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 with limited coding experience 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.

As with any software package, this one necessarily makes a number of design choices, which may or may not fit the needs of all users. Those who prefer a more automated pipeline with fewer knobs to turn may appreciate AVN in cases where the existing recipes fit their needs, while those who require more customization and flexibility may require a more bespoke (and thus code-intensive) approach.

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 a 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. 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.

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.

In the revised version of the paper, the authors have expanded their case for the design choices made in AVN and remain committed to maintaining the tool. Given the low cost for users in trying new methods and the work the authors have put into further reducing this overhead via documentation, those curious about the package are likely best served by simply downloading it and giving it a try on their own data.

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-and-maximum-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.

Update: The authors now provide an extensive comparison with the Goffinet et al. paper and also consider differences between MMD and EMD. This comparison both adds value to the original paper and provides useful benchmarking for others looking to develop latent space comparison methods.

(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):

This paper introduces the Avian Vocalization Network (AVN), a novel birdsong analysis pipeline using deep learning. By automating vocal annotation tasks, the AVN generates interpretable song features and song similarity scores on novel datasets without retraining. The performance of the network is solid and is comparable to that of human annotators.

The authors have improved the manuscript in several aspects, such as the comparison with the Goffinet work. Overall, the AVN feature set could become a useful tool for evaluating birdsongs. But the authors also chose not to address a certain number of criticisms, and some issues remain poorly addressed, and the work is not reproducible at this stage. With a little effort, these issues could get resolved in my view. I will just pick on four issues that I think can be easily addressed:

(1) Limitation of feature set: They claim that AVN satisfies the criteria (line 60) of "creating a common feature space for the comparison of behavioural phenotypes ..."(line 51), but then on LDA analysis, explained on line 910 they say "excluding amplitude and amplitude modulation features as they were found to vary". Since their feature set is not stable and not truly 'common' to all tasks, this limitation needs addressing in the discussion (that some features seem to vary undesirably, and they need exclusion based on some criteria to be defined).

(2) Missing information on classification training loss: The Authors insist that their triplet loss is not related to classification, and they brush off my request for more information. In their rebuttal, they write: '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.' Perplexingly, however, in the revised paper, authors speak themselves of 'classes', in Line 1004: this allows the model to begin learning an easier task, of separating syllables of different classes by a smaller margin.' So it seems the authors actually agree with me that there is an underlying classification task. I am therefore going to make it a bit more explicit here what I'm asking for, hoping this will better resonate with them.

In line 984 they define their loss function and in lines 994-996 they define 'hard' and 'semi-hard' triplets. Authors then train a system to minimize the loss with a ratio of 75 percent semi-hard triplets and 25 percent hard triplets and a final weighing parameter value alpha=0.7. What I'm asking for is this 'classification' loss their trained model achieves, or in other words, the fraction of triplets that end up producing a loss, either of the 'hard' or 'semi-hard' type. For example, if their model manages to separate all 'possible triplets' by a margin of at least alpha, then the loss would be zero. If the model achieves to separate all triplets except one, then the loss would correspond to the amount by which the separation differences between the anchor and the positive vs negative samples exceeds alpha. So, an important number to provide in the paper is the fraction of triplets that incur a nonzero loss, i.e., the fraction of semi-hard triplets. And another important quantity is the fraction of hard triplets, i.e. the fraction of triplets that would incur a loss if alpha were set to zero, or, in other words, the triplets for which the negative sample is closer to the anchor than the positive sample. By the way, I assume this latter fraction of hard cases will be zero - that their model does not confuse any positive and negative training samples...<br /> Note: the quantification chosen by the authors termed 'contrast index' is interesting, but it is a derived quantity, it is not the quantity authors chose to optimize during training. If authors were to report both the training loss achieved and the 'contrast index', follow-up work could be benchmarked against both these quantities. If for example, a follow-up model achieves smaller loss but worse contrast, then the loss is not a good placeholder measure for optimizing contrast. Alternatively, follow-up work could focus on the contrast index as training objective, obliterating the need for the triplet loss as an intermediate step (I don't buy the authors' argument that such an optimization would be infeasible).

(3) Reproducibility: they explain the way they train the CNN with triplet loss to produce the embeddings, but we're missing both actual scripts on GitHub to train and inference from scratch, and model weights, or even hyper parameters they used. Authors only provide the architecture, and I don't think that's enough to be considered replicable in today's standards. I would suggest they release complete model checkpoint weights for the result they report, the exact data splits, the hyper parameters they used and training and testing code, so that one can very easily verify their claims and apply their methods to other datasets. Note: for example, the code to extract the embeddings is incomplete (the function definition of single_bird_extract_embeddings cannot be found on GitHub) and the model weights they used are missing.

(4) With regards to the age prediction model, the authors should specify that this model is mainly useful for comparisons across studies but less so for precise evaluation of the effects of a treatment within a study. Namely, the effect on song of a treatment is best assessed by comparison to within-subject past song, and by comparison to age-matched control birds (ideally siblings) raised in identical conditions, rather than to invoke a generic model trained on other birds and from different colonies and breeding conditions as authors propose to do. In other words, to introduce a generic model for evaluation of song maturity introduces measurement noise in terms of the additional birds and their variable conditions, which can hinder precise assessment of treatment effects. Note that to state that in past work such maturity models were used is not a good justification, scientifically speaking.

Finally, the authors write that methods for syllable segmentation have not been systematically compared but the whisperseg work they use did such a comparison. So the authors should revise their novelty claim of being the first to compare syllable segmentation methods.

Reviewer #1 (Public review):

Summary:

This paper investigates the control signals that drive event model updating during continuous experience. The authors apply predictions from previously published computational models to fMRI data acquired while participants watched naturalistic video stimuli. They first examine the time course of BOLD pattern changes around human-annotated event boundaries, revealing pattern changes preceding the boundary in anterior temporal and then parietal regions, followed by pattern stabilization across many regions. The authors then analyze time courses around boundaries generated by a model that updates event models based on prediction error and another that uses prediction uncertainty. These analyses reveal overlapping but partially distinct dynamics for each boundary type, suggesting that both signals may contribute to event segmentation processes in the brain.

