limited and immature vision. We agree with the reviewer that long-term visual outcomes cannot be guaranteed without follow-up data. The term "sighted infants" was used operationally to distinguish this cohort from congenitally blind populations.

The post-menstrual age (PMA) at scan of the infants is also not described. The methods indicate that all were scanned at "term-equivalent age" but does this mean that there is some PMA variability between 37 and 41 weeks? Connectivity measures might be influenced by such inter-individual variability in PMA, and this could be evaluated.

The rationale for presenting results on the connectivity of secondary visual cortices before one of the primary cortices (V1) was not clear to understand. Also, it might be relevant to better justify why only the connectivity of visual regions to non-visual sensory regions (S1-M1, A1) and prefrontal cortex (PFC) was considered in the analyses, and not the ones to other brain regions.

In relation to the question explored, it might be informative to reposition the study in relation to what others have shown about the developmental chronology of structural and functional long-distance and short-distance connections during pregnancy and the first postnatal months.

The authors acknowledge the methodological difficulties in defining regions of interest (ROIs) in infants in a similar way as adults. The reliability and the comparability of the ROIs positioning in infants is definitely an issue. Given that brain development is not homogeneous and synchronous across brain regions (in particular with the frontal and parietal lobes showing delayed growth), the newborn brain is not homothetic to the adult brain, which poses major problems for registration. The functional specialization of cortical regions is incomplete at birth. This raises the question of whether the findings of this study would be stable/robust if slightly larger or displaced regions had been considered, to cover with greater certainty the same areas as those considered in adults. And have other cortical parcellation approaches been considered to assess the ROIs robustness (e.g. MCRIB-S for full-terms)?

Recommendations for the Authors:

Reviewer #1(Recommendations for the authors):

Further consideration should be given to the underlying changes in network architecture that may account for differences in functional correlations across groups. An increase (or decrease) in correlation between two regions could signify an increase (decrease) in connection or communication between those regions. Alternatively, it might reflect an increase in communication or connection with a third region, while the physical connections/interactions between the two original regions remain unchanged. These possibilities lead to distinct mechanistic interpretations. For example, there are substantial changes in connectivity during early visual (e.g. Burkhalter A. 1993, Cerebral Cortex) and visuo-motor development (e.g., Csibra et al. 2000 Neuroreport). It's not clear whether increases in communication within the visual network and improvements in visuo-motor behavior (e.g., Yizhar et al. 2023 Frontiers in Neuroscience) wouldn't produce a qualitatively similar pattern of results.

Relatedly, the within-network correlation patterns between visual ROIs and frontal ROIs appear markedly different between sighted adults and infants (Supplementary Figure S1). To what extent do the differences in long-range correlations between visual and frontal regions reflect these within-network differences in functional organization?

Response #3: The reviewer is raising some interesting questions about possible mechanisms and network changes. Resting state studies are indeed always subject to possibility that some effects are mediated by a third, unobserved region. Prior whole-cortex connectivity analyses have observed primarily changes in occipito-frontal connectivity in blindness, so there is not a clear cortical ‘third region’ candidate (Deen et al., 2015). However, some thalamic affects have also been observed and could contribute to the phenomenon (Bedny et al., 2011). Resting state changes in correlation between two areas do not imply changes in strength of long-range anatomical connectivity. Indeed, in the current case they may well reflect differential functional coupling, rather than strengthening or weakening of anatomical connections. We now discuss this in the Discussion section on page 12, line 301 as follows:

“Despite these insights, many questions remain regarding the neurobiological mechanisms underlying experience-based functional connectivity changes and their relationship to anatomical development. Long-range anatomical connections between brain regions are already present in infants—even prenatally—though they remain immature (Huang et al., 2009; Kostović et al., 2019, 2021; Takahashi et al., 2012; Vasung, 2017). Functional connectivity changes may stem from local synaptic modifications within these stable structural pathways, consistent with findings that functional connectivity can vary independently of structural connection strength (Fotiadis et al., 2024). Moreover, functional connectivity has been shown to outperform structural connectivity in predicting individual behavioral differences, suggesting that experience-based functional changes may reflect finer-scale synaptic or network-level modulations not captured by macrostructural measures (Ooi et al., 2022). Prior studies also suggest that, even in adults, coordinated sensory-motor experience can lead to enhancement of functional connectivity across sensory-motor systems, indicating that large-scale changes in functional connectivity do not necessarily require corresponding changes in anatomical connectivity (Guerra-Carrillo et al., 2014; Li et al., 2018).”

It is not clear how changes in correlation patterns among visual areas would produce the connectivity between visual areas and prefrontal areas reported in the current study. Activity in visual areas drives correlations both among visual areas and between visual and prefrontal areas and the same is true of prefrontal corticies.

The findings from this study should be more closely linked to the extensive literature surrounding the debate on whether experience plays an instructive or permissive role in visual development (e.g., Crair 1999 Current Opin Neurobiol; Sur et al. 1999 J Neurobiol; Kiorpes 2016 J Neurosci; Stellwagen & Shatz 2002 Neuron; Roy et al. 2020 Nature Communications).

Response #4: The instructive role suggests that specific experiences or patterns of neural activity directly shape and organize neural circuitry, while the permissive role indicates that such experiences or activity merely enable other factors, such as molecular signals, to influence neural circuit formation(Crair, 1999; Sur et al., 1999). To distinguish whether experience plays an instructive or permissive role, it is essential to manipulate the pattern or information content of neural activity while maintaining a constant overall activity level (Crair, 1999; Roy et al., 2020; Stellwagen & Shatz, 2002). However, both the sighted and blind adult groups have had extensive experience and neural activity in the visual cortices. For the sighted group, activity in the visual cortex is partly driven by bottom-up input from the external environment, through the retina, LGN, and ultimately to the cortex. In contrast, the blind group’s visual cortex activity is partially driven by top-down input from non-visual networks. The precise role of this activity in shaping the observed connectivity patterns remains unclear. Although our study cannot speak to this issue directly, we now link to the relevant literature on page 12,line 320 of the manuscript in the Discussion section as follows:

“The current findings reveal both effects of vision and effects of blindness on the functional connectivity patterns of the visual cortex. A further open question is whether visual experience plays an instructive or permissive role in shaping neural connectivity patterns. An instructive role suggests that specific sensory experiences or patterns of neural activity directly shape and organize neural circuitry. In contrast, a permissive role implies that sensory experience or neural activity merely facilitates the influence of other factors—such as molecular signals—on the formation and organization of neural circuits (Crair, 1999; Sur et al., 1999). Studies with animals that manipulate the pattern or informational content of neural activity while keeping overall activity levels constant could distinguish between these hypotheses (Crair, 1999; Roy et al., 2020; Stellwagen & Shatz, 2002).”

The assertion that a few weeks of vision after birth is insufficient to influence connectivity is provocative. Though supported by the study's results, it would benefit from integration with research in animal models showing considerable malleability of networks from early experience (e.g., Akerman et al. 2002 Neuron; Li et al. 2006 Nature Neuroscience; Stacy et al. 2023 J Neuroscience).

Response #5: We thank the reviewer for their suggestion. The present study found that several weeks of postnatal visual experience is insufficient to significantly alter the long-term connectivity patterns of the visual cortices. While animal studies have shown that acute visual experience, or even exposure to visual stimuli through unopened eyelids, can robustly influence visual system development(Akerman et al., 2002; Li et al., 2008; Van Hooser et al., 2012). We think this discrepancy may be attributed to the substantial differences in developmental timelines between species. The human lifespan is much longer, and so is the human critical period, making it unclear how to map duration from one species to another. We briefly touched upon the time course issue in page 11 line 289 in the Discussion section as follows:

“The present results reveal the effects of experience on development of functional connectivity between infancy and adulthood, but do not speak to the precise time course of these effects. Infants in the current sample had between 0 and 20 weeks of visual experience. Comparisons across these infants suggests that several weeks of postnatal visual experience is insufficient to produce a sighted-adult connectivity profile. The time course of development could be anywhere between a few months and years and could be tested by examining data from children of different ages.”

Substantial differences between the groups are evident in several key aspects of the study, including the number of subjects, brain sizes, imaging parameters, and data preprocessing, all of which are likely to have an impact on the overall signal quality. To clarify how these differences might have impacted correlation differences between groups, it would be essential to include information on the noise ceilings for each correlation analysis within each group.

Response #6: We thank the reviewer for their suggestion. We now report the split-half noise ceiling for adult and infant groups. For each participant, we first split the rs-fMRI time series into two halves, then calculated the ROI-wise rsFC pattern from the two splits. The split-half noise ceiling was estimated according to Lage-Castellanos et al (2019). The noise ceilings of the three groups (infants: 0.90 ± 0.056,blind adults: 0.88 ± 0.041, sighted adults: 0.90 ± 0.055) showed no significant difference (One-way ANOVA_, F(2,552) = 2.348, p = 0.097). Therefore, we believe that overall signal quality is unlikely to impact our results. We also add the relevant context in the Method section in page 16 Line 447 as follows:

“Substantial differences between the groups exist in this study, including the number of subjects, brain sizes, imaging parameters, and data preprocessing, all of which are likely to have an impact on the overall signal quality. To address this concern, we compared the split-half noise ceiling across the groups (infants, sighted adults, and blind adults). For each participant, we first split the rs-fMRI time series into two halves, then calculated the ROI-wise rsFC pattern from the two splits. The split-half noise ceiling was estimated according to Lage-Castellanos et al (Lage-Castellanos et al., 2019). The noise ceilings of the three groups (infants: 0.90 ± 0.056, blind adults: 0.88 ± 0.041, sighted adults: 0.90 ± 0.055) showed no significant difference (One-way ANOVA, F (2,552) = 2.348, p = 0.097). Therefore, overall signal quality is unlikely to impact our results.”

In general, it appears that the infant correlations are stronger compared to the other groups. While this could reflect increased coherence or lack of differentiation, it is also possible that it is simply due to the presence of a non-neuronal global signal. Such a signal has the potential to substantially limit the effective range of functional correlations and comparisons with adults. To address this, it is advisable to conduct control analyses aimed at assessing and potentially removing global signals.

Response #7: We agree with the reviewer that global signal regression (GSR) may help reduce non-neuronal artifacts, such as motion, cardiac, and respiratory signals, which are known to correlate with the global signal. However, the global signal also contains neural signals from gray matter, and removing it can introduce unwanted artifacts, especially for the current study. First, GSR can reduce the physiological accuracy of functional connectivity (FC); second, GSR may have differential effects across groups, potentially introducing additional artifacts in between-group comparisons, as noted by Murphy et al (Murphy & Fox, 2017). The CompCor method (Behzadi et al., 2007; Whitfield-Gabrieli & Nieto-Castanon, 2012) is capble to estimate the global non-neuronal artifacts like the GSR method. Meanwhile as it estimate global non-neuronal artifacts from signals within the white matter (WM) and cerebrospinal fluid (CSF) masks, but not the gray matter (GM), CompCor could introduce minimal unwanted bias to the GM signal.

Was there a difference in correlations for preterm vs term neonates? Recent research has suggested that preterm births can have an impact on functional networks, particularly in frontal cortices. e.g., Tokariev et al. 2019, Li et al. 2021 elife; Zhang et al. 2022 Fronteirs in Neuroscience.

Response #8: We have compared preterm and term neonates for all the main results, including the connectivity from the secondary visual cortex/V1 to non-visual sensory cortices versus prefrontal cortices, the laterality of occipito-frontal connectivity, and the specialization across different fronto-occipital networks. This information is reported in Page 6 line 169 and Supplementary Figure S7. The connectivities of full-term infants are generally higher than those of preterm infants. However, the connectivity patterns of term and preterm infants are very similar.

The consistency between the current results and prior work (e.g., Burton et al. 2014) is notable, particularly in the observed greater correlations in prefrontal regions and weaker correlations in somato-motor regions for early blind individuals compared to sighted. However, almost all visual-frontal correlations in both groups were negative in that prior study. Some discussion on why positive correlations were found in the current study could help to clarify.

Response #9: Many other papers have reported positive correlations similar to those found in our study (e.g., Deen et al., 2015; Kanjlia et al., 2021). In contrast, Burton's study identified predominantly negative visual-frontal correlations, we think this is likely because the global signal was regressed out during preprocessing. This methodological choice can lead to an increase in negative connections (Murphy & Fox, 2017).

The term "secondary visual areas" used throughout the paper lacks specificity, and its usage in terms of underlying anatomical and functional areas has been inconsistent in the literature. It would be advisable to adopt a more precise characterization based on functional and/or anatomical criteria.

Response #10: We specified in the article that Tthe occipital ROIs were defined in the current study are functional areas in people born blind identified in prior studies as regions that respond to three non-visual tasks such as language, math, or executive function, and show functional connectivity changes in blind adults in previous studies (Kanjlia et al., 2016, 2021; Lane et al., 2015). These regions respond to language, math and executivie function in the congenitally blind population (see Figure 1.) The are refered collectively as ‘secondary visual areas’ to destinguish them from V1. Anatomically, these three regions cover the majority of the lateral occipital cortex and part of the ventral occipital cortex, providing a good sample of the connectivity profile of higher-order visual areas. Thus, we are using the term "secondary visual areas" to refer to these regions. In blind individuals, although these regions respond to non-visual tasks, their exact functions are unknown.

The inclusion of the ventral temporal cortex in the visual ROIs is currently only depicted in Supplementary Figure S7. To enhance the clarity of the areas of interest analyzed, it would be advisable to illustrate the ventral temporal areas in the main text. Were there notable differences in the frontal correlations between the lateral occipital visual areas and ventral temporal areas?

Response #11: We thank the reviewer for pointing out this issue. We added a statement about the ventral visual cortex in describing the location of the ROI and added the ventral view of ROIs in the Figure 1. The language-responsive and math -responsive ROIs covers both the lateral and ventral visual cortex, whereas executive function (response-conflict) regions cover only the lateral visual cortex. We compared the connectivity patterns of these three regions and found no differences (see supplementary Fig S2).

The blind group results are characterized as reflecting a reorganization in comparison to sighted adults while the results for sighted adults compared to infants are discussed more as a maturation ("adult pattern isn't default but requires experience to establish"). Both the sighted and blind adult groups showed differences from the infant group, and these differences are attributed to the role of experience. Why use "reorganization" for one result and maturation for another?

Response #12: We agree with the reviewer that both of the adult groups should be thought of as equal in relation to the infants. In other words, the brain develops under one set of experiential conditions or another. We do not think that the adult sighted pattern reflects maturation. Rather, the sighted adult pattern reflects the combined influence of maturation and visual experience. The adult blind pattern reflects the combined influence of maturation and blindness. We use the term ‘reorganization’ to label differences in the blind adults relative to sighted infants. We do so for the purpose of clarity and to remain consistent with terminology in prior liaterature. However, we agree with the reviewer that the blind group does not reflect ‘reorganization’ intrinsically any more than the sighted adult group.

The statement that "visual experience is required to set up long-range functional connectivity" is unclear, especially since the infant and blind groups showed stronger long-range functional correlations with PFC.

Response #13: We revised this sentence to specifically as “visual experience establishes elements of the sighted-adult long-range connectivity” in tha Abstract line 17.

The statement that the visual ROIS roughly correspond to "the anatomical location of areas such as V5/MT+, LO, V3a, and V4v" appears imprecise. From Supplementary Figure S7, these areas cover anterior portions of ventral temporal cortex (do these span the anatomical location of putative category-selective areas?) and into the intraparietal sulcus.

Response #14: Thanks to the reviewer for the clarification. The ventral ROIs cover the middle and part of the anterior portion of the ventral temporal lobe, including the putative category-selective areas. Additionally, the dorsal ROIs extend beyond the occipital lobe to the intraparietal sulcus and superior parietal lobule. We have added a more detailed description of the anatomical location of the ROI in the Methods section Page 17 line 489 as follows:

“Each functional ROI spans multiple anatomical regions and together the secondary visual ROIs tile large portions of lateral occipital, occipito-temporal, dorsal occipital and occipito-parietal cortices. In sighted people, the secondary visual occipital ROIs include the anatomical locations of functional regions such as motion area V5/MT+, the lateral occipital complex (LO), category specific ventral occipitotemporal cortices and dorsally, V3a and V4v.  The occipital ROI also covers the middle of the ventral temporal lobe. Dorsally, it extended to the intraparietal sulcus and superior parietal lobule.”

The motivation for assessing correlations with motor and frontal regions was briefly discussed in the introduction. It would be helpful to reiterate this motivation when first introducing the analyses in the results.

Response #15: Thank you for the thoughtful suggestion. Upon reflection, we chose to substantially revise the Introduction to more clearly and comprehensively explain the rationale for examining the couplings with motor and frontal regions, rather than reiterating it in the Results section. We believe this revised framing provides a stronger foundation for the analyses that follow, while avoiding redundancy across sections. We hope this addresses the reviewer’s concern.

Reviewer #2 (Recommendations for the authors):

Congratulations on a well-written paper and an interesting set of results.

Reviewer #3 (Recommendations for the authors):

Abstract:

Mentioning "sighted infants" does not seem adequate.

Response #16: In our dataset, newborns (average age at scan = 2.79 weeks) have very limited and immature vision. We agree with the reviewer that long-term visual outcomes cannot be guaranteed without follow-up data. The term "sighted infants" was used operationally to distinguish this cohort from congenitally blind populations.

In sentences after "Specifically...", it was not clear whether the authors referred to V1 connectivity.

Response #17: We thank the reviewer for this comment. In the revised abstract, we have removed the original "Specifically..." phrasing and clarified the results.

Introduction

Talking about the "instructive effects" of vision might be confusing or misleading. Visual experiences like exposure to oral language are part of the normal/spontaneous environment that allows the infant behavioral acquisitions (contrarily with learnings that occur later during development with instruction like for reading).

Response #18: We appreciate the reviewer’s concern and would like to clarify that the term “instructive effect” is used here derived from neurodevelopmental studies (Crair, 1999; Sur et al., 1999). In this context, “instructive” refers to activity-dependent mechanisms where patterns of neural activity actively guide the organization of synaptic connectivity, emphasizing that spontaneous or sensory-driven activity (e.g., retinal waves, visual experience) can directly shape circuit refinement, as seen in ocular dominance column formation. In the context of our study, we emphasize that vision plays an instructive role in setting up the balance of connectivity between occipital cortex and non-visual networks.