Strengths:

(1) The question addressed by this paper is of high interest to researchers working on event cognition, perception, and memory. There has been considerable debate about what kinds of signals drive event boundaries, and this paper directly engages with that debate by comparing prediction error and prediction uncertainty as candidate control signals.

(2) The authors use computational models that explain significant variance in human boundary judgments, and they report the variance explained clearly in the paper.

(3) The authors' method of using computational models to generate predictions about when event model updating should occur is a valuable mechanistic alternative to methods like HMM or GSBS, which are data-driven.

(4) The paper utilizes an analysis framework that characterizes how multivariate BOLD pattern dissimilarity evolves before and after boundaries. This approach offers an advance over previous work focused on just the boundary or post-boundary points.

Weaknesses:

(1) While the paper raises the possibility that both prediction error and uncertainty could serve as control signals, it does not offer a strong theoretical rationale for why the brain would benefit from multiple (empirically correlated) signals. What distinct advantages do these signals provide? This may be discussed in the authors' prior modeling work, but is left too implicit in this paper.

(2) Boundaries derived from prediction error and uncertainty are correlated for the naturalistic stimuli. This raises some concerns about how well their distinct contributions to brain activity can be separated. The authors should consider whether they can leverage timepoints where the models make different predictions to make a stronger case for brain regions that are responsive to one vs the other.

(3) The authors refer to a baseline measure of pattern dissimilarity, which their dissimilarity measure of interest is relative to, but it's not clear how this baseline is computed. Since the interpretation of increases or decreases in dissimilarity depends on this reference point, more clarity is needed.

(4) The authors report an average event length of ~20 seconds, and they also look at +20 and -20 seconds around each event boundary. Thus, it's unclear how often pre- and post-boundary timepoints are part of adjacent events. This complicates the interpretations of the reported time courses.

(5) The authors describe a sequence of neural pattern shifts during each type of boundary, but offer little setup of what pattern shifts we might expect or why. They also offer little discussion of what cognitive processes these shifts might reflect. The paper would benefit from a more thorough setup for the neural results and a discussion that comments on how the results inform our understanding of what these brain regions contribute to event models.

Reviewer #2 (Public review):

Summary:

Tan et al. examined how multivoxel patterns shift in time windows surrounding event boundaries caused by both prediction errors and prediction uncertainty. They observed that some regions of the brain show earlier pattern shifts than others, followed by periods of increased stability. The authors combine their recent computational model to estimate event boundaries that are based on prediction error vs. uncertainty and use this to examine the moment-to-moment dynamics of pattern changes. I believe this is a meaningful contribution that will be of interest to memory, attention, and complex cognition research.

Strengths:

The authors have shown exceptional transparency in terms of sharing their data, code, and stimuli, which is beneficial to the field for future examinations and to the reproduction of findings. The manuscript is well written with clear figures. The study starts from a strong theoretical background to understand how the brain represents events and has used a well-curated set of stimuli. Overall, the authors extend the event segmentation theory beyond prediction error to include prediction uncertainty, which is an important theoretical shift that has implications in episodic memory encoding, the use of semantic and schematic knowledge, and attentional processing.

Weaknesses:

The data presented is limited to the cortex, and subcortical contributions would be interesting to explore. Further, the temporal window around event boundaries of 20 seconds is approximately the length of the average event (21.4 seconds), and many of the observed pattern effects occur relatively distal from event boundaries themselves, which makes the link to the theoretical background challenging. Finally, while multivariate pattern shifts were examined at event boundaries related to either prediction error or prediction uncertainty, there was no exploration of univariate activity differences between these two different types of boundaries, which would be valuable.

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.

Reviewer #1 (Public review):

Summary:

Weiss et. al. seek to delineate the mechanisms by which antigen-specific CD8+ T cells outcompete bystanders in the epidermis when active TGF-b is limiting, resulting in selective retention of these cells and more complete differentiation into the TRM phenotype.

Strengths:

They begin by demonstrating that at tissue sites where cognate antigen was expressed, CD8+ T cells adopt a more mature TRM transcriptome than cells at tissue sites where cognate antigen was never expressed. By integrating their scRNA-Seq data on TRM with the much more comprehensive ImmGenT atlas, the authors provide a very useful resource for future studies in the field. Furthermore, they conclusively show that these "local antigen-experienced" TRM have increased proliferative capacity and that TCR avidity during TRM formation positively correlates with their future fitness. Finally, using an elegant experimental strategy, they establish that TCR signaling in CD8+ T cells in the epidermis induces TGFBRIII expression, which likely contributes to endowing them with a competitive advantage over antigen-inexperienced TRM.

Weaknesses:

The main weakness in this paper lies in the authors' reliance on a single experimental model to derive conclusions on the role of local-antigen during the acute phase of the response by comparing T cells in model antigen-vaccinia virus (VV-OVA) exposed skin to T cells in contralateral skin exposed to DNFB 5 days after the VV-OVA exposure. In this setting, antigen-independent factors may contribute to the difference in CD8+ T cell number and phenotype at the two sites. For example, it was recently shown that very early memory precursors (formed 2 days after exposure) are more efficient at seeding the epithelial TRM compartment than those recruited to skin at later times (Silva et al, Sci Immunol, 2023). DNFB-treated skin may therefore recruit precursors with reduced TRM potential. In addition, TRM-skewed circulating memory precursors have been identified (Kok et al, JEM, 2020), and perhaps VV-OVA exposed skin more readily recruits this subset compared to DNFB-exposed skin. Therefore, when the DNFB challenge is performed 5 days after vaccinia virus, the DNFB site may already be at a disadvantage in the recruitment of CD8+ T cells that can efficiently form TRM. In addition, CD8+ T cell-extrinsic mechanisms may be at play, such as differences in myeloid cell recruitment and differentiation or local cytokine and chemokine levels in VV-infected and DNFB-treated skin that could account for differences seen in TRM phenotype and function between these two sites. Although the authors do show that providing exogenous peptide antigen at the DNFB-site rescues their phenotype in relation to the VV-OVA site, the potential antigen-independent factors distinguishing these two sites remain unaddressed. In addition, there is a possibility that peptide treatment of DNFB-treated skin initiates a second phase of priming of new circulatory effectors in the local-draining lymph nodes that are then recruited to form TRM at the DFNB-site, and that the effect does not solely rely on TRM precursors at the DNFB-treated skin site at the time of peptide treatment. These concerns are somewhat alleviated by the fact that in a prior publication (PMID: 33212014), the group has already established a role for local antigen encounter in skin in a setting where they compared contralateral ears infected with VV-OVA and VV expressing an irrelevant antigen.