For references on the development of connectivity, I would advise citing MRI studies but also studies based on histological approaches (see for example the detailed review by Kostovic et al, NeuroImage 2019).

Response #19: We thank the reviewer for this suggestion. We have incorporated a discussion on the long-range anatomical connections that emerge as early as infancy, referencing studies that employed diffusion MR imaging and histological methods, as detailed below.

“Many long-range anatomical connections between brain regions are already established in infants, even before birth, although they are not yet mature (Huang et al., 2009; Kostović et al., 2019, 2021; Takahashi et al., 2012; Vasung, 2017).” (Page 12, line 303 in the manuscript)

Results

P7 l170: It might be helpful to be precise that this is "compared with inter-hemispheric connectivity".

Response #20: We thank the reviewer for this suggestion. To align with our established terminology, we have revised the statement to explicitly contrast within-hemisphere connectivity with between-hemisphere connectivity. The modified text now reads (page 7, line 183 in the manuscript):

“Compared to sighted adults, blind adults exhibited a stronger dominance of within-hemisphere connectivity over between-hemisphere connectivity. That is, in people born blind, left visual networks are more strongly connected to left PFC, whereas right visual networks are more strongly connected to right PFC.

L176-181: It was not clear to me what was the difference between "across" and "between hemisphere connectivity". Would it be informative to test the difference between blind and sighted adults?

Response #21: We clarify that there is no distinction between the terms “across” and “between hemisphere connectivity”—they refer to the same concept. To ensure consistency, we have revised the text to exclusively use “between hemisphere connectivity” throughout the manuscript. Regarding the comparison between blind and sighted adults, we conducted statistical comparisons between these groups in our analysis, and the results have been incorporated into the revised version (Page 7, line 187 in the manuscript).

Adding statistics on Figure 3, but also on Figures 1 and 2 might help the reading.

Response #22: We have added the statistics in Figure 1-4.

Adding the third comparison in Figure 4 would be possible in my view.

Response #23: We explored integrating the response-conflict region into Figure 4, but this would require a 3x3 bar chart with pairwise statistical significance markers, which introduced excessive visual complexity that hindered readers’ ability to grasp our intended message. To ensure clarity, we retained the original Figure 4 while providing the complete three-region analysis (including all statistical comparisons) in Supplementary Figure S8 to ensure completeness.

Methods

The authors might have to specify ages at birth, and ages at scan (median + range?).

Response #24: We have added that information in the Methods section as follows:

“The average age from birth at scan = 2.79 weeks (SD = 3.77, median = 1.57, range = 0 – 19.71); average gestational age at scan = 41.23 weeks (SD = 1.77, median = 41.29, range = 37 – 45.14); average gestational age at birth = 38.43 weeks (SD = 3.73, median = 39.71, range = 23 – 42.71).” (Page 14, line 379 in the manuscript)

It might be relevant to comment on the range of available fMRI volumes, and the fact that connectivity measures might then be less robust in infants.

Response #25: We report the range of fMRI volumes in the Methods section (Page 16, Line 449). Adult participants (blind and sighted) underwent 1–4 scanning sessions, each containing 240 volumes (mean scan duration: 710.4 seconds per participant). For infants, all subjects had 2300 fMRI volumes, and we retained a subset of 1600 continuous volumes per subject with the minimum number of motion outliers. While infant connectivity measures may inherently exhibit lower robustness due to developmental and motion-related factors, our infant cohort’s large sample size (n=475) and stringent motion censoring criteria enhance the reliability of group-level inferences. We have integrated this clarification into the Methods section (Page 16, Line 444) as follows:

"While infant connectivity estimates may be less robust at the individual level compared to adults due to shorter scan durations and higher motion, our cohort’s large sample size (n=475) and rigorous motion censoring mitigate these limitations for group-level analyses. "

The mention of dHCP 2nd release should be removed from the paragraph on data availability.

Response #26: We have removed it.

Reviewer #3 (Public review):

A bias in how people infer the amount of control they have over their environment is widely believed to be a key component of several mental illnesses including depression, anxiety, and addiction. Accordingly, this bias has been a major focus in computational models of those disorders. However, all of these models treat control as a unidimensional property, roughly, how strongly outcomes depend on action. This paper proposes---correctly, I think---that the intuitive notion of "control" captures multiple dimensions in the relationship between action and outcome. In particular, the authors identify one key dimension: the degree to which outcome depends on how much *effort* we exert, calling this dimension the "elasticity of control". They additionally argue that this dimension (rather than the more holistic notion of controllability) may be specifically impaired in certain types of psychopathology. This idea has the potential to change how we think about several major mental disorders in a substantial way, and can additionally help us better understand how healthy people navigate challenging decision-making problems. More concisely, it is a *very good idea*.

The more concrete contributions, however, are not as strong. In particular, evidence for the paper's most striking claims is weak. Quoting the abstract, these claims are (1) "the elasticity of control [is] a distinct cognitive construct guiding adaptive behavior" and (2) "overestimation of elasticity is associated with elevated psychopathology involving an impaired sense of control."

Main issues

I'll highlight the key points.

- The task cannot distinguish elasticity inference from general learning processes

- Participants were explicitly instructed about elasticity, with labeled examples

- The psychopathology claims rely on an invalid interpretation of CCA, and are contradicted by simple correlations (elasticity bias and the sense of agency scale is r=0.03)

Distinct construct

Starting with claim 1, there are three subclaims here. (1A) People's behavior is sensitive to differences in elasticity; (1B) there are mental processes specific to elasticity inference, i.e., not falling out of general learning mechanisms; and, implicitly, (1C) people infer elasticity naturally as they go about their daily lives. The results clearly support 1A. However, 1B and 1C are not well supported.

(1B) The data cannot support the "distinct cognitive construct" claim because the task is too simple to dissociate elasticity inference from more general learning processes (also raised by Reviewer 1). The key behavioral signature for elasticity inference (vs. generic controllability inference) is the transfer across ticket numbers, illustrated in Fig 4. However, this pattern is also predicted by a standard Bayesian learner equipped with an intuitive causal model of the task. Each ticket gives you another chance to board and the agent infers the probability that each attempt succeeds. Crucially, this logic is not at all specific to elasticity or even control. An identical model could be applied to inferring the bias of a coin from observations of whether any of N tosses were heads-a task that is formally identical to this one (at least, the intuitive model of the task; see first minor comment).

Importantly, this point cannot be addressed by showing that the author's model fits data better than this or any other specific Bayesian model. It is not a question of whether one particular updating rule explains data better than another. Rather, it is a question of whether the task can distinguish between biases in *elasticity* inference versus biases in probabilistic inference more generally. The present task cannot make this distinction because it does not make separate measurements of the two types of inference. To provide compelling evidence that elasticity inference is a "distinct cognitive construct", one would need to show that there are reliable individual differences in elasticity inference that generalize across contexts but do not generalize to computationally similar types of probabilistic inference (e.g. the coin flipping example).

(1C) The implicit claim that people infer elasticity outside of the experimental task is undermined by the experimental design. The authors explicitly tell people about the two notions of control as part of the training phase: "To reinforce participants' understanding of how elasticity and controllability were manifested in each planet, [participants] were informed of the planet type they had visited after every 15 trips."

In the revisions, the authors seem to go back and forth on whether they are claiming that people infer elasticity without instruction (I won't quote it here). I'll just note that the examples they provide in the most recent rebuttal are all cases in which one never receives explicit labels about elasticity. If people only infer elasticity when it is explicitly labeled, I struggle to see its relevance for understanding human cognition and behavior.

Psychopathology

Finally, I turn to claim 2, that "overestimation of elasticity is associated with elevated psychopathology involving an impaired sense of control." The CCA analysis is in principle unable to support this claim. As the authors correctly note in their latest rebuttal, the CCA does show that "there is a relationship between psychopathology traits and task parameters". The lesion analysis further shows that "elasticity bias specifically contributes to this relationship" (and similarly for the Sense of Agency scale). Crucially, however, this does *not* imply that there is a relationship between those two variables. The most direct test of that relationship is the simple correlation, which the authors report only in a supplemental figure: there is no relationship (r=0.03). Although it is of course possible that there is a relationship that is obscured by confounding variables, the paper provides no evidence-statistical or otherwise-that such a relationship exists.

Minor comments

The statistical structure of the task is inconsistent with the framing. In the framing, participants can make either one or two second boarding attempts (jumps) by purchasing extra tickets. The additional attempt(s) will thus succeed with probability p for one ticket and 2p - p^2 for two tickets; the p^2 captures the fact that you only take the second attempt if you fail on the first. A consequence of this is buying more tickets has diminishing returns. In contrast, in the task, participants always jumped twice after purchasing two tickets, and the probability of success with two tickets was exactly double that with one ticket. Thus, if participants are applying an intuitive causal model to the task, the researcher could infer "biases" in elasticity inference that are probably better characterized as effective use of prior information (encoded in the causal model).

The model is heuristically defined and does not reflect Bayesian updating. For example, it over-estimates maximum control by not using losses with less than 3 tickets (intuitively, the inference here depends on what your beliefs about elasticity). Including forced three-ticket trials at the beginning of each round makes this less of an issue; but if you want to remove those trials, you might need to adjust the model. The need to introduce the modified model with kappa is likely another symptom of the heuristic nature of the model updating equations.

Author response:

The following is the authors’ response to the previous reviews

Reviewer #1 (Public review):

This research takes a novel theoretical and methodological approach to understanding how people estimate the level of control they have over their environment and how they adjust their actions accordingly. The task is innovative and both it and the findings are well-described (with excellent visuals). They also offer thorough validation for the particular model they develop. The research has the potential to theoretically inform understanding of control across domains, which is a topic of great importance.

We thank the Reviewer for their favorable appraisal and valuable suggestions, which have helped clarify and strengthen the study’s conclusion. 

In its revised form, the manuscript addresses most of my previous concerns. The main remaining weakness pertains to the analyses aimed at addressing my suggesting of Bayesian updating as an alternative to the model proposed by the authors. My suggestion was to assume that people perform a form of function approximation to relate resource expenditure to success probability. The authors performed a version of this where people were weighing evidence for a few canonical functions (flat, step, linear), and found that this model underperformed theirs. However, this Bayesian model is quite constrained in its ability to estimate the function relating resources. A more robust test would be to assume a more flexible form of updating that is able to capture a wide range of distributions (e.g., using basis functions, gaussian processes, or nonparametric estimators); see, e.g., work by Griffiths on human function learning). The benefit of testing this type of model is that it would make contact with a known form of inference that individuals engage in across various settings and therefore could offer a more parsimonious and generalizable account of function learning, whereby learning of resource elasticity is a special case. I defer to the authors as to whether they'd like to pursue this direction, but if not I think it's still important that they acknowledge that they are unable to rule out a more general process like this as an alternative to their model. This pertains also to inferences about individual differences, which currently hinge on their preferred model being the most parsimonious.

We thank the Reviewer for this thoughtful suggestion. We acknowledge that more flexible function learning approaches could provide a stronger test in favor of a more general account. Our Bayesian model implemented a basis function approach where the weights of three archetypal functions (flat, step, linear) are learned from experience Testing models with more flexible basis functions would likely require a task with more than three levels of resource investment (1, 2, or 3 tickets). This would make an interesting direction for future work expanding on our current findings. We now incorporate this suggestion in more detail in our updated manuscript (335-341):

“Second, future models could enable generalization to levels of resource investment not previously experienced. For example, controllability and its elasticity could be jointly estimated via function approximation that considers control as a function of invested resources. Although our implementation of this model did not fit participants’ choices well (see Methods), other modeling assumptions drawn from human function learning [30] or experimental designs with continuous action spaces may offer a better test of this idea.”

Reviewer #2 (Public review):

This research investigates how people might value different factors that contribute to controllability in a creative and thorough way. The authors use computational modeling to try to dissociate "elasticity" from "overall controllability," and find some differential associations with psychopathology. This was a convincing justification for using modeling above and beyond behavioral output and yielded interesting results. Notably, the authors conclude that these findings suggest that biased elasticity could distort agency beliefs via maladaptive resource allocation. Overall, this paper reveals important findings about how people consider components of controllability. The authors have gone to great lengths to revise the manuscript to clarify their definitions of "elastic" and "inelastic" and bolster evidence for their computational model, resulting in an overall strong manuscript that is valuable for elucidating controllability dynamics and preferences. 

We thank the Reviewer for their constructive feedback throughout the review process, which has substantially strengthened our manuscript and clarified our theoretical framework.

One minor weakness is that the justification for the analysis technique for the relationships between the model parameters and the psychopathology measures remains lacking given the fact that simple correlational analyses did not reveal any significant associations.

We note that the existence of bivariate relationships is not a prerequisite for the existence of multivariate relationships. Conditioning the latter on the former, therefore, would risk missing out on important relationships existing in the data. Ultimately, correlations between pairs of variables do not offer a sensitive test for the general hypothesis that there is a relationship between two sets of variables. As an illustration, consider that elasticity bias correlated in our data (r = .17, p<.001) with the difference between SOA (sense of agency) and SDS (self-rating depression). Notably, SOA and SDS were positively correlated (r = .47, p<.001), and neither of them was correlated with elasticity bias (SOA: r=.04 p=.43, SDS: r=-.06, p=.16). It was a dimension that ran between them that mapped onto elasticity bias. This specific finding is incidental and uncorrected for multiple comparisons, hence we do not report it in the manuscript, but it illustrates the kinds of relationships that cannot be accounted for by looking at bivariate relationships alone.  

Reviewer #3 (Public review):

A bias in how people infer the amount of control they have over their environment is widely believed to be a key component of several mental illnesses including depression, anxiety, and addiction. Accordingly, this bias has been a major focus in computational models of those disorders. However, all of these models treat control as a unidimensional property, roughly, how strongly outcomes depend on action. This paper proposes---correctly, I think---that the intuitive notion of "control" captures multiple dimensions in the relationship between action and outcome.

In particular, the authors identify one key dimension: the degree to which outcome depends on how much *effort* we exert, calling this dimension the "elasticity of control". They additionally argue that this dimension (rather than the more holistic notion of controllability) may be specifically impaired in certain types of psychopathology. This idea has the potential to change how we think about several major mental disorders in a substantial way and can additionally help us better understand how healthy people navigate challenging decision-making problems. More concisely, it is a very good idea.

We thank the Reviewer for their thoughtful engagement with our manuscript. We appreciate their recognition of elasticity as a key dimension of control that has the potential to advance our understanding of psychopathology and healthy decision-making.

Starting with theory, the authors do not provide a strong formal characterization of the proposed notion of elasticity. There are existing, highly general models of controllability (e.g., Huys & Dayan, 2009; Ligneul, 2021) and the elasticity idea could naturally be embedded within one of these frameworks. The authors gesture at this in the introduction; however, this formalization is not reflected in the implemented model, which is highly task-specific.

Our formal definition of elasticity, detailed in Supplementary Note 1, naturally extends the reward-based and information-theoretic definitions of controllability by Huys & Dayan (2009) and Ligneul (2021). We now further clarify how the model implements this formalized definition (lines 156-159).

“Conversely, in the ‘elastic controllability model’, the beta distributions represent a belief about the maximum achievable level of control (𝑎_Control, 𝑏_Control) coupled with two elasticity estimates that specify the degree to which successful boarding requires purchasing at least one (𝑎_elastic≥1, 𝑏_elastic≥1) or specifically two (𝑎_elastic2, 𝑏_elastic2) extra tickets. As such, these elasticity estimates quantify how resource investment affects control. The higher they are, the more controllability estimates can be made more precise by knowing how much resources the agent is willing and able to invest (Supplementary Note 1).”

Moreover, the authors present elasticity as if it is somehow "outside of" the more general notion of controllability. However, effort and investment are just specific dimensions of action; and resources like money, strength, and skill (the "highly trained birke") are just specific dimensions of state. Accordingly, the notion of elasticity is necessarily implicitly captured by the standard model. Personally, I am compelled by the idea that effort and resource (and therefore elasticity) are particularly important dimensions, ones that people are uniquely tuned to. However, by framing elasticity as a property that is different in kind from controllability (rather than just a dimension of controllability), the authors only make it more difficult to integrate this exciting idea into generalizable models.

We respectfully disagree that we present elasticity as outside of, or different in kind from, controllability. Throughout the manuscript, we explicitly describe elasticity as a dimension of controllability (e.g., lines 70-72, along many other examples). This is also expressed in our formal definition of elasticity (Supplementary Note 1). 

The argument that vehicle/destination choice is not trivial because people occasionally didn't choose the instructed location is not compelling to me-if anything, the exclusion rate is unusually low for online studies. The finding that people learn more from non-random outcomes is helpful, but this could easily be cast as standard model-based learning very much like what one measures with the Daw two-step task (nothing specific to control here). Their final argument is the strongest, that to explain behavior the model must assume "a priori that increased effort could enhance control." However, more literally, the necessary assumption is that each attempt increases the probability of success-e.g. you're more likely to get a heads in two flips than one. I suppose you can call that "elasticity inference", but I would call it basic probabilistic reasoning.

We appreciate the Reviewer’s concerns but feel that some of the more subjective comments might not benefit from further discussion. We only note that controllability and its elasticity are features of environmental structure, so in principle any controllability-related inference is a form of model-based learning. The interesting question is whether people account in their world model for that particular feature of the environment.   

The authors try to retreat, saying "our research question was whether people can distinguish between elastic and inelastic controllability." I struggle to reconcile this with the claim in the abstract "These findings establish the elasticity of control as a distinct cognitive construct guiding adaptive behavior". That claim is the interesting one, and the one I am evaluating the evidence in light of.

In real-world contexts, it is often trivial that sometimes further investment enhances control and sometimes it does not. For example, students know that if they prepare more extensively for their exams they will likely be able to achieve better grades, but they also know that there is uncertainty in this regard – their grades could improve significantly, modestly, or in some cases, they might not improve at all, depending on the type of exams their study program administers and the knowledge or skills being tested. Our research question was whether in such contexts people learn from experience the degree to which controllability is elastic to invested resources and adapt their resource investment accordingly. Our findings show that they do. 

The authors argue for CCA by appeal to the need to "account for the substantial variance that is typically shared among different forms of psychopathology". I agree. A simple correlation would indeed be fairly weak evidence. Strong evidence would show a significant correlation after *controlling for* other factors (e.g. a regression predicting elasticity bias from all subscales simultaneously). CCA effectively does the opposite, asking whether-with the help of all the parameters and all the surveys-one can find any correlation between the two sets of variables. The results are certainly suggestive, but they provide very little statistical evidence that the elasticity parameter is meaningfully related to any particular dimension of psychopathology.