Secondly, although the authors conclusively demonstrate that TGFBRIII is induced by TCR signals and required for conferring increased fitness to local-antigen experienced CD8+ TRM compared to local antigen-inexperienced cells, this is done in only one experiment, albeit repeated 3 times. The data suggest that antigen encounter during TRM formation induces sustained TGFBRIII expression that persists during the antigen-independent memory phase. It remains however, unclear why only antigen encounter in skin, but not already in the draining lymph nodes, induces sustained TGFBRIII expression. Further characterizing the dynamics of TGFBRIII expression on CD8+ T cells during priming in draining lymph nodes and over the course of TRM formation and persistence may shed more light on this question. Probing the role of this mechanism at other sites of TRM formation would also further strengthen their conclusions and enhance the significance of this finding.

A minor caveat of the study pertains to the use of FTY720 to block T cell egress from lymphoid tissues and thereby prevent a contribution of circulating memory OT-I T cells to the local recall response in skin. Since the half-life of FTY720 is less than a day in mice, its effects wear off rapidly. In their experiments, the authors discontinued treatment at the time of re-challenge, which may have allowed circulating T cells to contribute to the local recall response in skin, limiting the interpretability of the results somewhat. This concern is alleviated by the use of a second method (anti-Thy1.1-depleting antibodies) to eliminate circulating memory cells. For the benefit of readers intending to use this experimental strategy, it should however, be noted that FTY720 needs to be dosed continually (e.g. 3x/week at an appropriate dose) in order to sustain its effect.

Reviewer #2 (Public review):

Summary:

The authors set out to dissect the mechanistic basis of their previously published finding that encountering cutaneous antigen augments the persistence of CD8+ memory T cells that enter skin (TRM) (Hirai et al., 2021, Immunity). Here they use the same murine model to study the fate of CD8+ T cells after antigen-priming in the lymph nodes, (1) those that re-encounter antigen in the skin via vaccinia virus (VV) versus (2) those that do not encounter antigen in skin but rather are recruited via topical dinitrofluorobenzene (DNFB) (so-called "bystander TRM"). The authors' previous publication establishes that this first group of CD8+ TRM has a persistence advantage over bystander TRM under TGFb-limiting conditions. The current paper advances this finding by elucidating the role of TGFBR3 in regulating CD8+ TRM skin persistence upon topical antigen exposure. Key novelty of the work lies in generation and use of the CD8+ T cell-specific TGFBR3 knockout model, which allows them to demonstrate the role of TGFBR3 in fine tuning the degree of CD8+ T cell skin persistence and that TGFBR3 expression is promoted by CD8+ TRM encountering their cognate antigen upon initial skin entry. Future work directly measuring active TGFb in the skin under different conditions would help identify physiologic scenarios which yield active TGFb-limiting conditions, thus establishing physiologic relevance.

Strengths:

Technical strengths of the paper include (1) complementary imaging and flow cytometry analyses, (2) integration of their scRNA-seq data with the existing CD8+ TRM literature via pathway analysis, and (3) use of orthogonal models where possible. Using a vaccina virus (VV) model, with and without ovalbumin (OVA), the authors investigate how topical antigen exposure and TCR strength regulate CD8+ TRM skin recruitment and retention. The authors use both FTY720 and a Thy1.1 depleting antibody to demonstrate that skin CD8+ TRM expand locally following both a primary and secondary recall response to topical OVA application.

A conceptual strength of the paper is the authors' observation that TCR signal strength upon initial TRM tissue entry helps regulate the extent of their local re-expansion on subsequent antigen re-exposure. They achieved this by applying peptides of varying affinity for the OT-I TCR on the DNFB-exposed flank in tandem with initial VV-OVA + DNFB treatment. They then measured TRM expansion after OVA peptide rechallenge, revealing that encountering a higher affinity peptide upon skin entry leads to greater subsequent re-expansion. Additionally, by generating an OT-I Thy1.1+ E8i-creERT2 huNGFR Tgfbr3fl/fl (Tgfbr3∆CD8) mouse, the authors were able to elucidate a unique role for TGFBR3 in CD8+TRM persistence when active TGFb in skin is limited.

Weaknesses:

Overall, the authors' conclusions are well supported although there are some instances where additional controls, experiments, or clarifications would add rigor. The conclusions regarding skin localized TCR signaling leading to increased skin CD8+ TRM proliferation in-situ and increased TGFBR3 expression would be strengthened by assessing skin CD8+ TRM proliferation and TGFBR3 expression in models of high versus low avidity topical OVA-peptide exposure. The authors could further increase the impact of the paper by fully exploring whether TGFBR3 is regulated at the RNA or protein level; analysis of scRNAseq data included in the rebuttal did show an increase in Tgfbr3 RNA transcript levels in VV-treated compared to DNFB-treated back skin.

Quantification of the skin TRM population relies primarily on imaging analysis, which the authors indicate is more sensitive and consistent for quantifying this population. While flow cytometry is used to perform some phenotyping of TRMs, there remain some missed opportunities for more extensive analysis of markers expressed by this population. Finally, quantifying right and left skin draining lymph node CD8+ T cell numbers would clarify the skin specificity and cell trafficking dynamics of the authors' model.

This work heavily utilizes models developed and defined in previously published work (Hirai, T., et al., Competition for Active TGFβ Cytokine Allows for Selective Retention of Antigen-Specific Tissue- Resident Memory T Cells in the Epidermal Niche. Immunity, 2021. 54(1): p. 84-98.e5). Rather than repeating control experiments for this manuscript, the authors reference data included in this prior work. Thus, readers interested in a more in-depth understanding of these tools and concepts would be encouraged to read both papers.

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.

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.

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.

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.

(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.