We agree with the Reviewer on the relationship between elasticity and any particular dimension of psychopathology. The CCA asks a different question, namely, whether there is a relationship between psychopathology traits and task parameters, and whether elasticity bias specifically contributes to this relationship. 

I am very concerned to see that the authors removed the discussion of this limitation in response to my first review. I quote the original explanation here:

- In interpreting the present findings, it needs to be noted that we designed our task to be especially sensitive to overestimation of elasticity. We did so by giving participants free 3 tickets at their initial visits to each planet, which meant that upon success with 3 tickets, people who overestimate elasticity were more likely to continue purchasing extra tickets unnecessarily. Following the same logic, had we first had participants experience 1 ticket trips, this could have increased the sensitivity of our task to underestimation of elasticity in elastic environments. Such underestimation could potentially relate to a distinct psychopathological profile that more heavily loads on depressive symptoms. Thus, by altering the initial exposure, future studies could disambiguate the dissociable contributions of overestimating versus underestimating elasticity to different forms of psychopathology.

The logic of this paragraph makes perfect sense to me. If you assume low elasticity, you will infer that you could catch the train with just one ticket. However, when elasticity is in fact high, you would find that you don't catch the train, leading you to quickly infer high elasticity eliminating the bias. In contrast, if you assume high elasticity, you will continue purchasing three tickets and will never have the opportunity to learn that you could be purchasing only one-the bias remains.

The authors attempt to argue that this isn't happening using parameter recovery. However, they only report the *correlation* in the parameter, whereas the critical measure is the *bias*. Furthermore, in parameter recovery, the data-generating and data-fitting models are identical-this will yield the best possible recovery results. Although finding no bias in this setting would support the claims, it cannot outweigh the logical argument for the bias that they originally laid out. Finally, parameter recovery should be performed across the full range of plausible parameter values; using fitted parameters (a detail I could only determine by reading the code) yields biased results because the fitted parameters are themselves subject to the bias (if present). That is, if true low elasticity is inferred as high elasticity, then you will not have any examples of low elasticity in the fitted parameters and will not detect the inability to recover them.

The logic the Reviewer describes breaks down when one considers the dynamics of participants’ resource investment choices. A low elasticity bias in a participant’s prior belief would make them persist for longer in purchasing a single ticket despite failure, as compared to a person without such a bias. Indeed, the ability of the experimental design to demonstrate low elasticity biases is evidenced by the fact that the majority of participants were fitted with a low elasticity bias (μ = .16 ± .14, where .5 is unbiased). 

Originally, the Reviewer was concerned that elasticity bias was being confounded with a general deficit in learning. The weak inter-parameter correlations in the parameter recovery test resolved this concern, especially given that, as we now noted, the simulated parameter space encompassed both low and high elasticity biases (range=[.02,.76]). Furthermore, regarding the Reviewer's concern about bias in the parameter recovery, we found no such significant bias with respect to the elasticity bias parameter (Δ(Simulated, Recovered)= -.03, p=.25), showing that our experiment could accurately identify low and high elasticity biases.

The statistical structure of the task is inconsistent with the framing. In the framing, participants can make either one or two second boarding attempts (jumps) by purchasing extra tickets. The additional attempt(s) will thus succeed with probability p for one ticket and 2p – p^{^}2 for two tickets; the p^{^}2 captures the fact that you only take the second attempt if you fail on the first. A consequence of this is buying more tickets has diminishing returns. In contrast, in the task, participants always jumped twice after purchasing two tickets, and the probability of success with two tickets was exactly double that with one ticket. Thus, if participants are applying an intuitive causal model to the task, they will appear to "underestimate" the elasticity of control. I don't think this seriously jeopardizes the key results, but any follow-up work should ensure that the task's structure is consistent with the intuitive causal model.

We thank the Reviewer for this comment, and agree the participants may have employed the intuitive understanding the Reviewer describes. This is consistent with our model comparison results, which showed that participants did not assume that control increases linearly with resource investment (lines 677-692). Consequently, this is also not assumed by our model, except perhaps by how the prior is implemented (a property that was supported by model comparison). In the text, we acknowledge that this aspect of the model and participants’ behavior deviates from the true task's structure, and it would be worthwhile to address this deviation in future studies. 

That said, there is no reason that this will make participants appear to be generally underestimating elasticity. Following exposure to outcomes for one and three tickets, any nonlinear understanding of probabilities would only affect the controllability estimate for two tickets. This would have contrasting effects on the elasticity estimated to the second and third tickets, but on average, it would not change the overall elasticity estimated. On the other hand, such a participant is only exposed to outcomes for two and three tickets, they would come to judge the difference between the first and second tickets too highly, thereby overestimating elasticity.  

The model is heuristically defined and does not reflect Bayesian updating. For example, it overestimates maximum control by not using losses with less than 3 tickets (intuitively, the inference here depends on what your beliefs about elasticity). Including forced three-ticket trials at the beginning of each round makes this less of an issue; but if you want to remove those trials, you might need to adjust the model. The need to introduce the modified model with kappa is likely another symptom of the heuristic nature of the model updating equations.

Note that we have tested a fully Bayesian model (lines 676-691), but found that this model fitted participants’ choices worse. 

You're right; saying these analyses provides "no information" was unfair. I agree that this is a useful way to link model parameters with behavior, and they should remain in the paper. However, my key objection still holds: these analyses do not tell us anything about how *people's* prior assumptions influence behavior. Instead, they tell us about how *fitted model parameters* depend on observed behavior. You can easily avoid this misreading by adding a small parenthetical, e.g.

Thus, a prior assumption that control is likely available **(operationalized by \gamma_controllability)** was reflected in a futile investment of resources in uncontrollable environments.

We thank the Reviewer for the suggestion and have added this parenthetical (lines 219, 225).

Reviewer #2 (Public review):

Summary:

This paper considers the effects of cognitive load (using an n-back task related to font color), predictability, and age on reading times in two experiments. There were main effects of all predictors, but more interesting effects of load and age on predictability. The effect of load is very interesting, but the manipulation of age is problematic, because we don't know what is predictable for different participants (in relation to their age). There are some theoretical concerns about prediction and predictability, and a need to address literature (reading time, visual world, ERP studies).

Strengths/weaknesses

It is important to be clear that predictability is not the same as prediction. A predictable word is processed faster than an unpredictable word (something that has been known since the 1970/80s), e.g., Rayner, Schwanenfluegel, etc. But this could be due to ease of integration. I think this issue can probably be dealt with by careful writing (see point on line 18 below). To be clear, I do not believe that the effects reported here are due to integration alone (i.e., that nothing happens before the target word), but the evidence for this claim must come from actual demonstrations of prediction.

The effect of load on the effects of predictability is very interesting (and also, I note that the fairly novel way of assessing load is itself valuable). Assuming that the experiments do measure prediction, it suggests that they are not cost-free, as is sometimes assumed. I think the researchers need to look closely at the visual world literature, most particularly the work of Huettig. (There is an isolated reference to Ito et al., but this is one of a large and highly relevant set of papers.)

There is a major concern about the effects of age. See the Results (161-5): this depends on what is meant by word predictability. It's correct if it means the predictability in the corpus. But it may or may not be correct if it refers to how predictable a word is to an individual participant. The texts are unlikely to be equally predictable to different participants, and in particular to younger vs. older participants, because of their different experiences. To put it informally, the newspaper articles may be more geared to the expectations of younger people. But there is also another problem: the LLM may have learned on the basis of language that has largely been produced by young people, and so its predictions are based on what young people are likely to say. Both of these possibilities strike me as extremely likely. So it may be that older adults are affected more by words that they find surprising, but it is also possible that the texts are not what they expect, or the LLM predictions from the text are not the ones that they would make. In sum, I am not convinced that the authors can say anything about the effects of age unless they can determine what is predictable for different ages of participants. I suspect that this failure to control is an endemic problem in the literature on aging and language processing and needs to be systematically addressed.

Overall, I think the paper makes enough of a contribution with respect to load to be useful to the literature. But for discussion of age, we would need something like evidence of how younger and older adults would complete these texts (on a word-by-word basis) and that they were equally predictable for different ages. I assume there are ways to get LLMs to emulate different participant groups, but I doubt that we could be confident about their accuracy without a lot of testing. But without something like this, I think making claims about age would be quite misleading.

Reviewer #2 (Public review):

Summary:

This study investigates the influence of prior stimuli over multiple time scales in a position discrimination task, using pupillometry data and a reanalysis of EEG data from an existing dataset. The authors report consistent history-dependent effects across task-related, task-unrelated, and stimulus-related dimensions, observed across different time scales. These effects are interpreted as reflecting a unified mechanism operating at multiple temporal levels, framed within predictive coding theory.

Strengths:

The authors have done a good job in their revision, clarifying important points and stating the limitations of the study clearly.

I also think they made a valid effort to address and correct issues arising from the temporal dependency confound, although I still wonder whether the best approach would have been to design an experiment in a way that avoided this confound in the first place.<br /> Overall, this is a substantially improved version, and I particularly appreciate the clarification and correction regarding the direction of the bias in the EEG data (repulsive rather than attractive).

Weaknesses:

These are now relatively minor points.

I believe this latter aspect, the repulsive bias, may deserve further discussion, especially in relation to their behavioral findings and, in particular, to earlier work proposing multi-stage frameworks of serial dependence, where low-level repulsion interacts with attractive biases at higher-level stages (Fritsche et al., 2020; Pascucci et al., 2019; Sheehan & Serences, 2022). The authors may also consider to cite some key reviews on serial dependence that discuss both repulsion and attraction in forced-choice and reproduction tasks (Manassi et al., 2023; Pascucci et al., 2023).

Related to this, after finding the opposite pattern, is the sentence in line 472-473 ("Further, we found an attractive...") and the related argument still valid?

Regarding my earlier point about former line 197 and Figure 3b,c: what I noticed-similar to the patterns reported in the studies I referenced-is that the data cannot be simply described as showing faster and more accurate responses for small deltas. Responses also appear faster and more accurate for very large deltas, with performance being worse in between. Indeed, as the authors state: "The peak in precision for large Deltas locations is consistent with alternate events being encoded more precisely, while the peak for small offsets may be explained by the attractive bias towards the previous target." I wonder whether it is necessary, or unequivocally supported by the data, to hypothesize two separate mechanisms here. An alternative could be interference effects between consecutive stimuli that are neither identical nor completely different-making the previous one more likely to interfere with the current stimulus representation.

Finally, this is definitely a minor point, but I still find the reply to my comment about the prediction of stable retinal input rather speculative. Such a prediction would seem more plausible in world-centered coordinates.

Author response:

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

Reviewer #1 (Public review):

(1) The manuscript is quite dense, with some concepts that may prove difficult for the non-specialist. I recommend spending a few more words (and maybe some pictures) describing the difference between task-relevant and task-irrelevant planes. Nice technique, but not instantly obvious. Then we are hit with "stimulus-related", which definitely needs some words (also because it is orthogonal to neither of the above). 

We agree that the original description of the planes was too terse and have expanded on this in the revised manuscript.

Line 85 - To test the influence of attention, trials were sorted according to two spatial reference planes, based on the location of the stimulus: task-related and task-unrelated (Fig. 1b). The task-related plane corresponded to participants’ binary judgement (Fig 1b, light cyan vertical dashed line) and the task-unrelated plane was orthogonal to this (Fig 1b, dark cyan horizontal dashed line). For example, if a participant was tasked with performing a left-or-right of fixation judgement, then their task-related plane was the vertical boundary between the left and right side of fixation, while their task-unrelated plane was the horizontal boundary. The former (left-right) axis is relevant to their task while the latter (top-bottom) axis is orthogonal and task irrelevant. This orthogonality can be leveraged to analyze the same data twice (once according to the task-related plane and again according to the taskunrelated plane) in order to compare performance when the relative location of an event is either task relevant or irrelevant.

Line 183 - whereas task planes were constant, the stimulus-related plane was defined by the location of the stimulus on the previous trial, and thus varied from trial to trial. That is, on each trial, the target is considered a repeat if it changes location by <|90°| relative to its location on the previous trial, and an alternate if it moves by >|90°|.

(2) While I understand that the authors want the three classical separations, I actually found it misleading. Firstly, for a perceptual scientist to call intervals in the order of seconds (rather than milliseconds), "micro" is technically coming from the raw prawn. Secondly, the divisions are not actually time, but events: micro means one-back paradigm, one event previously, rather than defined by duration. Thirdly, meso isn't really a category, just a few micros stacked up (and there's not much data on this). And macro is basically patterns, or statistical regularities, rather than being a fixed time. I think it would be better either to talk about short-term and long-term, which do not have the connotations I mentioned. Or simply talk about "serial dependence" and "statistical regularities". Or both. 

We agree that the temporal scales defined in the current study are not the only way one could categorize perceptual time. We also agree that by using events to define scales, we ignore the influence of duration. In terms of the categories, we selected these for two reasons: 1) they conveniently group previous phenomena, and 2) they loosely correspond to iconic-, short- and long-term memory. We agree that one could also potentially split it up into two categories (e.g., short- and long-term), but in general, we think any form of discretization will have limitations. For example, Reviewer 1 suggests that the meso category is simply a few micros stacked together. However, there is a rich literature on phenomena associated with sequences of an intermediate length that do not appear to be entirely explained by stacking micro effects (e.g., sequence learning and sequential dependency). We also find that when controlling for micro level effects, there are clear meso level effects. Also, by the logic that meso level effects are just stacked micro effects, one could also argue the same for macro effects. We don’t think this argument is incorrect, rather we think it exemplifies the challenge of discretising temporal scales. Ultimately, the current study was aimed to test whether seemingly disparate phenomena identified in previous work could be captured by unifying principles. To this end we found that these categories were the most useful. However, we have included a “Limitations and future directions” section in the Discussion of the revised manuscript that acknowledges both the alternative scheme proposed by Reviewer 1, and the value of extending this work to consider the influence of duration (as well as events).

Line 488 - Limitations and future directions. One potential limitation of the current study is the categorization of temporal scales according to events, independent of the influence of event duration. While this simplification of time supports comparison between different phenomena associated with each scale (e.g., serial dependence, sequential dependencies, statistical learning), future work could investigate the role of duration to provide a more comprehensive understanding of the mechanisms identified in the current study.

Related to this, while the temporal scales applied here conveniently categorized known sensory phenomena, and partially correspond to iconic-, short-, and long-term memory, they are but one of multiple ways to delineate time. For example, temporal scales could alternatively be defined simply as short- and long-term (e.g., by combining micro and meso scale phenomena). However, this could obscure meaningful differences between phenomena associated with sensory persistence and short-term memory, or qualitative differences in the way that shortsequences of events are processed.

(3) More serious is the issue of precision. Again, this is partially a language problem. When people use the engineering terms "precision" and "accuracy" together, they usually use the same units, such as degrees. Accuracy refers to the distance from the real position (so average accuracy gives bias), and precision is the clustering around the average bias, usually measured as standard deviation. Yet here accuracy is percent correct: also a convention in psychology, but not when contrasting accuracy with precision, in the engineering sense. I suggest you change "accuracy" to "percent correct". On the other hand, I have no idea how precision was defined. All I could find was: "mixture modelling was used to estimate the precision and guess rate of reproduction responses, based on the concentration (k) and height of von Mises and uniform distributions, respectively". I do not know what that means.

In the case of a binary decision, is seems reasonable to use the term “accuracy” to refer to the correspondence between the target state and the response on a task. However, we agree that while our (main) task is binary, the target is not and nor is the secondary task. We thank the reviewer for bringing this to our attention, as we agree that this will be a likely cause of confusion. To avoid confusion we have specifically referred to “task accuracy” throughout the revised manuscript.

With regards to precision, our measure of precision is consistent with what Reviewer 1 describes as such, i.e., the clustering of responses. In particular, the von Mises distribution is essentially a Gaussian distribution in circular space, and the kappa parameter defines the width of the distribution, regardless of the mean, with larger values of kappa indicating narrower (more precise) distributions. We could have used standard deviation to assess precision; however, this would incorrectly combine responses on which participants failed to encode the target (e.g., because of a blink) and were simply guessing. To account for these trials, we applied mixture modelling of guess and genuine responses to isolate the precision of genuine responses, as is standard in the visual working memory literature. However, we agree that this was not sufficiently described in the original manuscript and have elaborated on this method in the revised version.

Line 598 - From the reproduction task, we sought to estimate participant’s recall precision. It is likely that on some trials participants failed to encode the target and were forced to make a response guess. To isolate the recall precision from guess responses, we used mixture modelling to estimate the precision and guess rate of reproduction responses, based on the concentration (k) and height of von Mises and uniform distributions, respectively (Bays et al., 2009). The k parameter of the von Mises distribution reflects its width, which indicates the clustering of responses around a common location.

(4) Previous studies show serial dependence can increase bias but decrease scatter (inverse precision) around the biased estimate. The current study claims to be at odds with that. But are the two measures of precision relatable? Was the real (random) position of the target subtracted from each response, leaving residuals from which the inverse precision was calculated? (If so, the authors should say so..) But if serial dependence biases responses in essentially random directions (depending on the previous position), it will increase the average scatter, decreasing the apparent precision. 

Previous studies have shown that when serial dependence is attractive there is a corresponding increase in precision around small offsets from the previous item (citations). Indeed, attractive biases will lead to reduced scattering (increased precision) around a central attracter. Consistent with previous studies, and this rational, we also found an attractive bias coupled with increased precision. To clarify, for the serial dependency analysis, we calculated bias and precision by binning reproduction responses according to the offset between the current and previous target and then performing the same mixture modelling described above to estimate the mean (bias) and kappa (precision) parameters of the von Mises distribution fit to the angular errors. This was not explained in the original manuscript, so we thank Reviewer 1 for bringing this to our attention and have clarified the analysis in the revised version.

Line 604 - For the serial dependency analysis, we calculated bias and precision by binning reproduction responses according to the angular offset between the current and previous target and then performing mixture modelling to estimate the mean (bias) and k (precision) parameters of the von Mises distribution.

(5) I suspect they are not actually measuring precision, but location accuracy. So the authors could use "percent correct" and "localization accuracy". Or be very clear what they are actually doing. 

As explained in our response to Reviewer 1’s previous comment, we are indeed measuring precision.