Reviewer #1 (Public review):

Summary:

Zinn and colleagues investigated the role of proteases 2A and 3C of enterovirus D68 (EVD68), an emerging pathogen associated with outbreaks of acute flaccid myelitis (AFM), a polio-like disease, on the nucleocytoplasmic trafficking in different systems, including human neurons derived from pluripotent cells. They found that 2A specifically cleaved Nup98 and POM121. Using reporter proteins and RNA synthesis and trafficking assays in cells expressing viral proteases, they showed that 2A induces broad loss of the nuclear pore barrier function, but, surprisingly, the RNA export appears to be minimally affected. Since nucleocytoplasmic trafficking defects are known to be associated with neuropatologies, they propose a hypothesis that 2A-dependent cleavage of nucleoporins in motoneurons underlies the development of EVD68-induced AFM. They further show that a 2A-specific inhibitor increases the survival of human neurons differentiated from stem cells upon EVD68 infection.

Strengths:

Use of multiple methods to investigate the effect of 2A and 3C expression on nucleoporin cleavage and nucleocytoplasmic trafficking.

Weaknesses:

Overall, the paper follows multiple others that extensively investigated the cleavage of nucleoporins by enterovirus 2As, so the results are of limited novelty. The hypothesis that infection of motoneurons is the cause of EVD68-induced neurological complications so far is supported by only one autopsy report. Other data suggest that infection of other cell types, such as astrocytes, and/or inflammatory cell infiltration in the CNS, are likely to be responsible for the symptoms. In any case, the claim that EVD68 is specifically neurotoxic because of the 2A-dependent cleavage of nucleoporins in neurons is unfounded, as the virus will be just as "toxic" for other infected cell types.

The paper also requires a more convincing presentation of the data.

Reviewer #2 (Public review):

Summary:

This manuscript investigates the role of EV-D68 proteases 2A and 3C in nuclear pore complex (NPC) dysfunction and their contribution to motor neuron toxicity. The authors demonstrate that both proteases cleave only a limited number of nucleoporins, with 2A^pro showing the strongest impact by inhibiting nuclear import and export of proteins and disrupting NPC permeability without affecting RNA export. Importantly, treatment with the 2A^pro inhibitor telaprevir reduced neuronal cell death in a dose-dependent manner, achieving neuroprotection at concentrations below those required to inhibit viral replication. The study addresses a relevant mechanism underlying EV-D68-induced neuropathology and explores a potential therapeutic intervention.

Strengths:

(1) Provides significant mechanistic insight into how EV-D68 proteases alter NPC function and contribute to neuronal toxicity.

(2) The use of recombinant 2A and 3C proteins allows clear dissection of the specific contribution of each protease.

(3) Demonstrates a therapeutic effect of telaprevir, with neuroprotection independent of viral replication inhibition, adding translational value to the findings.

(4) The topic is highly relevant given the association of EV-D68 with acute flaccid myelitis.

Weaknesses:

(1) Most experiments were performed with recombinant proteases, lacking validation in the context of viral infection, where both proteases act simultaneously.

(2) The conclusion that RNA export is unaffected requires confirmation during actual infection.

(3) The reduction of neurotoxicity by telaprevir does not fully demonstrate that the protective effect is solely mediated through NPC preservation; additional analyses of eIF4G cleavage, nucleoporin integrity, and stress granules are needed.

(4) The study would be strengthened by including another 2A inhibitor (e.g., boceprevir) to confirm the specificity of telaprevir's protective effects.

Reviewer #3 (Public review):

Summary:

The author showed expression of the viral proteases 2Apro and 3Cpro of EV-D68, which cleaved specific components of the nuclear pore complex (Nup98 and POM121 by 2Apro), and 2A but not 3C expression altered nuclear import and export. Similar nucleocytoplasmic transport deficits are observed in EV-D68-infected RD cells and iPSC-derived motor neurons (diMNs). 2A inhibitor telaprevir partially rescued the nucleocytoplasmic transport deficits and suppressed neuronal cell death after infection. While it's clear that 2A can cleave NPC proteins and affect nuclear transport, the link to neurotoxicity after EV-D68 infection is less convincing.

This study opens up a very intriguing hypothesis: that EV-D68 2Apro could be directly responsible for motor neuron cell death, mediated by POM121 and possibly Nup98 cleavage, that ultimately results in paralysis known as acute flaccid myelitis. This hypothesis notably does run counter to other published data showing that human neuronal organoids derived from iPSCs can support productive EV-D68 infection for weeks without cell death and that EV-D68-infected mice can have paralysis prevented by depletion of CD8 T cells, still with EV-D68 infection of the spinal cord. However, even if 2Apro is not ultimately responsible for motor neurons dying in human infections, that does not exclude the possibility that cleavage of nups could still disrupt motor neuron function. Notably, most children with AFM have some amount of motor function return after their acute period of paralysis, but most still have some residual paralysis for years to life. It is possible that 2A pro could mediate the acute onset of weakness, while T cells killing neurons could determine the amount of long-term, residual paralysis.

Strengths:

The characterization of nuclear pore complex components that appear to be targets of both poliovirus and EV-D68 proteases is quite thorough and expansive, so this data set alone will be useful for reference to the field. And the process by which the authors narrowed their focus to EV-D68 2Apro reducing Nup98 and POM121 as consequential to both import and export of nuclear cargo but not RNA was technically impressive, thorough, and convincing. As will be detailed below, when the authors move from studying over-expressed proteases in transformed cell lines to studying actual virus infection in both transformed cell lines and iPSC-derived neurons, some of the data only indirectly support their conclusions; however, the quality of the experiments performed is still high. So even if the claim that 2Apro causes neurotoxicity is circumstantial, the data certainly are intriguing and certainly justify further study of the effects of EV-D68 2Apro on the NPC and how this impacts pathogenesis. This is a convincing start to an intriguing line of inquiry.

Weaknesses:

This study falls a bit shy of actually showing that 2Apro effects are causing motor neuron toxicity because the evidence of this is fairly indirect. At points, the authors do admit these limitations, but at other times, they claim to have shown the link directly. The following are reasons why these claims are only indirectly supported:

(1) Cleavage of Nup98 and POM121 after EV-D68 infection in RD cells and diMNs is never demonstrated.

(2) Telaprevir was able to rescue nucleocytoplasmic transport in RD cells at low concentrations (Figure 4A). It is not shown if this correlates with its antiviral effect in RD cells, or could this correlate with inhibition of 2A cleavage of Nup98 or POM121, which is never measured.

(3) Building off of the prior point, the authors' claim that the neuroprotective effect of telaprevir is independent of its antiviral effect is not well-founded. Figure 4E (neuroprotection) was done with MOI 5, and Figure 4G (virus growth) was MOI 0.5. Telaprevir neuroprotection is not shown at MOI 0.5, nor is the neuroprotective effect correlated with inhibition of 2A cleavage of Nup98 or POM121.

(4) The use of mixed virus isolates only in the diMNs is problematic because different EV-D68 isolates are known to have drastically different effects on pathogenesis in mice. Since all initial data were generated with the MO isolate, adding the additional MD isolate to the diMN experiments actually adds uncertainty to the conclusions. It is not clear if the authors infected different cultures with the different isolates and combined the data or infected all cultures with a mixture of the two isolates. If the former, then the data should be reported separately to see the effect of each individual strain, which would be interesting to EV-D68 virologists. If the latter, then there is no way to know from these data whether one of the two isolates had increased fitness over the other and exerted a dominant effect. If the MD isolate overtook the MO isolate, from which all other data in this manuscript are derived, then we have much less of an idea how much the data from the first three figures supports the final figure.

Reviewer #1 (Public review):

In this manuscript, Rishiq et al. investigate whether natural killer (NK) cells can interact with Fusobacterium nucleatum and identify the molecular mediators involved in this interaction. The authors propose that the bacterial adhesin RadD may bind to the activating NK cell receptor NKp46 (NCR1 in mice), leading to NK cell activation and tumor control. While the topic is of significant interest and the hypothesis intriguing, the manuscript lacks critical experimental evidence, contains several technical concerns, and requires substantial revisions.

Major Concerns:

(1) Lack of Direct Evidence for RadD-NKp46 Interaction

The central claim that RadD interacts with NKp46 is not formally demonstrated. A direct binding assay (e.g., Biacore, ELISA, or pull-down with purified proteins) is essential to support this assertion. The absence of this fundamental experiment weakens the mechanistic conclusions of the study.

(2) Figure 2: Binding Specificity and Bacterial Strains

A CEACAM1-Ig control should be included in all binding experiments to distinguish between specific and non-specific Ig interactions. There is differential Ig binding between strains ATCC 23726 and 10953. The authors should quantify RadD expression in each strain to determine if the difference in binding is due to variation in RadD levels.

(3) Figure 3: Flow Cytometry Inconsistencies and Missing Controls

What do the FITC-negative, Ig-negative events represent? The authors should clarify whether these are background signals, bacterial aggregates, or debris.

Panel B, CEACAM1-Ig binding appears markedly increased compared to WT bacteria. The reason for this enhancement should be discussed-does it reflect upregulation of the bacterial ligand or an artifact of overexpression? Fluorescence compensation should be carefully reviewed for the NKp46/NCR1-Ig binding assays to ensure that the signals are not due to spectral overlap or nonspecific binding. Importantly, binding experiments using the FadI/RadD double knockout strain are missing and should be included. This control is essential.

In Panel E, the basis for calculating fold-change in MFI is unclear. Please indicate the reference condition to which the change is normalized.

(4) Figure 4: Binding Inhibition and Receptor Sensitivity

Panel A lacks representative FACS plots and is currently difficult to interpret. Differences in the sensitivity of human vs. mouse NKp46 to arginine inhibition should be discussed, given species differences in receptor-ligand interactions. What are the inhibition results using F. nucleatum strains deficient in FadI?

In Panel B, CEACAM1-Ig and RadD-deficient bacteria must be included as negative controls for binding specificity upon anti-NKp46 blocking.

(5) Figure 5: Functional NK Activation and Tumor Killing

In Panels B and C, the key control condition (NK cells + anti-NKp46, without bacteria) is missing. This is needed to evaluate if NKp46 recognition is involved in tumor killing. The authors should explicitly test whether pre-incubation of NK cells with bacteria enhances their anti-tumor activity. Alternatively, could bacteria induce stress signals in tumor cells that sensitize them to NK killing? This distinction is critical.

(6) Figure 5D: Mechanism of Peripheral Activation

It is suggested that contact between bacteria and NK cells in the periphery leads to their activation. Can the authors confirm whether this pre-activation leads to enhanced killing of tumor targets, or if bacteria-tumor co-localization is required? The literature indicates that F. nucleatum localizes intracellularly within tumor cells. If so, how is RadD accessible to NKp46 on infiltrating NK cells?

(8) Figure 5E and In Vivo Relevance

Surprisingly, F. nucleatum infection is associated with increased tumor burden. Does this reflect an immunosuppressive effect? Are NK cells inhibited or exhausted in infected mice (TGIT, SIGLEC7...)? If NK cell activation leads to reduced tumor control in the infected context, the role of RadD-induced activation needs further explanation. RadD-deficient bacteria, which do not activate NK cells, result in even poorer tumor control. This paradox needs to be addressed: how can NK activation impair tumor control while its absence also reduces tumor control?

(9) NKp46-Deficient Mice: Inconsistencies

In Ncr1⁻/⁻ mice, infection with WT or RadD-deficient F. nucleatum has no impact on tumor burden. This suggests that NKp46 is dispensable in this context and casts doubt on the physiological relevance of the proposed mechanism. This contradiction should be discussed more thoroughly.

Reviewer #2 (Public review):

Summary:

In the present study, Rishiq et al. investigated whether the RadD protein expressed by Fusobacterium nucleatum subsp. Nucleatum serves as a natural ligand for the NK-activating receptor NKp46, and whether RadD-NKp46 interaction enhances NK cell cytotoxicity against tumor cells. To address this, the authors first performed an association analysis of F. nucleatum abundance and NKp46 expression in head and neck squamous cell carcinoma (HNSC) and colorectal cancer (CRC) using the TCMA and TCGA databases, respectively. While a positive association between NKp46⁺ and F. nucleatum⁺ status with improved overall survival was observed in HNSC patients, no such correlation was found in CRC.