Reviewer #2 (Public review):

(1) The abstract should more explicitly mention that conclusions about feedforward mechanisms were derived from a reanalysis of an existing EEG dataset. As it is, it seems to present behavioral data only.

It is not clear what relevance the fact that the data has been analyzed previously has to the results of the current study. However, we do think that it is important to be clear that the EEG recordings were collected separately from the behavioural and eyetracking data, so we have clarified this in the revised abstract.

Line 7 - By integrating behavioural and pupillometry recordings with electroencephalographical recordings from a previous study, we identify two distinct mechanisms that operate across all scales.

(2) The EEG task seems quite different from the others, with location and color changes, if I understand correctly, on streaks of consecutive stimuli shown every 100 ms, with the task involving counting the number of target events. There might be different mechanisms and functions involved, compared to the behavioral experiments reported. 

As stated above, we agree that it is important that readers are aware that the EEG recordings were collected separately to the behavioural and eyetracking data. We were forthright about this in the original manuscript and how now clarified this in the revised abstract. We agree that collecting both sets of data in the same experiment would be a useful validation of the current results and have acknowledged this in a new Limitations and future directions section of the Discussion of the revised manuscript.

Line 501 - Another limitation of the current study is that the EEG recordings were collected in the separate experiment to the behavioural and pupillometry data. The stimuli and task were similar between experiments, but not identical. For example, the EEG experiment employed coloured arc stimuli presented at a constant rate of ~3.3 Hz and participants were tasked with counting the number of stimuli presented at a target location. By contrast, in the behavioural experiment, participants viewed white blobs presented at an average rate of ~2.8 Hz and performed a binary spatial task coupled with an infrequent reproduction task. An advantage of this was that the sensory responses to stimuli in the EEG recordings were not conflated with motor responses; however, future work combining these measures in the same experiment would serve as a validation for the current results.

(3) How is the arbitrary choice of restricting EEG decoding to a small subset of parieto-occipital electrodes justified? Blinks and other artifacts could have been corrected with proper algorithms (e.g., ICA) (Zhang & Luck, 2025) or even left in, as decoders are not necessarily affected by noise. Moreover, trials with blinks occurring at the stimulus time should be better removed, and the arbitrary selection of a subset of electrodes, while reducing the information in input to the decoder, does not account for trials in which a stimulus was missed (e.g., due to blinks).

Electrode selection was based on several factors: 1) reduction of eye movement/blink artifacts (as noted in the original manuscript), 2) consistency with the previous EEG study (Rideaux, 2024) and other similar decoding studies (Buhmann et al., 2024; Harrison et al., 2023; Rideaux et al., 2023), 3) improved signal-to-noise by including only sensors that carry the most position information (as shown in Supplementary Figure 1a and the previous EEG study). We agree that this was insufficiently explained in the original manuscript and have clarified our sensor selection in the revised version.

Line 631 - We only included the parietal, parietal-occipital, and occipital sensors in the analyses to i) reduce the influence of signals produced by eye movements, blinks, and non-sensory cortices, ii) for consistency with similar previous decoding studies (Buhmann et al., 2024; Rideaux, 2024; Rideaux et al., 2025), and iii) to improve decoding accuracy by restricting sensors to those that carried spatial position information (Supplementary Fig. 1a).

(4) The artifact that appears in many of the decoding results is puzzling, and I'm not fully convinced by the speculative explanation involving slow fluctuations. I wonder if a different high-pass filter (e.g., 1 Hz) might have helped. In general, the nature of this artifact requires better clarification and disambiguation.

We agree that the nature of this artifact requires more clarification and disambiguation. Due to relatively slow changes in the neural signal, which are not stimulus-related, there is a degree of temporal autocorrelation in the recordings. This can be filtered out, for example, by using a stricter high-pass filter; however, we tried a range of filters and found that a cut-off of at least 0.7 Hz is required to remove the artifact, and even a filter of 0.2 Hz introduces other (stimulus-related) artifacts, such as above-chance decoding prior to stimulus onset. These stimulus-related artifacts are due to the temporal smearing of data, introduced by the filtering, and have a more pronounced and complex influence on the results and are more difficult to remove through other means, such as the baseline correction applied in the original manuscript.

The temporal autocorrelation is detected by the decoder during training and biases it to classify/decode targets that are presented nearby in time as similar. That is, it learns the neural pattern for a particular stimulus location based on the activity produced by the stimulus and the temporal autocorrelation (determined by slow stimulus unrelated fluctuations). The latter only accounts for a relatively smaller proportion of the variance in the neural recordings under normal circumstances and would typically go undetected when simply plotting decoding accuracy as a function of position. However, it becomes weakly visible when decoding accuracy is plotted as a function of distance from the previous target, as now the bias (towards temporally adjacent targets) aligns with the abscissa. Further, it becomes highly visible when the stimulus labels are shuffled, as now the decoder can only learn from the variance associated with the temporal autocorrelation (and not from the activity produced by the stimulus).

In the linear discriminant analysis, this led to temporally proximal items being more likely to be classified as on the same side. This is why there is above-chance performance for repeat trials (Supplementary Figure 2b), and below-chance performance for alternate trials, even when the labels are shuffled – the temporal autocorrelation produces a general bias towards classifying temporally proximate stimuli as on the same side, which selectively improves the classification accuracy of repeat trials. Fortunately, the bias is relatively constant as a function of time within the epoch and is straightforward to estimate by shuffling the labels, which means that it can be removed through a baseline correction. However, to further demonstrate that the autocorrelation confound cannot account for the differences observed between repeat and alternate trials in the micro classification analysis, we now additionally show the results from a more strictly filtered version of the data (0.7 Hz). These results show a similar pattern as the original, with the additional stimulusrelated artifacts introduced by the strict filter, e.g., above chance decoding prior to stimulus onset.

In the inverted encoding analysis, the same temporal autocorrelation manifests as temporally proximal trials being decoded as more similar locations. This is why there is increased decoding accuracy for targets with small angular offsets from the previous target, even when the labels are shuffled (Supplementary Figure 3c), because it is on these trials that the bias happens to align with the correct position. This leads to an attractive bias towards the previous item, which is most prominent when the labels are shuffled.

To demonstrate the phenomenon, we simulated neural recordings from a population of tuning curves and performed the inverted encoding analysis on a clean version of the data and a version in which we introduced temporal autocorrelation. We then repeated this after shuffling the labels. The simulation produced very similar results to those we observed in the empirical data, with a single exception: while precision in the simulated shuffled data was unaffected by autocorrelation, precision in the unshuffled data was clearly affected by this manipulation. This may explain why we did not find a correlation between the shuffled and unshuffled precision in the original manuscript. 

These results echo those from the classification analysis, albeit in a more continuous space. However, whereas in the classification analysis it was straightforward to perform a baseline correction to remove the influence of general temporal dependency, the more complex nature of the accuracy, precision, and bias parameters over the range of time and delta location makes this approach less appropriate. For example, the bias in the shuffled condition ranged from -180 to 180 degrees, which when subtracted from the bias in the unshuffled condition would produce an equally spurious outcome, i.e., the equal opposite of this extreme bias. Instead for the inverted encoding analysis, we used the data high-pass filtered at 0.7 Hz. As with the classification analysis, this removed the influence of general temporal dependencies, as indicated by the results of the shuffled data analysis (Supplementary Figure 3f), but it also temporally smeared the stimulus-related signal, resulting in above chance decoding accuracy prior to stimulus onset (Supplementary Figure 3d). However, given thar we were primarily interested in the pattern of accuracy, precision, and bias as a function of delta location, and less concerned with the precise temporal dynamics of these changes, which appeared relatively stable in the filtered data. Thus, this was the more suitable approach to removing the general temporal dependencies in the inverted encoding analysis and the one that is presented in Figure 3.

We have updated the revised manuscript in light of these changes, including a fuller description of the artifact and the results from the abovementioned control analyses.

Figure 3 updated.

Figure 3 caption - e) Decoding accuracy for stimulus location, from reanalysis of previously published EEG data (17). Inset shows the EEG sensors included in the analysis (blue dots), and black rectangles indicate the timing of stimulus presentations (solid: target stimulus, dashed: previous and subsequent stimuli). f) Decoding accuracy for location, as a function of time and D location. Bright colours indicate higher decoding accuracy; absolute accuracy values can be inferred from (e). g-i) Average location decoding  (g) accuracy, (h) precision, and (h) bias from 50 – 500 ms following stimulus onset. Horizontal bar in (e) indicates cluster corrected periods of significance; note, all time points were significantly above chance due to temporal smear introduced by strict high-pass filtering (see Supplementary Figure 3 for full details). Note, the temporal abscissa is aligned across (e & f). Shaded regions indicate ±SEM.

Line 218 - To further investigate the influence of serial dependence, we applied inverted encoding modelling to the EEG recordings to decode the angular location of stimuli. We found that decoding accuracy of stimulus location sharply increased from ~60 ms following stimulus onset (Fig. 3e). Note, to reduce the influence of general temporal dependencies, we applied a 0.7 Hz high-pass filter to the data, which temporally smeared the stimulus-related information, resulting in above chance decoding accuracy prior to stimulus presentation (for full details, see Supplementary Figure 3). To understand how serial dependence influences the representation of these features, we inspected decoding accuracy for location as a function of both time and D location (Fig. 3f). We found that decoding accuracy varied depending not only as a function of time, but also as a function of D location. To characterise this relationship, we calculated the average decoding accuracy from 50 ms until the end of the epoch (500 ms), as a function of D location (Fig. 3g). This revealed higher accuracy for targets with larger D location. We found a similar pattern of results for decoding precision (Fig. 3h). These results are consistent with the micro temporal context (behavioural) results, showing that targets that alternated were recalled more precisely. Lastly, we calculated the decoding bias as a function of D location and found a clear repulsive bias away from the previous item (Fig. 3i). While this result is inconsistent with the attractive behavioural bias, it is consistent with recent studies of serial dependence suggesting an initial pattern of repulsion followed by an attractive bias during the response period (20–22).

Line 726 - As shown in Supplementary Figure 3, we found the same general temporal dependencies in the decoding accuracy computed using inverted encoding that were found using linear discriminant classification. However, as a baseline correction would not have been appropriate or effective for the parameters decoded with this approach, we instead used a high-pass filter of 0.7 Hz to remove the confound, while being cautious about interpreting the timing of effects produced by this analysis due to the temporal smear introduced by the filter.

Supplementary Figure 2 updated.

Supplementary Figure 2 caption - Removal of general micro temporal dependencies in EEG responses. We found that there were differences in classification accuracy for repeat and alternate stimuli in the EEG data, even when stimulus labels were shuffled. This is likely due to temporal autocorrelation within the EEG data due to low frequency signal changes that are unrelated to the decoded stimulus dimension. This signal trains the decoder to classify temporally proximal stimuli as the same class, leading to a bias towards repeat classification. For example, in general, the EEG signal during trial one is likely to be more similar to that during trial two than during trial ten, because of low frequency trends in the recordings. If the decoder has been trained to classify the signal associated with trial one as a leftward stimulus, then it will be more likely to classify trial two as a leftward stimulus too. These autocorrelations are unrelated to stimulus features; thus, to isolate the influence of stimulus-specific temporal context, we subtracted the classification accuracy produced by shuffling the stimulus labels from the unshuffled accuracy (as presented in Figure 2e, f). We confirmed that using a stricter high-pass filter (0.7 Hz) removes this artifact, as indicated by the equal decoding accuracy between the two shuffled conditions. However, the stricter high-pass filter temporally smears the stimulus-related signal, which introduces other (stimulus-related) artifacts, e.g., above-chance decoding accuracy prior to stimulus presentation, that are larger and more complex, i.e., changing over time. Thus, we opted to use the original high pass filter (0.1 Hz) and apply a baseline correction. a) The uncorrected classification  accuracy along task related and unrelated planes. Note that these results are the same as the corrected version shown in Figure 2e, because the confound is only apparent when accuracy is grouped according to temporal context.

b) Same as (a), but split into repeat and alternate stimuli, along (left) task-related and (right) unrelated planes. Classification  accuracy when labels are shuffled is also shown. Inset in (a) shows the EEG sensors included in the analysis (blue dots). (c, d) Same as (a, b), but on data filtered using a 0.7 Hz high-pass filter. Black rectangles indicate the timing of stimulus presentations (solid: target stimulus, dashed: previous and subsequent stimuli). Shaded regions indicate ±SEM.

Supplementary Figure 3 updated.

Supplementary Figure 3 caption - Removal of general temporal dependencies in EEG responses for inverted encoding analyses. As described in Methods - Neural Decoding, we used inverted encoding modelling of EEG recordings to estimate the decoding accuracy, precision, and bias of stimulus location. Just as in the linear discriminant classification analysis, we also found the influence of general temporal dependencies in the results produced by the inverted encoding analysis. In particular, there was increased decoding accuracy for targets with low D location. This was weakly evident in the period prior to stimulus presentation, but clearly visible when the labels were shuffled. These results are mirror those from the classification analysis, albeit in a more continuous space. However, whereas in the classification analysis it was straightforward to perform a baseline correction to remove the influence of general temporal dependency, the more complex nature of the accuracy, precision, and bias parameters over the range of time and D location makes this approach less appropriate. For example, the bias in the shuffled condition ranged from -180° to 180°, which when subtracted from the bias in the unshuffled condition would produce an equally spurious outcome, i.e., the equal opposite of this extreme bias. Instead for the inverted encoding analysis, we used the data high-pass filtered at 0.7 Hz. As with the classification analysis, this significantly reduced the influence of general temporal dependencies, as indicated by the results of the shuffled data analysis, but it also temporally smeared the stimulus-related signal, resulting in above chance decoding accuracy prior to stimulus onset. However, we were primarily interested in the pattern of accuracy, precision, and bias as a function of D location, and less concerned with the precise temporal dynamics of these changes. Thus, this was the more suitable approach to removing the general temporal dependencies in the inverted encoding analysis and the one that is presented in Figure 3. (a) Decoding accuracy as a function of time for the EEG data filtered using a 0.1 Hz high-pass filter. Inset shows the EEG sensors included in the analysis (blue dots), and black rectangles indicate the timing of stimulus presentations (solid: target stimulus, dashed: previous and subsequent stimuli). (b, c) The same as (a), but as a function of time and D location for (b) the original data and (c) data with shuffled labels. (d-f) Same as (a-c), but for data filtered using a 0.7 Hz high-pass filter. Shaded regions in (a, d) indicate ±SEM. Horizontal bars in (a, d) indicate cluster corrected periods of significance; note, all time points in (d) were significantly above chance. Note, the temporal abscissa is vertically aligned across plots (a-c & d-f).

In the process of performing these additional analyses and simulations, we became aware that the sign of the decoding bias in the inverted encoding analyses had been interpreted in the wrong direction. That is, where we previously reported an initial attractive bias followed by a repulsive bias relative to the previous target, we have in fact found the opposite, an initial repulsive bias followed by an attractive bias relative to the previous target. Based on the new control analyses and simulations, we think that the latter attractive bias was due to general temporal dependencies. That is, in the filtered data, we only observe a repulsive bias. While the bias associated with serial dependence was not a primary feature of the study, this (somewhat embarrassing) discovery has led to reinterpretation of some results relating to serial dependence. However, it is encouraging to see that our results now align with those of recent studies (Fischer et al., 2024; Luo et al., 2025; Sheehan et al. 2024).

Line 385 - Our corresponding EEG analyses revealed better decoding accuracy and precision for stimuli preceded by those that were different and a bias away from the previous stimulus. These results are consistent with finding that alternating stimuli are recalled more precisely. Further, while the repulsive pattern of biases is inconsistent with the observed behavioural attractive biases, it is consistent with recent work on serial dependence indicating an initial period of repulsion, followed by an attractive bias during the response period (20–22). These findings indicate that serial dependence and first-order sequential dependencies can be explained by the same underlying principle.

(5) Given the relatively early decoding results and surprisingly early differences in decoding peaks, it would be useful to visualize ERPs across conditions to better understand the latencies and ERP components involved in the task.

A rapid presentation design was used in the EEG experiment, and while this is well suited to decoding analyses, unfortunately we cannot resolve ERPs because the univariate signal is dominated by an oscillation at the stimulus presentation frequency (~3 Hz). We agree that this could be useful to examine in future work.

(6) It is unclear why the precision derived from IEM results is considered reliable while the accuracy is dismissed due to the artifact, given that both seem to be computed from the same set of decoding error angles (equations 8-9).

This point has been addressed in our response to point (4).

(7) What is the rationale for selecting five past events as the meso-scale? Prior history effects have been shown to extend much further back in time (Fritsche et al., 2020). 

We used five previous items in the meso analyses to be consistent with previous research on sequential dependencies (Bertelson, 1961; Gao et al., 2009; Jentzsch & Sommer, 2002; Kirby, 1976; Remington, 1969). However, we agree that these effects likely extend further and have acknowledged this in the revied version of the manuscript.

Line 240 - Higher-order sequential dependences are an example of how stimuli (at least) as far back as five events in the past can shape the speed and task accuracy of responses to the current stimulus (9, 10); however, note that these effects have been observed for more than five events (20).

(8) The decoding bias results, particularly the sequence of attraction and repulsion, appear to run counter to the temporal dynamics reported in recent studies (Fischer et al., 2024; Luo et al., 2025; Sheehan & Serences, 2022). 

This point has been addressed in our response to point (4).

(9) The repulsive component in the decoding results (e.g., Figure 3h) seems implausibly large, with orientation differences exceeding what is typically observed in behavior. 

As noted in our response to point (4), this bias was likely due to the general temporal dependency confound and has been removed in the revised version of the manuscript.

(10) The pattern of accuracy, response times, and precision reported in Figure 3 (also line 188) resembles results reported in earlier work (Stewart, 2007) and in recent studies suggesting that integration may lead to interference at intermediate stimulus differences rather than improvement for similar stimuli (Ozkirli et al., 2025).

Thank you for bringing this to our attention, we have acknowledged this in the revised manuscript.

Line 197 - Consistent with our previous binary analysis, and with previous work (19), we also found that responses were faster and more accurate when D location was small (Fig. 3b, c).

(11) Some figures show larger group-level variability in specific conditions but not others (e.g., Figures 2b-c and 5b-c). I suggest reporting effect sizes for all statistical tests to provide a clearer sense of the strength of the observed effects. 