Next, they examined the binding of NKp46-Ig to various F. nucleatum strains. To confirm that this interaction was mediated specifically by RadD, they employed a RadD-deficient mutant strain. Finally, to establish the functional relevance of the RadD-NKp46 interaction in promoting NK cell cytotoxicity and anti-tumor responses, they utilized a syngeneic mouse breast cancer model. In this setup, AT3 cells were orthotopically implanted into the mammary fat pad of C57BL/6 wild-type (WT) or Ncr1-deficient (NCR1⁻/⁻; murine orthologue of human NKp46) mice, followed by intravenous inoculation with either WT F. nucleatum or the ∆RadD mutant strain.

Strengths:

A notable strength of the work is that it identifies a previously unrecognized activating interaction between F. nucleatum RadD and the NK cell receptor NKp46, demonstrating that the same bacterial protein can engage distinct NK cell receptors (activating or inhibitory) to exert context-dependent effects on anti-tumor immunity. This dual-receptor insight adds depth to our understanding of F. nucleatum-immune interactions and highlights the complexity of microbial modulation of the tumor microenvironment.

Weaknesses:

(1) A previous study by this group (PMID: 38952680) demonstrated that RadD of F. nucleatum binds to NK cells via Siglec-7, thereby diminishing their cytotoxic potential. They further proposed that the RadD-Siglec-7 interaction could act as an immune evasion mechanism exploited by tumor cells. In contrast, the present study reports that RadD of F. nucleatum can also bind to the activating receptor NKp46 on NK cells, thereby enhancing their cytotoxic function.

While F. nucleatum-mediated tumor progression has been documented in breast and colon cancers, the current study proposes an NK-activating role for F. nucleatum in HNSC. However, it remains unclear whether tumor-infiltrating NK cells in HNSC exhibit differential expression of NKp46 compared to Siglec-7. Furthermore, heterogeneity within the NK cell compartment, particularly in the relative abundance of NKp46⁺ versus Siglec-7⁺ subsets, may differ substantially among breast, colon, and HNSC tumors. Such differences could have been readily investigated using publicly available single-cell datasets. A deeper understanding of this subset heterogeneity in NK cells would better explain why F. nucleatum is passively associated with a favorable prognosis in HNSC but correlates with poor outcomes in breast and colon cancers.

(2) The in vivo tumor data (Figure 5D-F) appear to contradict the authors' claims. Specifically, Figure 5E suggests that WT mice engrafted with AT3 breast tumors and inoculated with WT F. nucleatum exhibited an even greater tumor burden compared to mice not inoculated with F. nucleatum, indicating a tumor-promoting effect. This finding conflicts with the interpretation presented in both the results and discussion sections.

(3) Although the authors acknowledge that F. nucleatum may have tumor context-specific roles in regulating NK cell responses, it is unclear why they chose a breast cancer model in which F. nucleatum has been reported to promote tumor growth. A more appropriate choice would have been the well-established preclinical oral cancer model, such as the 4-nitroquinoline 1-oxide (4NQO)-induced oral cancer model in C57BL/6 mice, which would more directly relate to HNSC biology.

(4) Since RadD of F. nucleatum can bind to both Siglec-7 and NKp46 on NK cells, exerting opposing functional effects, the expression profiles of both receptors on intratumoral NK cells should be evaluated. This would clarify the balance between activating and inhibitory signals in the tumor microenvironment and provide a more mechanistic explanation for the observed tumor context-dependent outcomes.

Reviewer #3 (Public review):

Summary:

The manuscript by Zhang et al. demonstrates that MORC2 undergoes liquid-liquid phase separation (LLPS) to form nuclear condensates critical for transcriptional repression. Using a combination of in vitro LLPS assays, cellular studies, NMR spectroscopy, and crystallography, the authors show that a dimeric scaffold formed by CC3 drives phase separation, while multivalent interactions between an intrinsically disordered region (IDR) and a newly defined IDR-binding domain (IBD) further promote condensate formation. Notably, LLPS enhances MORC2 ATPase activity in a DNA-dependent manner and contributes to transcriptional regulation, establishing a functional link between phase separation, DNA binding, and transcriptional control. Overall, the manuscript is well-organized and logically structured, offering mechanistic insights into MORC2 function, and most conclusions are supported by the presented data. Nevertheless, some of the claims are not sufficiently supported by the current data and would benefit from additional evidence to strengthen the conclusions.

The following suggestions may help strengthen the manuscript:

Major comments:

(1) The central model proposes that multivalent interactions between the IDR and IBD promote MORC2 LLPS. However, the characterization of these interactions is currently limited. It is recommended that the authors perform more systematic analyses to investigate the contribution of these interactions to LLPS, for example, by in vitro assays assessing how the IDR or IBD individually influence MORC2 phase separation.

(2) The authors mention that DNA binding can promote MORC2 LLPS. It is recommended that they generate a phase diagram to systematically assess how DNA influences phase separation.

(3) The authors use the N39A mutant as a negative control to study the effect of DNA binding on ATP hydrolysis. Given that N39A is defective in DNA binding, it could also be employed to directly test whether DNA binding influences MORC2 phase separation.

(4) Many of the cellular and in vitro LLPS experiments employ EGFP fusions. The authors should evaluate whether the EGFP tag influences MORC2 phase separation behavior.

Reviewer #2 (Public review):

Summary:

The study by Zhang et al. focuses on how phase separation of a chromatin-associated protein MORC2, could regulate gene expression. Their study shows that MORC2 forms dynamic nuclear condensates in cells. In vitro, MORC2 phase separation is driven by dimerization and multivalent interactions involving the C-terminal domain. A key finding is that the intrinsically disordered region (IDR) of MORC2 exhibits strong DNA binding. They report that DNA binding enhances MORC2's phase separation and its ATPase activity, offering new insights into how MORC2 contributes to chromatin organization and gene regulation. The authors try to correlate MORC2's condensate-forming ability with its gene silencing function, but this warrants additional controls and validation. Moreover, they investigate the effect of disease-linked mutations in the N-terminal domain of MORC2 on its ability to form cellular condensates, ATPase activity, and DNA-binding, though the findings appear inconclusive in the manuscript's current form.