Yes, as noted in the original manuscript, we find significant differences between the variance task-related and -unrelated conditions. We think this is due to opposing forces in the task-related condition: 

“The increased variability of response time differences across the taskrelated plane likely reflects individual differences in attention and prioritization of responding either quickly or accurately. On each trial, the correct response (e.g., left or right) was equally probable. So, to perform the task accurately, participants were motivated to respond without bias, i.e., without being influenced by the previous stimulus. We would expect this to reduce the difference in response time for repeat and alternate stimuli across the taskrelated plane, but not the task-unrelated plane. However, attention may amplify the bias towards making faster responses for repeat stimuli, by increasing awareness of the identity of stimuli as either repeats or alternations (17). These two opposing forces vary with task engagement and strategy and thus would be expected produce increased variability across the task-related plane.” We agree that providing effect sizes may provided a clearer sense of the observed effects and have done so in the revised version of the manuscript.

Line 739 - For Wilcoxon signed rank tests, the rank-biserial correlation (r) was calculated as an estimate of effect size, where 0.1, 0.3, and 0.5 indicate small, medium, and large effects, respectively (54). For Friedman’s ANONA tests, Kendal’s W was calculated as an estimate of effect size, where 0.1, 0.3, and 0.5 indicate small, medium, and large effects, respectively (55).

(12) The statement that "serial dependence is associated with sensory stimuli being perceived as more similar" appears inconsistent with much of the literature suggesting that these effects occur at post-perceptual stages (Barbosa et al., 2020; Bliss et al., 2017; Ceylan et al., 2021; Fischer et al., 2024; Fritsche et al., 2017; Sheehan & Serences, 2022). 

In light of the revised analyses, this statement has been removed from the manuscript.

(13) If I understand correctly, the reproduction bias (i.e., serial dependence) is estimated on a small subset of the data (10%). Were the data analyzed by pooling across subjects?

The dual reproduction task only occurred on 10% of trials. There were approximately 2000 trials, so ~200 reproduction responses. For the micro and macro analyses, this was sufficient to estimate precision within each of the experimental conditions (repeat/alternate, expected/unexpected). However, it is likely that we were not able to reproduce the effect of precision at the meso level across both experiments because we lacked sufficient responses to reliably estimate precision when split across the eight sequence conditions. Despite this, the data was always analysed within subjects.

(14) I'm also not convinced that biases observed in forced-choice and reproduction tasks should be interpreted as arising from the same process or mechanism. Some of the effects described here could instead be consistent with classic priming. 

We agree that the results associated with the forced-choice task (response time task accuracy) were likely due to motor priming, but that a separate (predictive) mechanism may explain the (precision) results associated with the reproduction task. These are two mechanisms we think are operating across the three temporal scales investigated in the current study.

Reviewing Editor Comments:

(1) Clarify task design and measurement: The dense presentation makes it difficult to understand key design elements and their implications. Please provide clearer descriptions of all task elements, and how they relate to each other (EEG vs. behaviour, stimulus plane vs. TR and TU plane, reproduction vs. discrimination and role of priming), and clearly explain how key measures were computed for each of these (e.g., precision, accuracy, reproduction bias).

In the revised manuscript, we have expanded on descriptions of the source and nature of the data (behavioural and EEG), the different planes analyzed in the behavioural task, and how key metrics (e.g., precision) were computed.

(2) Offer more insight into underlying data, including original ERP waveforms to aid interpretation of decoding results and the timing of effects. In particular, unpack the decoding temporal confound further.

In the revised manuscript, we have considerably offered more insight into the decoding results, in particular, the nature of the temporal confound. We were unable to assess ERPs due to the rapid presentation design employed in the EEG experiment.

(3) Justify arbitrary choices such as electrode selection for EEG decoding (e.g., limiting to parieto-occipital sensors), number of trials in meso scale, and the time terminology itself.

In the revised manuscript, we have clarified the reasons for electrode selection.

(3) Discuss deviations from literature: Several findings appear to contradict or diverge from previous literature (e.g., effects of serial dependence). These discrepancies could be discussed in more depth. 

Upon re-analysis of the serial dependence bias and removal of the temporal confound, the results of the revised manuscript now align with those from previous literature, which has been acknowledged.

Reviewer #1 (Recommendations for the authors):

(1) would like to use my reviewer's prerogative to mention a couple of relevant publications. 

Galluzzi et al (Journal of Vision, 2022) "Visual priming and serial dependence are mediated by separate mechanisms" suggests exactly that, which is relevant to this study.

Xie et al. (Communications Psychology, 2025) "Recent, but not long-term, priors induce behavioral oscillations in peri-saccadic vision" also seems relevant to the issue of different mechanisms. 

Thank you for bringing these studies to our attention. We agree that they are both relevant have referenced both appropriately in the revised version of the manuscript.

Reviewer #2 (Recommendations for the authors): 

(1) I find the discussion on attention and awareness (from line 127 onward) somewhat vague and requiring clarification.

We agree that this statement was vague and referred to “awareness” without operationation. We have revised this statement to improve clarity.

Line 135 - However, task-relatedness may amplify the bias towards making faster responses for repeat stimuli, by increasing attention to the identity of stimuli as either repeats or alternations (17).

(2) Line 140: It's hard to argue that there are expectations that the image of an object on the retina is likely to stay the same, since retinal input is always changing. 

We agree that retinal input is often changing, e.g., due to saccades, self-motion, and world motion. However, for a prediction to be useful, e.g., to reduce metabolic expenditure or speed up responses, it must be somewhat precise, so a prediction that retinal input will change is not necessarily useful, unless it can specify what it will change to. Given retinal input of x at time t, the range of possible values of x at time t+1 (predicting change) is infinite. By contrast, if we predict that x=x at time t+1 (no change), then we can make a precise prediction. There is, of course, other information that could be used to reduce the parameter space of predicted change from x at time t, e.g., the value of x at time t-1, and we think this drives predictions too. However, across the infinite distribution of changes from x, zero change will occur more frequently than any other value, so we think it’s reasonable to assert that the brain may be sensitive to this pattern.

(3) Line 564: The gambler's fallacy usually involves sequences longer than just one event.

Yes, we agree that this phenomenon is associated with longer sequences. This section of the manuscript was in regards to previous findings that were not directly relevant to the current study and has been removed in the revised version.

(4) In the shared PDF, the light and dark cyan colors used do not appear clearly distinguishable. 

I expect this is due to poor document processing or low-quality image embeddings. I will check that they are distinguishable in the final version.

References: 

Barbosa, J., Stein, H., Martinez, R. L., Galan-Gadea, A., Li, S., Dalmau, J., Adam, K. C. S., Valls-Solé, J., Constantinidis, C., & Compte, A. (2020). Interplay between persistent activity and activity-silent dynamics in the prefrontal cortex underlies serial biases in working memory. Nature Neuroscience, 23(8), Articolo 8. https://doi.org/10.1038/s41593-020-0644-4

Bliss, D. P., Sun, J. J., & D'Esposito, M. (2017). Serial dependence is absent at the time of perception but increases in visual working memory. Scientific reports, 7(1), 14739. 

Ceylan, G., Herzog, M. H., & Pascucci, D. (2021). Serial dependence does not originate from low-level visual processing. Cognition, 212, 104709. https://doi.org/10.1016/j.cognition.2021.104709

Fischer, C., Kaiser, J., & Bledowski, C. (2024). A direct neural signature of serial dependence in working memory. eLife, 13. https://doi.org/10.7554/eLife.99478.1

Fritsche, M., Mostert, P., & de Lange, F. P. (2017). Opposite effects of recent history on perception and decision. Current Biology, 27(4), 590-595. 

Fritsche, M., Spaak, E., & de Lange, F. P. (2020). A Bayesian and efficient observer model explains concurrent attractive and repulsive history biases in visual perception. eLife, 9, e55389. https://doi.org/10.7554/eLife.55389

Gekas, N., McDermott, K. C., & Mamassian, P. (2019). Disambiguating serial effects of multiple timescales. Journal of vision, 19(6), 24-24. 

Luo, M., Zhang, H., Fang, F., & Luo, H. (2025). Reactivation of previous decisions repulsively biases sensory encoding but attractively biases decision-making. PLOS Biology, 23(4), e3003150. https://doi.org/10.1371/journal.pbio.3003150

Ozkirli, A., Pascucci, D., & Herzog, M. H. (2025). Failure to replicate a superiority effect in crowding. Nature Communications, 16(1), 1637. https://doi.org/10.1038/s41467025-56762-5

Sheehan, T. C., & Serences, J. T. (2022). Attractive serial dependence overcomes repulsive neuronal adaptation. PLoS biology, 20(9), e3001711. 

Stewart, N. (2007). Absolute identification is relative: A reply to Brown, Marley, and

Lacouture (2007).  Psychological  Review, 114, 533-538. https://doi.org/10.1037/0033-295X.114.2.533

Treisman, M., & Williams, T. C. (1984). A theory of criterion setting with an application to sequential dependencies. Psychological review, 91(1), 68. 

Zhang, G., & Luck, S. J. (2025). Assessing the impact of artifact correction and artifact rejection on the performance of SVM- and LDA-based decoding of EEG signals. NeuroImage, 316, 121304. https://doi.org/10.1016/j.neuroimage.2025.121304

Healthcare leaders often rely too heavily on past data, even though the future rarely unfolds the same way as the past. Scenario analysis encourages organizations to think in terms of possibilities, not certainties, which is especially relevant in healthcare, where conditions can change quickly. For example, we can plan for best-case, worst-case, and most likely outcomes during a pandemic. This improves resource planning and highlights the risks of making decisions based on outdated assumptions. It’s a reminder that uncertainty should be treated as part of strategy, not just as an obstacle.

Here, Macaulay challenges the logic of permanently excluding Indians from higher office under British rule. He frames the issue as a series of rhetorical questions, pointing out the contradictions in denying education and advancement to Indians while still claiming to rule justly. His language reveals both a moral stance and a pragmatic one: keeping India submissive through ignorance is unjust and also unwise for Britain’s long-term prosperity. By insisting that knowledge will naturally create ambition, he argues that denying Indians political opportunity would lead to instability. Overall, the passage reveals Macaulay’s conviction that the gradual inclusion of Indians into governance was not only a duty but also a means to strengthen Britain’s honor and secure its empire.

Author response:

The following is the authors’ response to the previous reviews

Reviewer #1 (Public review):

Summary:

The authors aim to explore the effects of the electrogenic sodium-potassium pump (Na<SUP>+</SUP>/K<SUP>+</SUP>ATPase) on the computational properties of highly active spiking neurons, using the weakly-electric fish electrocyte as a model system. Their work highlights how the pump's electrogenicity, while essential for maintaining ionic gradients, introduces challenges in neuronal firing stability and signal processing, especially in cells that fire at high rates. The study identifies compensatory mechanisms that cells might use to counteract these effects, and speculates on the role of voltage dependence in the pump's behavior, suggesting that Na<SUP>+</SUP>/K<SUP>+</SUP>-ATPase could be a factor in neuronal dysfunctions and diseases

Strengths:

(1) The study explores a less-examined aspect of neural dynamics-the effects of Na<SUP>+</SUP>/K<SUP>+</SUP>-ATPase electrogenicity. It offers a new perspective by highlighting the pump's role not only in ion homeostasis but also in its potential influence on neural computation.

(2) The mathematical modeling used is a significant strength, providing a clear and controlled framework to explore the effects of the Na<SUP>+</SUP>/K<SUP>+</SUP>-ATPase on spiking cells. This approach allows for the systematic testing of different conditions and behaviors that might be difficult to observe directly in biological experiments.

(3) The study proposes several interesting compensatory mechanisms, such as sodium leak channelsand extracellular potassium buffering, which provide useful theoretical frameworks for understanding how neurons maintain firing rate control despite the pump's effects.

Weaknesses:

(1) While the modeling approach provides valuable insights, the lack of experimental data to validate the model's predictions weakens the overall conclusions.

(2)The proposed compensatory mechanisms are discussed primarily in theoretical terms without providing quantitative estimates of their impact on the neuron's metabolic cost or other physiological parameters.

Comments on revisions:

The revised manuscript is notably improved.

We thank the reviewer for their concise and accurate summary and appreciate the constructive feedback on the article’s strengths and weaknesses. Experimental work is beyond the scope of our modeling-based study. However, we would like our work to serve as a framework for future experimental studies into the role of the electrogenic pump current (and its possible compensatory currents) in disease, and its role in evolution of highly specialized excitable cells (such as electrocytes).

Quantitative estimates of metabolic costs in this study are limited to the ATP that is required to fuel the Na<SUP>+</SUP>/K<SUP>+</SUP> pump. By integrating the net pump current over time and dividing by one elemental charge, one can find the rate of ATP that is consumed by the Na<SUP>+</SUP>/K<SUP>+</SUP> pump for either compensatory mechanism. The difference in net pump current is thus proportional to ATP consumption, which allows for a direct comparison of the cost efficiency of the Na<SUP>+</SUP>/K<SUP>+</SUP> pump for each proposed compensatory mechanism. The Na<SUP>+</SUP>/K<SUP>+</SUP> pump is however not the only ATP-consuming element in the electrocyte, and some of the compensatory mechanisms induce other costs related to cell ‘housekeeping’ or presynaptic processes. We now added a section in the appendix titled ‘Considerations on metabolic costs of compensatory mechanisms’ (section 11.4), where we provide rough estimates on the influence of the compensatory mechanisms on the total metabolic costs of the cell and membrane space occupation. Although we argue that according these rough estimates, the impact of discussed compensatory mechanisms could be significant, due to the absence of more detailed experimental quantification, a plausible quantitative cost estimate on the whole cell level remains beyond the scope of this article.

Reviewer #1 (Recommendations for the authors):

I just have a few recommendations on the updated manuscript.

(1) When exploring the different roles of Na<SUP>+</SUP>/K<SUP>+</SUP>-ATPase in the Results section, the authors employed many different models. For instance, the voltage equation on page 15, voltage equation (2) on page 22, voltage equation (12) on page 24, voltage equation (30) on page 32, and voltage equation (38) on page 35 are presented as the master equations for their respective biophysical models. Meanwhile, the phase models are presented on page 29 and page 33. I would recommend that the authors clearly specify which equations correspond to each subsection of the Results section and explicitly state which equations were used to generate the data in each figure. This would help readers more easily follow the connections between the models, the results, and the figures.

We thank the reviewer for pointing out that the links of the different voltage equations to the results could be expressed more explicitly in the article. All simulations were done using the ‘master equation’  expressed in Eq. 2, and the other voltage equations that are specified in the article (in the new version of the article Eqs. 13, 31, and 39) are reformulations of Eq. 2 to analytically show different properties of the voltage equation (Eq. 2). This has now been mentioned in the article when formulating the voltage equations, and the equation for the total leak current (in the new version Eq. 3) has been added for completeness.

(2) The authors may want to revisit their description and references concerning Eigenmannia virescens. For example, wave-type weakly electric fish (e.g., Eigenmannia) and pulse-type weakly electric fish (e.g., Gymnotus carapo) exhibit large differences, making references 52-55 may be inappropriate for subsection 4.3.1, as these studies focus on Gymnotus carapo. Additionally, even within wave-type species, chirp patterns vary. For example, Eigenmannia can exhibit short "pauses"-type chirps, whereas Apteronotus leptorhynchus (another waver-form fish) does not (https://pubmed.ncbi.nlm.nih.gov/14692494/).

We thank the reviewer for pointing this out. The citations and phrasing in sections 4.3.1 and 4.3.2 have been updated to specifically refer to the weakly electric fish e. Virescens.

(3) Table on page 21: Please explain why the parameter value (13.5mM) of [Na<SUP>^</SUP>+]_{in} is 10 timeslarger than its value (1.35mM) in reference [26]? How does this value (13.5mM) compare with the range of variable [Na<SUP>^</SUP>+]_{in} in equation (6)?

The intracellular sodium concentration in reference [26] was reported to be 1.35 mM, but the authors also reported an extracellular sodium concentration of 120 mM, and a sodium reversal potential of 55 mV. Upon calculating the sodium reversal potential, we found that an intracellular sodium concentration of 1.35 mM would give a sodium reversal potential of 113 mV. An intracellular sodium concentration of 13.5 mM, on the other hand, leads to the reported and physiological reversal potential of 55 mV. This has now been clarified in the article, and the connection between this value and Eq. 6 (Eq. 7 in the new version) has also been clarified.

Reviewer #2 (Public review):

Summary:

The paper by Weerdmeester, Schleimer, and Schreiber uses computational models to present the biological constraints under which electrocytes - specialized, highly active cells that facilitate electro-sensing in weakly electric fish-may operate. The authors suggest potential solutions that these cells could employ to circumvent these constraints.

Electrocytes are highly active or spiking (greater than 300Hz) for sustained periods (for minutes to hours), and such activity is possible due to an influx of sodium and efflux of potassium ions into these cells after each spike. The resulting ion imbalance must be restored, which in electrocytes, as with many other biological cells, is facilitated by the Na-K pumps at the expense of biological energy, i.e., ATP molecules. For each ATP molecule the pump uses, three positively charged sodium ions from the intracellular space are exchanged for two positively charged potassium ions from the extracellular space. This creates a net efflux of positive ions into the extracellular space, resulting in hyperpolarized potentials for the cell over time. For most cells, this does not pose an issue, as their firing rate is much slower, and other compensatory mechanisms and pumps can effectively restore the ion imbalances. However, in the electrocytes of weakly electric fish, which spike at exceptionally high rates, the net efflux of positive ions presents a challenge. Additionally, these cells are involved in critical communication and survival behaviors, underscoring their essential role in reliable functioning.

In a computational model, the authors test four increasingly complex solutions to the problem of counteracting the hyperpolarized states that occur due to continuous NaK pump action to sustain baseline activity. First, they propose a solution for a well-matched Na leak channel that operates in conjunction with the NaK pump, counteracting the hyperpolarizing states naturally. Their model shows that when such an orchestrated Na leak current is not included, quick changes in the firing rates could have unexpected side effects. Secondly, they study the implications of this cell in the context of chirps-a means of communication between individual fish. Here, an upstream pacemaking neuron entrains the electrocyte to spike, which ceases to produce a so-called chirp - a brief pause in the sustained activity of the electrocytes. In their model, the authors demonstrate that including the extracellular potassium buffer is necessary to obtain a reliable chirp signal. Thirdly, they tested another means of communication in which there was a sudden increase in the firing rate of the electrocyte, followed by a decay to the baseline. For this to occur reliably, the authors emphasize that a strong synaptic connection between the pacemaker neuron and the electrocyte is necessary. Finally, since these cells are energy-intensive, they hypothesize that electrocytes may have energy-efficient action potentials, for which their NaK pumps may be sensitive to the membrane voltages and perform course correction rapidly.