Strengths:

The authors determined a 3.1 Å resolution crystal structure of the dimeric coiled-coil 3 (CC3) domain of MORC2, revealing a hydrophobic interface that stabilizes dimer formation. They present extensive evidence that MORC2 undergoes liquid-liquid phase separation (LLPS) across multiple contexts, including in vitro, in cellulo, and in vivo. Through systematic cellular screening, they identified the C-terminal domain of MORC2 as a key driver of condensate formation. Biophysical and biochemical analyses further show that the IDR within the C-terminal domain interacts with the C-terminal end region (IBD) and also exhibits strong DNA-binding capacity, both of which promote MORC2 phase separation. Together, this study emphasizes that interactions mediated by multiple domains-CC3, IDR, and IBD- drives MORC2 phase separation. Finally, the authors quantified the effect of removing the CC3 on the upregulation and downregulation of target gene expression.

Weaknesses:

Though the findings appear compelling in isolation, the study lacks discussion on how its findings compare with previous studies. Particularly in the context of MORC2-DNA binding, there are previous studies extensively exploring MORC2-DNA binding (Tan, W., Park, J., Venugopal, H. et al. Nat Commun 2025), and its effect on ATPase activity (ref 22). The contradictory results in ref 22 about the impact of DNA-binding on ATPase activity, and ATPase activity on transcriptional repression, warrant proper discussion. The authors performed extensive in-cellulo screening for the investigation of domain contribution in MORC2 condensate formation, but the study does not consider/discuss the possibility of some indirect contributions from the complex cellular environment. Alternatively, the domain-specific contributions could be quantified in vitro by comparing phase diagrams for their variants. While the basis of this study is to investigate the mechanism of MORC2 condensate-mediated gene silencing, the findings in Figure 6 appear incomplete because the CC3 deletion not only affects phase separation of MORC2 but also dimerization. Furthermore, their investigation on disease-linked MORC2 mutations appears very preliminary and inconclusive because there are no obvious trends from the data. Overall, the discussion appears weak as it is missing references to previous studies and, most importantly, how their findings compare to others'.

Reviewer #1 (Public review):

Summary:

This work demonstrates that MORC2 undergoes phase separation (PS) in cells to form nuclear condensates, and the authors demonstrate convincingly the interactions responsible for this phase separation. Specifically, the authors make good use of crystallography and NMR to identify multiple protein:protein interactions and use EMSA to confirm protein:DNA interactions. These interactions work together to promote in vitro and in cell phase separation and boost ATPase activity by the catalytic domain of MORC2.

However, the authors have very weak evidence supporting their potentially valuable claim that MORC2 PS is important for the appropriate gene regulatory role of MORC2 in cells. Exploring causal links between PS and function is an important need in the phase separation field, particularly as regards the role of condensates in gene regulation, and is a non-trivial matter. Any study with convincing data on this matter will be very important. For this reason, it is crucial to properly explore the alternative possibility that soluble complexes, existing in the same conditions as phase-separated condensates, are the functional species. It is also critical to keep in mind that, while a specific protein domain may be essential for PS, this does not mean its only important function pertains to PS.

In this study, the authors do not sufficiently explore the role that soluble MORC2 complexes may play alongside MORC2 condensates. Neither do they include enough data to solidly show that domain deletion leads to phenotypes via a loss of phase separation per se, rather than the loss of phase separation being a microscopically visible result, not cause, of an underlying shift in protein function. For these reasons, the authors' conclusions regarding the functional role of MORC2 condensates are based on incomplete data. This also dampens the utility of this work as a whole, since the very nice work detailing the mechanism of MORC2 PS is not paired with strong data showing the importance of this observation.

Strengths:

Static light scattering and crystallography are nicely used to demonstrate the dimerization of MORC2FL and to discover the structure of the CC3 domain dimer, presumably responsible for the dimerization of MORC2FL (Figure 1).

Extensive use of deletion mutants in multiple cell lines is used to identify regions of MORC2 that are important for forming condensates in the nucleus: the IBD, IDR, and CC3 domains are found to be essential for condensate formation, while the CW domain plays an unknown role in condensate morphology (Figure 3). The authors use NMR to further identify that the IBD domain seems to interact with the first third of the centrally located IDR, termed IDRa, but not with the latter two-thirds of the IDR domain (Figure 4). This leads them to propose that phase separation is the product of IDB:IDRa interaction, CC3 dimerization, and an unknown but important role for the CW domain.

Based on the observation that removal of the NLS resulted in diffuse cytoplasmic localization, they hypothesized that DNA may play an important role in MORC2 PS. EMSA was used to demonstrate interaction between DNA and several MORC2 domains: CC1, CC2, IDR, and TCD-CC3-IBD. Further in vitro microscopy with purified MORC2 showed that DNA addition significantly reduces MORC2 saturation concentration (Figure 5).

These assays convincingly demonstrate that MORC2 phase separates in cells, and identify the protein domains and interactions responsible for this phenomenon, with the notable caveat that the role of the CW domain here is left unexplored.

Weaknesses:

Although the authors demonstrated phase separation of MORC2FL, their evidence that this plays a functional role in the cell is incomplete.

Firstly, looking at differentially upregulated genes under MORC2FL overexpression, the authors acknowledge that only 10% are shared with differentially regulated genes identified in other MORC2FL overexpression studies (Figure 6c,d). No explanation is given for why this overlap is so low, making it difficult to trust conclusions from this data set.

Secondly, of the 21 genes shared in this study and in earlier studies, the authors note that the differential regulation is less pronounced when a phase-separation-deficient MORC2 mutant is overexpressed, rather than MORC2FL (Figure 6e). This is taken as evidence that phase separation is important for the proper function of MORC2. However, no consideration is made for the alternative possibility that the mutant, lacking the CC3 dimerization domain, may result in non-functional complexes involving MORC2, eliminating the need for a PS-centric conclusion. To take the overexpression data as solid evidence for a functional role of MORC2 PS, the authors would need to test the alternative, soluble complex hypothesis. Furthermore, there seems to be low replicate consistency for the MORC2 mutant condition (Figure S6a), with replicate 3 being markedly upregulated when compared to replicates 1 and 2.

Thirdly, the authors close by examining the in-cell PS capabilities and ATPase activity of several disease-associated mutants of MORC2 ( Figure 7). However, the relevance of these mutants to the past 6 figures is unclear. None of these mutations is in regions identified as important for PS. Two of the mutations result in a higher percentage of the cell population being condensate-positive, but this is not seemingly connected to ATPase activity, as only one of these two mutants has increased ATPase activity. Figure 7 does not add any support to the main hypotheses in the paper, and nowhere in the paper do the authors investigate the protein regions where the mutations in Figure 7 are found.