Strengths:

The authors extend an existing electrocyte model (Joos et al., 2018) based on the classical Hodgkin and Huxley conductance-based models of sodium and potassium currents to include the dynamics of the sodium-potassium (NaK) pump. The authors estimate the pump's properties based on reasonable assumptions related to the leak potential. Their proposed solutions are valid and may be employed by weakly electric fish. The authors explore theoretical solutions to electrosensing behavior that compound and suggest that all these solutions must be simultaneously active for the survival and behavior of the fish. This work provides a good starting point for conducting in vivo experiments to determine which of these proposed solutions the fish employ and their relative importance. The authors include testable hypotheses for their computational models.

Weaknesses:

The model for action potential generation simplifies ion dynamics by considering only sodium and potassium currents, excluding other ions like calcium. The ion channels considered are assumed to be static, without any dynamic regulation such as post-translational modifications. For instance, a sodium-dependent potassium pump could modulate potassium leak and spike amplitude (Markham et al., 2013).

This work considers only the sodium-potassium (NaK) pumps to restore ion gradients. However, in many cells, several other ion pumps, exchangers, and symporters are simultaneously present and actively participate in restoring ion gradients. When sodium currents dominate action potentials, and thus when NaK pumps play a critical role, such as the case in Eigenmannia virescens, the present study is valid. However, since other biological processes may find different solutions to address the pump's non-electroneutral nature, the generalizability of the results in this work to other fast-spiking cell types is limited. For example, each spike could include a small calcium ion influx that could be buffered or extracted via a sodium-calcium exchanger.

We thank the reviewer for the detailed summary and the updated identified strengths and weaknesses. The current article indeed focuses on and isolates the interplay between sodium currents, potassium currents, and sodium-potassium pump currents. As discussed in section 5.1, in excitable cells where these currents are the main players in action-potential generation, the results presented in this article are applicable. The contribution of post-translational effects of ion channels, other ionic currents, and other active transporters and pumps, could be exciting avenues for further studies

.

Reviewer #2 (Recommendations for the authors):

Thank you for addressing my comments.

All the figures are now consistent. The color schema used is clear.

The methods and discussions expansions improve the paper.

Including the model assumptions and simplifications is appreciated.

Including internal references is helpful.

The equations are clear, and the references have been fixed.

I am content with the changes. I have updated my review accordingly.

We thank the reviewer for their initial constructive comments that lead to the significant improvement of the article.

Page : 3 Line : 113 Author : Unknown Author 07/24/2025 

Although this is technically correct, the article is about electrocommunication signals and does not focus on sensing.

Page : 3 Line : 153 Author : Unknown Author 07/24/2025

electrocommunication

Page : 4 Line : 164 Author : Unknown Author 07/24/2025 

Judging from the cited article, I think this should be a sodium-dependent potassium current.

Author response:

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

Reviewer #1 (Public review):

Summary:

The authors developed a sequence-based method to predict drug-interacting residues in IDP, based on their recent work, to predict the transverse relaxation rates (R2) of IDP trained on 45 IDP sequences and their corresponding R2 values. The discovery is that the IDPs interact with drugs mostly using aromatic residues that are easy to understand, as most drugs contain aromatic rings. They validated the method using several case studies, and the predictions are in accordance with chemical shift perturbations and MD simulations. The location of the predicted residues serves as a starting point for ligand optimization.

Strengths:

This work provides the first sequence-based prediction method to identify potential druginteracting residues in IDP. The validity of the method is supported by case studies. It is easy to use, and no time-consuming MD simulations and NMR studies are needed.

Weaknesses:

The method does not depend on the information of binding compounds, which may give general features of IDP-drug binding. However, due to the size and chemical structures of the compounds (for example, how many aromatic rings), the number of interacting residues varies, which is not considered in this work. Lacking specific information may restrict its application in compound optimization, aiming to derive specific and potent binding compounds.

We fully recognize that different compounds may have different interaction propensity profiles along the IDP sequence. In future studies, we will investigate compound-specific parameter values. The limiting factor is training data, but such data are beginning to be available.

Reviewer #2 (Public review):

Summary:

In this work, the authors introduce DIRseq, a fast, sequence-based method that predicts druginteracting residues (DIRs) in IDPs without requiring structural or drug information. DIRseq builds on the authors' prior work looking at NMR relaxation rates, and presumes that those residues that show enhanced R2 values are the residues that will interact with drugs, allowing these residues to be nominated from the sequence directly. By making small modifications to their prior tool, DIRseq enables the prediction of residues seen to interact with small molecules in vivo.

Strengths:

The preprint is well written and easy to follow

Weaknesses:

(1) The DIRseq method is based on SeqDYN, which itself is a simple (which I do not mean as a negative - simple is good!) statistical predictor for R2 relaxation rates. The challenge here is that R2 rates cover a range of timescales, so the physical intuition as to what exactly elevated R2 values mean is not necessarily consistent with "drug interacting". Presumably, the authors are not using the helix boost component of SeqDYN here (it would be good to explicitly state this). This is not necessarily a weakness, but I think it would behove the authors to compare a few alternative models before settling on the DIRseq method, given the somewhat ad hoc modifications to SeqDYN to get DIRseq.

Actually, the factors that elevate R2 are well-established. These are local interactions and residual secondary structures (if any). The basic assumption of our method is that intra-IDP interactions that elevate R2 convert to IDP-drug interactions. This assumption was supported by our initial observation that the drug interaction propensity profiles predicted using the original SeqDYN parameters already showed good agreement with CSP profiles. We only made relatively small adjustments to the parameters to improve the agreement. Indeed we did not apply the helix boost portion of SeqDYN to DIRseq, and now state as such (p. 4, second last paragraph). We now also compare DIRseq with several alternative models, as summarized in new Table S2.

Specifically, the authors previously showed good correlation between the stickiness parameter of Tesei et al and the inferred "q" parameter for SeqDYN; as such, I am left wondering if comparable accuracy would be obtained simply by taking the stickiness parameters directly and using these to predict "drug interacting residues", at which point I'd argue we're not really predicting "drug interacting residues" as much as we're predicting "sticky" residues, using the stickiness parameters. It would, I think, be worth the authors comparing the predictive power obtained from DIRseq with the predictive power obtained by using the lambda coefficients from Tesei et al in the model, local density of aromatic residues, local hydrophobicity (note that Tesei at al have tabulated a large set of hydrophobicity scores!) and the raw SeqDYN predictions. In the absence of lots of data to compare against, this is another way to convince readers that DIRseq offers reasonable predictive power.

We now compare predictions of these various parameter sets, and report the results in Table S2.  In short, among all the tested parameter sets, DIRseq has the best performance as measured by (1) strong correlations between prediction scores and CSPs and (2) high true positives and low false positives (p. 7-9).

(2) Second, the DIRseq is essentially SeqDYN with some changes to it, but those changes appear somewhat ad hoc. I recognize that there is very limited data, but the tweaking of parameters based on physical intuition feels a bit stochastic in developing a method; presumably (while not explicitly spelt out) those tweaks were chosen to give better agreement with the very limited experimental data (otherwise why make the changes?), which does raise the question of if the DIRseq implementation of SeqDYN is rather over-parameterized to the (very limited) data available now? I want to be clear, the authors should not be critiqued for attempting to develop a model despite a paucity of data, and I'm not necessarily saying this is a problem, but I think it would be really important for the authors to acknowledge to the reader the fact that with such limited data it's possible the model is over-fit to specific sequences studied previously, and generalization will be seen as more data are collected.

We have explained the rationale for the parameter tweaks, which were limited to q values for four amino-acid types, i.e., to deemphasize hydrophobic interactions and slightly enhance electrostatic interactions (p. 4-5). We now add that these tweaks were motivated by observations from MD simulations of drug interactions with a-syn (ref 13). As already noted in the response to the preceding comment, we now also present results for the original parameter values as well as for when the four q values are changed one at a time.

(3) Third, perhaps my biggest concern here is that - implicit in the author's assumptions - is that all "drugs" interact with IDPs in the same way and all drugs are "small" (motivating the change in correlation length). Prescribing a specific length scale and chemistry to all drugs seems broadly inconsistent with a world in which we presume drugs offer some degree of specificity. While it is perhaps not unexpected that aromatic-rich small molecules tend to interact with aromatic residues, the logical conclusion from this work, if one assumes DIRseq has utility, is that all IDRs bind drugs with similar chemical biases. This, at the very least, deserves some discussion.

The reviewer raises a very important point. In Discussion, we now add that it is important to further develop DIRseq to include drug-specific parameters when data for training become available (p. 12-13). To illustrate this point, we use drug size as a simple example, which can be modeled by making the b parameter dependent on drug molecule size.

(4) Fourth, the authors make some general claims in the introduction regarding the state of the art, which appear to lack sufficient data to be made. I don't necessarily disagree with the author's points, but I'm not sure the claims (as stated) can be made absent strong data to support them. For example, the authors state: "Although an IDP can be locked into a specific conformation by a drug molecule in rare cases, the prevailing scenario is that the protein remains disordered upon drug binding." But is this true? The authors should provide evidence to support this assertion, both examples in which this happens, and evidence to support the idea that it's the "prevailing view" and specific examples where these types of interactions have been biophysically characterized.

We now cite nine studies showing that IDPs remain disordered upon drug binding.

Similarly, they go on to say:

"Consequently, the IDP-drug complex typically samples a vast conformational space, and the drug molecule only exhibits preferences, rather than exclusiveness, for interacting with subsets of residues." But again, where is the data to support this assertion? I don't necessarily disagree, but we need specific empirical studies to justify declarative claims like this; otherwise, we propagate lore into the scientific literature. The use of "typically" here is a strong claim, implying most IDP complexes behave in a certain way, yet how can the authors make such a claim? 

Here again we add citations to support the statement.

Finally, they continue to claim:

"Such drug interacting residues (DIRs), akin to binding pockets in structured proteins, are key to optimizing compounds and elucidating the mechanism of action." But again, is this a fact or a hypothesis? If the latter, it must be stated as such; if the former, we need data and evidence to support the claim.

We add citations to both compound optimization and mechanism of action.

Reviewer #1 (Recommendations for the authors):

(1) The authors should compare the sequences of the IDPs in the case studies with the 45 IDPs in training the SeqDYN model to make sure that they are not included in the training dataset or are highly homologous.

Please note that the data used for training SeqDYN were R2 rates, which are independent of the property being studied here, i.e., drug interacting residues. Therefore whether the IDPs studied here were in the training set for SeqDYN is immaterial.

(2) The authors manually tuned four parameters in SeqDYN to develop the model for predicting drug-interacting residues without giving strict testing or explanations. More explanations, testing of more values, and ablation testing should be given.

As responded above, we now both expand the explanation and present more test results.

(3) The authors changed the q values of L, I, and M to the value of V. What are the results if these values are not changed?

These results are shown in Table S2 (entry named SeqDYN_orig).

(4) Only one b value is chosen based on the assumption that a drug molecule interacts with 3-4 residues at a time. However, the number of interacting residues is related to the size of the drug molecule. Adjusting the b value with the size of the ligand may provide improvement. It is better to test the influence of adjusting b values. At least, this should be discussed.

Good point! We now state that b potentially can be adjusted according to ligand size (p. 12-13). In addition, we also show the effect of varying b on the prediction results (Table S2; p. 8, last paragraph).

(5) The authors add 12 Q to eliminate end effects. However, explanations on why 12 Qs are chosen should be given. How about other numbers of Q or using other residues (e.g., the commonly used residues in making links, like GS/PS or A?

As we already explained, “Gln was selected because its 𝑞 value is at the middle of the 20 𝑞 values.” (p. 5, second paragraph). Also, 12 Qs are sufficient to remove any end effects; a higher number of Qs does not make any difference.

Reviewer #2 (Recommendations for the authors):

(1) The authors make reference to the "C-terminal IDR" in cMyc, but the region they note is found in the bHLH DNA binding domain (which falls from residue ~370-420).

We now clarify that this region is disordered on its own but form a helix-loop-loop structure upon heterodimerization with Max (p. 11, last paragraph).

(2) Given the fact that X-seq names are typically associated with sequencing-based methods, it's perhaps confusing to name this method DIRseq?

We appreciate the reviewer’s point, but by now the preprint posted in bioRxiv is in wide circulation, and the DIRseq web server has been up for several months, so changing its name would cause a great deal of confusion.

(3) I'd encourage the authors just to spell out "drug interacting residues" and retain an IDR acronym for IDRs. Acronyms rarely make writing clearer, and asking folks to constantly flip between IDR and DIR is asking a lot of an audience (in this reviewer's opinion, anyway).

The reviewer makes a good point; we now spell out “drug-interacting residues”.

(4) The assumption here is that CSPs result from direct drug:IDR interactions. However, CSPs result from a change in the residue chemical environment, which could in principle be an indirect effect (e.g., in the unbound state, residues A and B interact; in the bound state, residue A is now free, such that it experiences a CSP despite not engaging directly). While I recognize such assumptions are commonly made, it behoves the authors to explicitly make this point so the reader understands the relationship between CSPs and binding.

We did add caveats of CSP in Introduction (p. 3, second paragraph).

(5) On the figures, please label which protein is which figure, as well as provide a legend for the annotations on the figures (red line, blue bar, cyan region, etc.)

We now label protein names in Fig. 1. For annotation of display items, it is also made in the Figs. 2 and 3 captions; we now add it to the Fig. 4 caption.

(6) abstract: "These successes augur well for deciphering the sequence code for IDP-drug binding." - This is not grammatically correct, even if augur were changed to agree. Suggest rewriting.

“Augur well” means to be a good sign (for something). We use this phrase here in this meaning.

(6) page 5: "we raised the 𝑞 value of Asp to be the same as that of Glu" → suggested "increased" instead of raised.

We have made the suggested change.

(7) The authors should consider releasing the source code (it is available via the .js implementation on the server, but this is not very transferable/shareable, so I'd encourage the authors to provide a stand-alone implementation that's explicitly shareable).

We have now added a link for the user to download the source code.

Author response:

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

eLife Assessment

The authors examine the effect of cell-free chromatin particles (cfChPs) derived from human serum or from dying human cells on mouse cells in culture and propose that these cfChPs can serve as vehicles for cell-to-cell active transfer of foreign genetic elements. The work presented in this paper is intriguing and potentially important, but it is incomplete. At this stage, the claim that horizontal gene transfer can occur via cfChPs is not well supported because it is only based on evidence from one type of methodological approach (immunofluorescence and fluorescent in situ hybridization (FISH)) and is not validated by whole genome sequencing.

We disagree with the eLife assessment that our study is incomplete because we did not perform whole genome sequencing. Tens of thousands of genomes have been sequenced, and yet they have failed to detect the presence of the numerous “satellite genomes” that we describe in our paper. To that extent whole genome sequencing has proved to be an inappropriate technology. Rather, eLife should have commended us for the numerous control experiments that we have done to ensure that our FISH probes and antibodies are target specific and do not cross-react.

Public Reviews:

Reviewer #1 (Public review):

Summary:

Horizontal gene transfer is the transmission of genetic material between organisms through ways other than reproduction. Frequent in prokaryotes, this mode of genetic exchange is scarcer in eukaryotes, especially in multicellular eukaryotes. Furthermore, the mechanisms involved in eukaryotic HGT are unknown. This article by Banerjee et al. claims that HGT occurs massively between cells of multicellular organisms. According to this study, the cell free chromatin particles (cfChPs) that are massively released by dying cells are incorporated in the nucleus of neighboring cells.

The reviewer is mistaken. We do not claim that the internalized cfChPs are incorporated into the nucleus. We show throughout the paper that the cfChPs perform their novel functions autonomously outside the genome without being incorporated into the nucleus. This is clearly seen in all our chromatin fibre images, metaphase spreads and our video abstract. Occasionally, when the cfChPs fluorescent signal overlie the chromosomes, we have been careful to state that the cfChPs are associated with the chromosomes without implying that they have integrated.

These cfChPs are frequently rearranged and amplified to form concatemers, they are made of open chromatin, expressed, and capable of producing proteins. Furthermore, the study also suggests that cfChPs transmit transposable elements (TEs) between cells on a regular basis, and that these TEs can transpose, multiply, and invade receiving cells. These conclusions are based on a series of experiments consisting in releasing cfChPs isolated from various human sera into the culture medium of mouse cells, and using FISH and immunofluorescence to monitor the state and fate of cfChPs after several passages of the mouse cell line.

Strengths:

The results presented in this study are interesting because they may reveal unsuspected properties of some cell types that may be able to internalize free-circulating chromatin, leading to its chromosomal incorporation, expression, and unleashing of TEs. The authors propose that this phenomenon may have profound impacts in terms of diseases and genome evolution. They even suggest that this could occur in germ cells, leading to within-organism HGT with long-term consequences.

Again the reviewer makes the same mistake. We do not claim that the internalized cfChPs are incorporated into the chromosomes. We have addressed this issue above.

We have a feeling that the reviewer has not understood our work – which is the discovery of “satellite genomes” which function autonomously outside the nuclear genome.

Weaknesses:

The claims of massive HGT between cells through internalization of cfChPs are not well supported because they are only based on evidence from one type of methodological approach: immunofluorescence and fluorescent in situ hybridization (FISH) using protein antibodies and DNA probes. Yet, such strong claims require validation by at least one, but preferably multiple, additional orthogonal approaches. This includes, for example, whole genome sequencing (to validate concatemerization, integration in receiving cells, transposition in receiving cells), RNA-seq (to validate expression), ChiP-seq (to validate chromatin state).

We disagree with the reviewer that our study is incomplete because we did not perform whole genome sequencing. Tens of thousands of genomes have been sequenced, and yet they have failed to detect the presence of the numerous “satellite genomes” that we describe in our paper. To that extent whole genome sequencing has proved to be an inappropriate approach. Rather, the reviewer should have commended us for the numerous control experiments that we have done to ensure that our FISH probes and antibodies are target specific and do not cross-react.

Should HGT through internalization of circulating chromatin occur on a massive scale, as claimed in this study, and as illustrated by the many FISH foci observed on Fig 3 for example, one would expect that the level of somatic mosaicism may be so high that it would prevent assembling a contiguous genome for a given organism. Yet, telomere-to-telomere genomes have been produced for many eukaryote species, calling into question the conclusions of this study.

The reviewer has raised a related issue below and we have responded to both of them together.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

I thank the authors for taking my comments and those of the other reviewer into account and for adding new material to this new version of the manuscript. Among other modifications/additions, they now mention that they think that NIH3T3 cells treated with cfChPs die out after 250 passages because of genomic instability which might be caused by horizontal transfer of cfChPs DNA into the genome of treated cells (pp. 45-46, lines 725-731). However, no definitive formal proof of genomic instability and horizontal transfer is provided.

We mention that the NIH3T3 cells treated with cfChPs die out after 250 passages in response to the reviewer’s earlier comment “Should HGT through internalization of circulating chromatin occur on a massive scale, as claimed in this study, and as illustrated by the many FISH foci observed in Fig 3 for example, one would expect that the level of somatic mosaicism may be so high that it would prevent assembling a contiguous genome for a given organism”.

We have agreed with the reviewer and have simply speculated that the cells may die because of extreme genomic instability. We have left it as a speculation without diverting our paper in a different direction to prove genomic instability.

The authors now refer to an earlier study they conducted in which they Illumina-sequenced NIH3T3 cells treated with cfChPs (pp. 48, lines. 781-792). This study revealed the presence of human DNA in the mouse cell culture. However, it is unclear to me how the author can conclude that the human DNA was inside mouse cells (rather than persisting in the culture medium as cfChPs) and it is also unclear how this supports horizontal transfer of human DNA into the genome of mouse cells. Horizontal transfer implies integration of human DNA into mouse DNA, through the formation of phosphodiester bounds between human nucleotides and mouse nucleotides. The previous Illumina-sequencing study and the current study do not show that such integration has occured. I might be wrong but I tend to think that DNA FISH signals showing that human DNA lies next to mouse DNA does not necessarily imply that human DNA has integrated into mouse DNA. Perhaps such signals could result from interactions at the protein level between human cfChPs and mouse chromatin?

With due respect, our earlier genome sequencing study that the reviewer refers to was done on two single cell clones developed following treatment with cfChPs. So, the question of cfChPs lurking in the culture medium does not arise.

The authors should be commended for doing so many FISH experiments. But in my opinion, and as already mentioned in my earlier review of this work, horizontal transfer of human DNA into mouse DNA should first be demonstrated by strong DNA sequencing evidence (multiple long and short reads supporting human/mouse breakpoints; discarding technical DNA chimeras) and only then eventually confirmed by FISH.

As mentioned earlier, we disagree with the reviewer that our study is incomplete because we did not perform whole genome sequencing. Tens of thousands of genomes have been sequenced, and yet they have failed to detect the presence of the numerous “satellite genomes” that we describe in our paper. To that extent whole genome sequencing has proved to be an inappropriate approach. Rather, the reviewer should have commended us for the numerous control experiments that we have done to ensure that our FISH probes and antibodies are target specific and do not cross-react.

Regarding my comment on the quantity of human cfChPs that has been used for the experiments, the authors replied that they chose this quantity because it worked in a previous study. Could they perhaps explain why they chose this quantity in the earlier study? Is there any biological reason to choose 10 ng and not more or less? Is 10 ng realistic biologically? Could it be that 10 ng is orders of magnitude higher than the quantity of cfChPs normally circulating in multicellular organisms and that this could explain, at least in part, the results obtained in this study?

The reviewer again raises the same issue to which we have already addressed in our revised manuscript. To quote “We chose to use 10ng based on our earlier report in which we had obtained robust biological effects such as activation of DDR and activation of apoptotic pathways using this concentration of cfChPs (Mittra I et. al., 2015)”.

It is also mentioned in the response that RNA-seq has been performed on mouse cells treated with cfChPs, and that this confirms human-mouse fusion (genomic integration). Since these results are not included in the manuscript, I cannot judge how robust they are and whether they reflect a biological process rather than technical issues (technical chimeras formed during the RNA-seq protocol is a well-known artifact). In any case, I do not think that genomic integration can be demonstrated through RNA-seq as junction between human and mouse RNA could occur at the RNA level (i.e. after transcription). RNA-seq could however show whether human-mouse chimeras that have been validated by DNA-sequencing are expressed or not.

We did perform transcriptome sequencing as suggested earlier by the reviewer, but realized that the amount of material required to be incorporated into the manuscript to include “material and methods”, “results”, “discussion”, “figures” and “legends to figures” and “supplementary figures and tables” would be so massive that it will detract from the flow of our work and hijack it in a different direction. We have, therefore, decided to publish the transcriptome results as a separate manuscript.

Given these comments, I believe that most of the weaknesses I mentioned in my review of the first version of this work still hold true.

An important modification is that the work has been repeated in other cell lines, hence I removed this criticism from my earlier review.

Additional changes made

(1) We have now rewritten the “Abstract” to 250 words to fit in eLife’s instructions. (It was not possible to reduce the word count further.

(2) We have provided the Video 1 as separate file instead of link.

(3) Some of Figure Supplements (which were stand-alone) are now given as main figures. We have re-arranged Figures and Figure Supplements in accordance with eLife’s instructions.

(4) We have now provided a list of the various cell lines used in this study, their tissue origin and procurement source in Supplementary File 3.

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

Public Reviews:

Reviewer #1 (Public review):

Summary:

Horizontal gene transfer is the transmission of genetic material between organisms through ways other than reproduction. Frequent in prokaryotes, this mode of genetic exchange is scarcer in eukaryotes, especially in multicellular eukaryotes. Furthermore, the mechanisms involved in eukaryotic HGT are unknown. This article by Banerjee et al. claims that HGT occurs massively between cells of multicellular organisms. According to this study, the cell free chromatin particles (cfChPs) that are massively released by dying cells are incorporated in the nucleus of neighboring cells. These cfChPs are frequently rearranged and amplified to form concatemers, they are made of open chromatin, expressed, and capable of producing proteins. Furthermore, the study also suggests that cfChPs transmit transposable elements (TEs) between cells on a regular basis, and that these TEs can transpose, multiply, and invade receiving cells. These conclusions are based on a series of experiments consisting in releasing cfChPs isolated from various human sera into the culture medium of mouse cells, and using FISH and immunofluorescence to monitor the state and fate of cfChPs after several passages of the mouse cell line.

Strengths:

The results presented in this study are interesting because they may reveal unsuspected properties of some cell types that may be able to internalize free-circulating chromatin, leading to its chromosomal incorporation, expression, and unleashing of TEs. The authors propose that this phenomenon may have profound impacts in terms of diseases and genome evolution. They even suggest that this could occur in germ cells, leading to within-organism HGT with long-term consequences.

Weaknesses:

The claims of massive HGT between cells through internalization of cfChPs are not well supported because they are only based on evidence from one type of methodological approach: immunofluorescence and fluorescent in situ hybridization (FISH) using protein antibodies and DNA probes. Yet, such strong claims require validation by at least one, but preferably multiple, additional orthogonal approaches. This includes, for example, whole genome sequencing (to validate concatemerization, integration in receiving cells, transposition in receiving cells), RNA-seq (to validate expression), ChiP-seq (to validate chromatin state).

We have responded to this criticism under “Reviewer #1 (Recommendations for the authors, item no. 1-4)”.

Another weakness of this study is that it is performed only in one receiving cell type (NIH3T3 mouse cells). Thus, rather than a general phenomenon occurring on a massive scale in every multicellular organism, it could merely reflect aberrant properties of a cell line that for some reason became permeable to exogenous cfChPs. This begs the question of the relevance of this study for living organisms.

We have responded to this criticism under “Reviewer #1 (Recommendations for the authors, item no. 6)”.

Should HGT through internalization of circulating chromatin occur on a massive scale, as claimed in this study, and as illustrated by the many FISH foci observed in Fig 3 for example, one would expect that the level of somatic mosaicism may be so high that it would prevent assembling a contiguous genome for a given organism. Yet, telomere-to-telomere genomes have been produced for many eukaryote species, calling into question the conclusions of this study.

The reviewer is right in expecting that the level of somatic mosaicism may be so high that it would prevent assembling a contiguous genome. This is indeed the case, and we find that beyond ~ 250 passages the cfChPs treated NIH3T3 cells begin to die out apparently become their genomes have become too unstable for survival. This point will be highlighted in the revised version (pp. 45-46, lines 725-731).

Reviewer #2 (Public review):

I must note that my comments pertain to the evolutionary interpretations rather than the study's technical results. The techniques appear to be appropriately applied and interpreted, but I do not feel sufficiently qualified to assess this aspect of the work in detail.

I was repeatedly puzzled by the use of the term "function." Part of the issue may stem from slightly different interpretations of this word in different fields. In my understanding, "function" should denote not just what a structure does, but what it has been selected for. In this context, where it is unclear if cfChPs have been selected for in any way, the use of this term seems questionable.

We agree. We have removed the term “function” wherever we felt we had used it inappropriately.

Similarly, the term "predatory genome," used in the title and throughout the paper, appears ambiguous and unjustified. At this stage, I am unconvinced that cfChPs provide any evolutionary advantage to the genome. It is entirely possible that these structures have no function whatsoever and could simply be byproducts of other processes. The findings presented in this study do not rule out this neutral hypothesis. Alternatively, some particular components of the genome could be driving the process and may have been selected to do so. This brings us to the hypothesis that cfChPs could serve as vehicles for transposable elements. While speculative, this idea seems to be compatible with the study's findings and merits further exploration.

We agree with the reviewer’s viewpoint. We have replaced the term “predatory genome” with a more realistic term “satellite genome” in the title and throughout the manuscript. We have also thoroughly revised the discussion section and elaborated on the potential role of LINE-1 and Alu elements carried by the concatemers in mammalian evolution. (pp. 46-47, lines 743-756).

I also found some elements of the discussion unclear and speculative, particularly the final section on the evolution of mammals. If the intention is simply to highlight the evolutionary impact of horizontal transfer of transposable elements (e.g., as a source of new mutations), this should be explicitly stated. In any case, this part of the discussion requires further clarification and justification.

As mentioned above, we have revised the “discussion” section taking into account the issues raised by the reviewer and highlighted the potential role of cfChPs in evolution by acting as vehicles of transposable elements.

In summary, this study presents important new findings on the behavior of cfChPs when introduced into a foreign cellular context. However, it overextends its evolutionary interpretations, often in an unclear and speculative manner. The concept of the "predatory genome" should be better defined and justified or removed altogether. Conversely, the suggestion that cfChPs may function at the level of transposable elements (rather than the entire genome or organism) could be given more emphasis.

As mentioned above, we have replaced the term “predatory genome” with “satellite genome” and revised the “discussion” section taking into account the issues raised by the reviewer.

Reviewer #1 (Recommendations for the authors):

(1) I strongly recommend validating the findings of this study using other approaches. Whole genome sequencing using both short and long reads should be used to validate the presence of human DNA in the mouse cell line, as well as its integration into the mouse genome and concatemerization. Breakpoints between mouse and human DNA can be searched in individual reads. Finding these breakpoints in multiple reads from two or more sequencing technologies would strengthen their biological origin. Illumina and ONT sequencing are now routinely performed by many labs, such that this validation should be straightforward. In addition to validating the findings of the current study, it would allow performance of an in-depth characterization of the rearrangements undergone by both human cfChPs and the mouse genome after internalization of cfChPs, including identification of human TE copies integrated through bona fide transposition events into the mouse genome. New copies of LINE and Alu TEs should be flanked by target site duplications. LINE copies should be frequently 5' truncated, as observed in many studies of somatic transposition in human cells.

(2) Furthermore, should the high level of cell-to-cell HGT detected in this study occur on a regular basis within multicellular organisms, validating it through a reanalysis of whole genome sequencing data available in public databases should be relatively easy. One would expect to find a high number of structural variants that for some reason have so far gone under the radar.

(3) Short and long-read RNA-seq should be performed to validate the expression of human cfChPs in mouse cells. I would also recommend performing ChIP-seq on routinely targeted histone marks to validate the chromatin state of human cfChPs in mouse cells.

(4) The claim that fused human proteins are produced in mouse cells after exposing them to human cfChPs should be validated using mass spectrometry.

The reviewer has suggested a plethora of techniques to validate our findings. Clearly, it is neither possible to undertake all of them nor to incorporate them into the manuscript. However, as suggested by the reviewer, we did conduct transcriptome sequencing of cfChPs treated NIH3T3 cells and were able to detect the presence of human-human fusion sequences (representing concatemerisation) as well as human-mouse fusion sequences (representing genomic integration). However, we realized that the amount of material required to be incorporated into the manuscript to include “material and methods”, “results”, “discussion”, “figures” and “legends to figures” and “supplementary figures and tables” would be so massive that it will detract from the flow of our work and hijack it in a different direction. We have, therefore, decided to publish the transcriptome results as a separate manuscript. However, to address the reviewer’s concerns we have now referred to results of our earlier whole genome sequencing study of NIH3T3 cells similarly treated with cfChPs wherein we had conclusively detected the presence of human DNA and human Alu sequences in the treated mouse cells. These findings have now been added as an independent paragraph (pp. 48, lines. 781-792).

(5) It is unclear from what is shown in the paper (increase in FISH signal intensity using Alu and L1 probes) if the increase in TE copy number is due to bona fide transposition or to amplification of cfChPs as a whole, through mechanisms other than transposition. It is also unclear whether human TEs end up being integrated into the neighboring mouse genome. This should be validated by whole genome sequencing.

Our results suggest that TEs amplify and increase their copy number due to their association with DNA polymerase and their ability to synthesize DNA (Figure 14a and b). Our study design cannot demonstrate transposition which will require real time imaging.

The possibility of incorporation of TEs into the mouse genome is supported by our earlier genome sequencing work, referred to above, wherein we detected multiple human Alu sequences in the mouse genome (pp. 48, lines. 781-792).

(6) In order to be able to generalize the findings of this study, I strongly encourage the authors to repeat their experiments using other cell types.

We thank the reviewer for this suggestion. We have now used four different cell lines derived from four different species and demonstrated that horizontal transfer of cfChPs occur in all of them suggesting that it is a universal phenomenon. (pp. 37, lines 560-572) and (Supplementary Fig. S14a-d).

We have also mentioned this in the abstract (pp. 3, lines 52-54).

(7) Since the results obtained when using cfChPs isolated from healthy individuals are identical to those shown when using cfChPs from cancer sera, I wonder why the authors chose to focus mainly on results from cancer-derived cfChPs and not on those from healthy sera.

Most of the experiments were conducted using cfChPs isolated from cancer patients because of our especial interest in cancer, and our earlier results (Mittra et al., 2015) which had shown that cfChPs isolated from cancer patients had significantly greater activity in terms of DNA damage and activation of apoptotic pathways than those isolated from healthy individuals. We have now incorporated the above justification on (pp. 6, lines. 124-128).

(8) Line 125: how was the 10-ng quantity (of human cfChPs added to the mouse cell culture) chosen and how does it compare to the quantity of cfChPs normally circulating in multicellular organisms?

We chose to use 10ng based on our earlier report in which we had obtained robust biological effects such as activation of DDR and apoptotic pathways using this concentration of cfChPs (Mittra I et. al. 2015). We have now incorporated the justification of using this dose in our manuscript (pp. 51-52, lines. 867-870).

(9) Could the authors explain why they repeated several of their experiments in metaphase spreads, in addition to interphase?

We conducted experiments on metaphase spreads in addition to those on chromatin fibres because of the current heightened interest in extra-chromosomal DNA in cancer, which have largely been based on metaphase spreads. We were interested to see how the cfChP concatemers might relate to the characteristics of cancer extrachromosomal DNA and whether the latter in fact represent cfChPs concatemers acquired from surrounding dying cancer cells. We have now mentioned this on pp. 7, lines 150-155.

(10) Regarding negative controls consisting in checking whether human probes cross-react with mouse DNA or proteins, I suggest that the stringency of washes (temperature, reagents) should be clearly stated in the manuscript, such that the reader can easily see that it was identical for controls and positive experiments.

We were fully aware of these issues and were careful to ensure that washing steps were conducted meticulously. The careful washing steps have been repeatedly emphasized under the section on “Immunofluorescence and FISH” (pp. 54-55, lines. 922-944).

(11) I am not an expert in Immuno-FISH and FISH with ribosomal probes but it can be expected that ribosomal RNA and RNA polymerase are quite conserved (and thus highly similar) between humans and mice. A more detailed explanation of how these probes were designed to avoid cross-reactivity would be welcome.

We were aware of this issue and conducted negative control experiment to ensure that the human ribosomal RNA probe and RNA polymerase antibody did not cross-react with mouse. Please see Supplementary Fig. S4c.

(12) Finally, I could not understand why the cfChPs internalized by neighboring cells are called predatory genomes. I could not find any justification for this term in the manuscript.

We agree and this criticism has also been made by #Reviewer 2. We have now replaced the term “predatory” genomes with “satellite” genomes.

Reviewer #2 (Recommendations for the authors):

(1) P2 L34: The term "role" seems to imply "what something is supposed to do" (similar to "function"). Perhaps "impact" would be more neutral. Additionally, "poorly defined" is vague-do you mean "unknown"?

We thank the reviewer for this suggestion. We have now rephrased the sentence to read “Horizontal gene transfer (HGT) plays an important evolutionary role in prokaryotes, but it is thought to be less frequent in mammals.” (pp. 2, lines. 26-27).

(2) P2 L35: It seems that the dash should come after "human blood."

Thank you, we have changed the position of the dash (pp. 2, line. 29).

(3) P2 L37: Must we assume these structures have a function? Could they not simply be side effects of other processes?

We think this is a matter of semantics, especially since we show that cfChPs once inside the cell perform many functions such as replication, DNA synthesis, RNA synthesis, protein synthesis etc. We, therefore, think the word “function” is not inappropriate.

(4) Abstract: After reading the abstract, I am unclear on the concept of a "predatory genome." Based on the summarized results, it seems one cannot conclude that these elements provide any adaptive value to the genome.

We agree. We have now replaced the term “predatory” genomes with a more realistic term viz. “satellite” genomes.

(5) Video abstract: The video abstract does not currently stand on its own and needs more context to be self-explanatory.

Thank you for pointing this out. We have now created a new and much more professional video with more context which we hope will meet with the reviewer’s approval.

(6) P4 L67: Again, I am uncertain that HGT should be said to have "a role" in mammals, although it clearly has implications and consequences. Perhaps "role" here is intended to mean "consequence"?

We have now changed the sentence to read as follows “However, defining the occurrence of HGT in mammals has been a challenge” (pp. 4, line. 73).

(7) P6 L111: The phrase "to obtain a new perspective about the process of evolution" is unclear. What exactly is meant by this statement?

We have replaced this sentence altogether which now reads “The results of these experiments are presented in this article which may help to throw new light on mammalian evolution, ageing and cancer” (pp. 5-6, lines 116-118).

(8) P38 L588: The term "predatory genome" has not been defined, making it difficult to assess its relevance.

This issue has been addressed above.

(9) P39 L604: The statement "transposable elements are not inherent to the cell" suggests that some TEs could originate externally, but this does not rule out that others are intrinsic. In other words, TEs are still inherent to the cell.

This part of the discussion section has been rewritten and the above sentence has been deleted.

(10) P39 L609: The phrase "may have evolutionary functions by acting as transposable elements" is unclear. Perhaps it is meant that these structures may serve as vehicles for TEs?

This sentence has disappeared altogether in the revised discussion section.

(11) P41 L643: "Thus, we hypothesize ... extensively modified to act as foreign genetic elements." This sentence is unclear. Are the authors referring to evolutionary changes in mammals in general (which overlooks the role of standard mutational processes)? Or is it being proposed that structural mutations (including TE integrations) could be mediated by cfChPs in addition to other mutational mechanisms?

We have replaced this sentence which now reads “Thus, “within-self” HGT may occur in mammals on a massive scale via the medium of cfChP concatemers that have undergone extensive and complex modifications resulting in their behaviour as “foreign” genetic elements” (pp. 47, lines 763-766).

(12) P41 L150: The paragraph beginning with "It has been proposed that extreme environmental..." transitions too abruptly from HGT to adaptation. Is it being proposed that cfChPs are evolutionary processes selected for their adaptive potential? This idea is far too speculative at this stage and requires clarification.

We agree. This paragraph has been removed.

(13) P43 L681: This summary appears overly speculative and unclear, particularly as the concept of a "predatory genome" remains undefined and thus cannot be justified. It suggests that cfChPs represent an alternative lifestyle for the entire genome, although alternative explanations seem far more plausible at this point.

We have now replaced the term “predatory” genome with “satellite” genome. The relevant part of the summary section has also been partially revised (pp. 49-50, lines 817-831).

Changes independent of reviewers’ comments.

We have made the following additions / modifications.

(1) The abstract has been modified and it’s “conclusion” section has been rewritten.

(2) Section 1.14 has been newly added together with accompanying Figures 15 a,b and c.

(3) The “Discussion” section has been greatly modified and parts of it has been rewritten.

Author response:

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

Reviewer #1 (Public review):

Summary:

The present work studies the coevolution of HIV-1 and the immune response in clinical patient data. Using the Marginal Path Likelihood (MPL) framework, they infer selection coefficients for HIV mutations from time-series data of virus sequences as they evolve in a given patient.

Strengths:

The authors analyze data from two human patients, consisting of HIV population sequence samples at various points in time during the infection. They infer selection coefficients from the observed changes in sequence abundance using MPL. Most beneficial mutations appear in viral envelop proteins. The authors also analyze SHIV samples in rhesus macaques, and find selection coefficients that are compatible with those found in the corresponding human samples.

Weaknesses:

The MPL method used by the authors considers only additive effects of mutations, thus ignoring epistasis.

As suggested, we have now addressed this limitation by inferring epistatic fitness landscapes for CH505, CH848, SHIV.CH505, and SHIV.CH848. Indeed, the computational burden of the epistasis inference procedure was one constraint that motivated us to consider only additive fitness in the previous version of our paper. The original approach developed by Sohail et al. (2022) tested only sequences with <50 sites due to this limitation, far smaller than the ones we consider. Beyond this computational constraint, we also believed that 1) an additive fitness model may suffice to capture local fitness landscapes, and practically, 2) epistatic interactions are more challenging to validate than the effects of individual mutations, making the interpretation of the model more complex.

However, after performing the analyses described in this paper, we developed a new approach for identifying epistatic interactions that can scale to much longer sequences (Shimagaki et al., Genetics, in press). We therefore applied this method to infer an epistatic fitness landscape for the HIV and SHIV data sets that we studied. As in that work, we focused on short-range (<50 bp) interactions which we could more confidently estimate from data. We have added a section in the SI describing the epistatic fitness model and our analysis. 

Overall, we found substantial agreement between the epistatic and purely additive models in terms of the estimated fitness effects of individual mutations (new Supplementary Fig. 8) and overall fitness (Supplementary Fig. 9). Consistent with our prior work, we did not find substantial evidence for very strong epistatic interactions (Supplementary Fig. 10). This does not necessarily mean that strong epistatic interactions do not exist; rather, this shows that strong interactions don’t substantially improve the fit of the model to data, and thus many are regularized toward zero. While the biological validation of epistatic interactions is challenging, we found that the largest epistatic interactions, which we defined as the top 1% of all shortrange interactions, were modestly but significantly enriched in the CD4 binding site, V1 and V5 regions for CH505 and in the CD4 binding site, V4, and V5 for CH848. In addition, mutation pairs N280S/V281A and E275K/V281G, which confer resistance to CH235, ranked in the top 15% of all epistatic interactions in CH505.

We have now included an additional section in the Results, “Robustness of inferred selection to changes in the fitness model and finite sampling”, which discusses our epistatic analyses (page 6, lines 415-464), along with the above Supplementary Figures and a technical section in the SI summarizing the epistasis inference approach.

Although the evolution of broadly neutralizing antibodies (bnAbs) is a motivating question in the introduction and discussion sections (and the title), the relevance of the analysis and results to better understanding how bnAbs arise is not clear. The only result presented in direct connection to bnAbs is Figure 6.

It is true that, while bnAb development is a major motivator of our study, our analysis focuses on HIV-1 and does not directly consider antibody evolution. We have now brought attention to this point as a limitation directly in the Discussion. Following the suggestion below in the “Recommendations for the authors,” we have edited our manuscript to place more emphasis on viral fitness and somewhat reduce the emphasis on bnAbs, though this remains an important motivating factor. Specifically, the Abstract now begins

Human immunodeficiency virus (HIV)-1 evolves within individual hosts to escape adaptive immune responses while maintaining its capacity for replication. Coevolution between the HIV-1 and the immune system generates extraordinary viral genetic diversity. In some individuals, this process also results in the development of broadly neutralizing antibodies (bnAbs) that can neutralize many viral variants, a key focus of HIV-1 vaccine design. However, a general understanding of the forces that shape virusimmune coevolution within and across hosts remains incomplete. Here we performed a quantitative study of HIV-1 evolution in humans and rhesus macaques, including individuals who developed bnAbs.

We have similarly modified the Discussion to focus first on viral fitness. In response to comments from Reviewer 3, we have also more clearly articulated how our work might contribute to the understanding of bnAb development in the Discussion.

Questions or suggestions for further discussion:

I list here a number of points for which I believe the paper would benefit if additional discussion/results were included.

The MPL method used by the authors considers only additive effects of mutations, thus ignoring epistasis. In Sohail et al (2022) MBE 39(10), p. msac199  (https://doi.org/10.1093/molbev/msac199) an extension of MPL is developed allowing one to infer epistasis. Can the authors comment on why this was not attempted here?

I presume one possible reason is that epistasis inference requires considerably more computational effort (and more data). However, since the authors find most beneficial mutations occurring in Env, perhaps restricting the analysis to Env genes only (e.g. the trimer shown in Figure 2) can lead to tractable inference of epistasis within this segment (instead of the full genome).

As described above, we have now addressed this comment by inferring epistatic fitness landscapes for the data sets that we consider. Our overall results using the epistatic fitness model are consistent with the ones that we previously obtained with an additive model.

Do the authors find correlations in the inferred selection coefficients of the two samples CH505 and CH848? I could not find any discussion of this in the manuscript. Only correlations between Humans and RM are discussed.

To address this question, we compared the fitness values and individual selection coefficients across CH505 and CH848 data sets. We found little correlation between CH505 and CH848 fitness values (shown in a new Supplementary Fig. 6) or selection coefficients. We found only 199 common mutations between HIV-1 amino acid sequences from CH505 and CH848 out of 868 and 1,406 total mutations, respectively. Thus, we were not surprised to find no strong relationship between fitness estimates from CH505 and CH848 data sets. 

Reviewer #2 (Public review):

Summary:

This paper combines a biological topic of interest with the demonstration of important theoretical/methodological advances. Fitness inference is the foundation of the quantitative analysis of adapting systems. It is a hard and important problem and this paper highlights a compelling approach (MPL) first presented in (1) and refined in (2), roughly summarized in equation 12.

(1) Sohail, M. S., Louie, R. H., McKay, M. R. & Barton, J. P. Mpl resolves genetic linkage in fitness inference from complex evolutionary histories. Nature biotechnology 39, 472-479 (2021).

(2) Shimagaki, K. & Barton, J. P. Bézier interpolation improves the inference of dynamical models from data. Physical Review E 107, 024116 (2023).

The authors find that positive selection shapes the variable regions of env in shared patterns across two patient donors. The patterns of positive selection are interesting in and of themselves, they confirm the intuition that hyper-variation in env is the result of immune evasion rather than a broadly neutral landscape (flatness). They show that the immune evasion patterns due to CD8 T and naive B-cell selection are shared across patients. Furthermore, they suggest that a particular evolutionary history (larger flux to high fitness states) is associated with bNAb emergence. Mimicking this evolutionary pattern in vaccine design may help us elicit bNAbs in patients in the future.

There is a lot of information to be found in the full fitness landscape of env. The enormous strength of reversion-to-consensus in the patterns is a known pattern of HIV post-infection populations but they are nicely quantified here. Agreement between SHIV and HIV evolution is shown. They find selection is larger for autologous antibodies than the bNAbs themselves (perhaps bNAbs are just too small a component of the host response to drive the bulk of selection?), and that big fitness increases precede antibody breadth in rhesus macaques, suggesting that this fitness increase is the immune challenge required to draw forth a bNAb. This is all of high interest to HIV researchers.

Strength of evidence:

One limitation is, of course, that the fitness model is constant in time when the immune challenge is variable and changing. This simplification may complicate some interpretations.

We agree that this is a limitation of our current approach. In prior work, we have found that the constant fitness effects of mutations that we infer typically reflect the time-averaged fitness effect when the selection changes over time (Gao and Barton, PNAS 2025; Lee et al., Nat Commun 2025). It could be difficult, however, to capture changes in selection that fluctuate rapidly with underlying immune responses. We have added a new paragraph in the Discussion that more clearly sets out some of the limitations of our analysis, including our assumption of constant selection coefficients.

There are additional methodological and technical limitations that should be considered in the interpretation of our results. Most notably, we assume that the viral fitness landscape is static in time. While we do not expect selection for effective replication (“intrinsic” fitness) to change substantially over time, pressure for immune escape could vary along with the immune responses that drive them. In prior work, we have found that constant selection coefficients typically reflect the average fitness effect of a mutation when its true contribution to fitness is time-varying [42,43]. This may not adequately description mutational effects that undergo large or rapid shifts in time. Future work should also examine temporal patterns in selection for individual mutations.

Equation 12 in the methods is really a beautiful tool because it is so simple, but accounts for linkage and can be solved precisely even in the presence of detailed mutational and selection models. However, the reliance on incomplete observations of the frequency leads to complications that must be carefully (re)addressed here.

For instance, the consistent finding of strong selection in hypervariable regions is biologically intuitive but so striking, that I worry that it might be the result of a bias for selection in high entropy regions. 

Thank you for this suggestion. We agree that it is important to carefully interrogate these results. To assess the effects of general sequence variability on inferred selection, we first computed a position-specific entropy measure, H<sub >i</sub >, for each site i. We first defined the time-dependent entropy H<sub >i</sub >(t) = - ∑<sub >a</sub> x_i (a, t) log x_i (a, t)), where x_i (a, t) represents the frequency of amino acid/nucleotide a at position i and time t, at each sample time. We then computed H_i as the average of H_i(t) across all sample times. A new Supplementary Fig. 1 plots the entropy against the inferred selection coefficients. Although some sequence variation must be observed in order for us to infer that a mutation is beneficial, we did not find a systematic bias toward larger (more beneficial) selection coefficients at more variable sites. Overall, we found only a modest correlation between inferred selection coefficients and entropy (Pearson’s r = 0.33 and 0.29 for CH505 and CH848, respectively), which appears to be partly driven by the tendency for mutations inferred to be significantly deleterious to occur at sites with low entropy. In addition to the new Supplementary Figure, we have added a reference to this analysis in the main text:

To test whether our results might be biased by overall sequence variability, we examined the relationship between our inferred selection coefficients and entropy, a common measure of sequence variability. Overall, we found only a modest correlation between selection and entropy, suggesting that the signs of selection that we observe are not due to increased sequence variability alone (Supplementary Fig. 1).

Mutational and covariance terms in equation 12 might be underestimated, due to finite sampling effect in highly diverse populations. Sampling effects lead to zeros in x(t) when actual frequency zeros might be rare at the population sizes of HIV viral loads and mutation rates. Both mutational flux and C underestimation will bias selection upward in eq. 12. 

The prior papers (1) and (2) seem to show robustness to finite sampling effects, but, again, more care needs to be shown that this robustness transfers to the amino acid inference under these conditions. That synonymous sites are rarely selected for in the nucleotide level is a good sign, and it may be a matter of simply fully explaining the amino-acid level model.

As above, we agree that these tests are important. To assess the robustness of our results to finite sampling, we performed bootstrap sampling on the viral sequences and inferred selection coefficients using the resampled sequences. Specifically, we resampled the same number of sequences as in the original data at each time point and repeated this for all time points across all HIV-1 and SHIV data sets. A new Supplementary Fig. 11 shows a typical comparison of the original selection coefficients vs. those obtained through bootstrap resampling. Overall, we observe a high degree of consistency between the selection coefficients in each case, which is surely aided by the long time series in these data sets. As pointed out by the reviewer, uncertainty in low-frequency mutations is a particular concern, though the effects on inferred selection are mitigated by regularization. 

We have added a section in the Results, “Robustness of inferred selection to changes in the fitness model and finite sampling”, which includes this analysis:

Finite sampling of sequence data could also affect our analyses. To further test the robustness of our results, we inferred selection coefficients using bootstrap resampling, where we resample sequences from the original ensemble, maintaining the same number of sequences for each time point and subject. The selection coefficients from the bootstrap samples are consistent with the original data (see Supplementary Fig. 11), with Pearson’s r values of around 0.85 for HIV-1 data sets and 0.95 for SHIV data sets, respectively.

Uncertainty propagates to the later parts of the paper, eg. HIV and SIV shared patterns might be the result of shared biases in the method application. However, this worry does not extend to the apples-to-apples comparison of fitness trajectories across individuals (Figures 5 and 6) which I think are robust (for these sample sizes). 

One way to address this uncertainty is to compare the fitness values and individual selection coefficients across CH505 and CH848 data sets, which was also requested by Reviewer 1. Overall, we found little correlation between CH505 and CH848 fitness values (shown in a new Supplementary Fig. 6) or selection coefficients. This suggests that similarities between HIV-1 and SHIV landscapes are not solely determined by potential biases in the inference approach. We have now added a reference to this point in the main text:

In contrast, the inferred fitness landscapes of CH505 and CH848, which share few mutations in common, are poorly correlated (Supplementary Fig. 6). This suggests that the similarities between viral fitness values in humans and RMs are not artifacts of the model, but rather stem from similarities in underlying evolutionary drivers.

The timing evidence is slightly weakened by the fact that bNAb detection is different from bNAb presence and the possibility that fitness increases occurred after the bNAbs appeared remains. Still, their conclusion is plausible and fits in with the other observations which form a coherent and compelling picture.

Yes, we agree that this is a limitation of our analysis — bNAbs may have been present at low levels before they were detected, and we cannot definitively reject selection by bNAbs. Nonetheless, in at least one case (RM5695), rapid fitness gains were substantially separated in time from bNAb detection (roughly 2 weeks after infection vs. 16 weeks, respectively). We have now added this point in a new paragraph in the Discussion:

While we found a strong relationship between viral fitness dynamics and the emergence of bnAbs, it may not be true that the former stimulates the latter. For example, bnAbs may have been present within each host before they were experimentally detected. Rapid viral fitness gains within hosts that developed broad antibody responses could then have been driven by undetected bnAb lineages. However, we did not find strong selection for known bnAb resistance mutations, and in at least one case (RM5695), rapid fitness gains (roughly 2 weeks after infection) substantially preceded bnAb detection (16 weeks). Still, given the limited size of the data set that we studied, it is unclear the extent to which our results will transfer to larger and broader data sets.

Overall thisrpretations could provide valuable insights into the broader significance of these results. is a convincing paper, part of a larger admirable project of accurately inferring complete fitness landscapes.

Reviewer #3 (Public review):

Summary:

Shimagaki et al. investigate the virus-antibody coevolutionary processes that drive the development of broadly neutralizing antibodies (bnAbs). The study's primary goal is to characterize the evolutionary dynamics of HIV-1 within hosts that accompany the emergence of bnAbs, with a particular focus on inferring the landscape of selective pressures shaping viral evolution. To assess the generality of these evolutionary patterns, the study extends its analysis to rhesus macaques (RMs) infected with simianhuman immunodeficiency viruses (SHIV) incorporating HIV-1 Env proteins derived from two human individuals.

Strengths:

A key strength of the study is its rigorous assessment of the similarity in evolutionary trajectories between humans and macaques. This cross-species comparison is particularly compelling, as it quantitatively establishes a shared pattern of viral evolution using a sophisticated inference method. The finding that similar selective pressures operate in both species adds robustness to the study's conclusions and suggests broader biological relevance.

Weaknesses:

However, the study has some limitations. The most significant weakness is that the authors do not sufficiently discuss the implications of the observed similarities. While the identification of shared evolutionary patterns (e.g., Figure 5) is intriguing, the study would benefit from a more explicit discussion of what these findings mean for instance, in the context of HIV vaccine design, immunotherapy, or fundamental viral-host interactions. Even speculative inte