Reviewer #1 (Public review):

Summary:

The authors focused on medaka retinal organoids to investigate the mechanism underlying the eye cup morphogenesis. The authors succeeded to induce lens formation in fish retinal organoids using 3D suspension culture with minimal growth factor-containing media containing the Hepes. At day 1, Rx3:H2B-GFP＋ cells appear in the surface region of organoids. At day 1.5, Prox1+cells appear in the interface area between the organoid surface and the core of central cell mass, which develops a spherical-shaped lens later. So, Prox1+ cells covers the surface of the internal lens cell core. At day 2, foxe3:GFP+ cells appear in the Prox1+ area, where early lens fiber marker, LFC, starts to be expressed. In addition, foxe3:GFP+ cells show EdU+ incorporation, indicating that foxe3:GFP+ cells have lens epithelial cell-characters. At day 4, cry:EGFP+ cells differentiate inside the spherical lens core, whose surface area consists of LFC+ and Prox1+ cells. Furthermore, at day 4, the lens core moves towards the surface of retinal organoids to form an eyecup like structure, although this morphogenesis "inside out" mechanism is different from in vivo cellular "outside -in" mechanism of eye cup formation. From these data, the authors conclude that optic cup formation, especially the positioning of the lens, is established in retinal organoids though the different mechanism of in vivo morphogenesis.

Overall, manuscript presentation is nice. However, there are still obscure points to understand background mechanism. My comments are shown below.

Major comments:

(1) At the initial stage of retinal organoid morphogenesis, a spherical lens is centrally positioned inside the retinal organoids, by covering a central lens core by the outer cell sheet of retinal precursor cells. I wonder if the formation of this structure may be understood by differential cell adhesive activity or mechanical tension between lens core cells and retinal cell sheet, just like the previous study done by Heisenberg lab on the spatial patterning of endoderm, mesoderm and ectoderm (Nat. Cell Biol. 10, 429 - 436 (2008)). Lens core cells may be integrated inside retinal cell mass by cell sorting through the direct interaction between retinal cells and lens cells, or between lens cells and the culture media. After day 1, it is also possible to understand that lens core moves towards the surface of retinal organoids, if adhesive/tensile force states of lens core cells may be change by secretion of extracellular matrix. I wonder if the authors measure physical property, adhesive activity and solidness, of retinal precursor cells and lens core cells. If retinal organoids at day 1 are dissociated and cultured again, do they show the same patterning of internal lens core covering by the outer retinal cell sheet?

(2) Optic cup is evaginated from the lateral wall of neuroepithelium of the diencephalon. In zebrafish, cell movement occurs from the pigment epithelium to the neural retina during eye morphogenesis in an FGF-dependent manner. How the medaka optic cup morphogenesis is coordinated? I also wonder if the authors conduct the tracking of cell migration during optic cup morphogenesis to reveal how cell migration and cell division are regulated in lens of the Medaka retinal organoids. It is also interesting to examine how retinal cell movement is coordinated during Medaka retinal organoids.

(3) The authors showed that blockade of FGF signaling affects lens fiber differentiation in day 1-2, whereas lens formation seems to be intact in the presence of FGF receptor inhibitor in day 0-1. I suggest the authors to examine which tissue is a target of FGF signaling in retinal organoids, using markers such as pea3, which is a downstream target of ERK branch of FGF signaling. Since FGF signaling promotes cell proliferation, is the lens core size normal in SU5402-treated organoids from day 0 to day 1?

(4) Fig. 3f and 3g indicate that there is some cell population located between foxe3:GFP+ cells and rx2:H2B-RFP+ cells. What kind of cell-type is occupied in the interface area between foxe3:GFP+ cells and rx2:H2B-RFP+ cells?

(5) Fig. 5e indicates the depth of Rx3 expression at day 1. Is the depth the thickness of Rx3 expressing cell sheet, which covers the central lens core in the organoids? If so, I wonder if total cell number of Rx3 expressing cell sheet may be different in each seeded-cell number, because thickness is the same across each seeded-cell number, but the surface area size may be different depending on underneath the lens core size. Please clarify this point.

(6) Noggin application inhibits lens formation at day 0-1. BMP signaling regulates formation of lens placode and olfactory placode at the early stage of development. It is interesting to examine whether Noggin-treated organoid expands olfactory placode area. Please check forebrain territory markers.

Significance:

Strength: This study is unique. The authors examined eye cup morphogenesis using fish retinal organoids. Eye cup normally consists of the lens, the neural retina, pigment epithelium and optic stalk. However, retinal organoids seem to be simple and consists of two cell types, lens and retina. Interestingly, a similar optic cup-like structure is achieved in both cases; however, underlying mechanism is different. It is interesting to investigate how eye morphogenesis is regulated in retinal organoids, under the unconstrained embryo-free environment.

Limitation: Description is OK, but analysis is not much profound. It is necessary to apply a bit more molecular and cellular level analysis, such as tracking of cell movement and visualization of FGF signaling in organoid tissues.

Advancement: The current study is descriptive. Need some conceptual advance, which impact cell biology field or medical science.

Audience: The target audience of current study are still within ophthalmology and neuroscience community people, maybe translational/clinical rather than basic biology. To beyond specific fields, need to formulate a general principle for cell and developmental biology.

Reviewer #2 (Public review):

Summary:

In this study from Stahl et al., the authors demonstrate that medaka pluripotent embryonic cells can self-organise into eye organoids containing both retina and lens tissues. While these organoids can self-organize into an eye structure that resembles the vertebrate eye, they are built from a fundamentally different morphogenetic process - an "inside-out" mechanism where the lens forms centrally and moves outward, rather than the normal "outside-in" embryonic process. This is a very interesting discovery, both for our understanding of developmental biology and the potential for tissue engineering applications. The study would benefit from some additional experiments and a few clarifications. The authors suggest that the lens cells are the ones that move from the central to a more superficial position. Is this an active movement of lens cells or just the passive consequence of the retina cells acquiring a cup shape? Are the retina cells migrating behind the lens or the lens cells pushing outwards? High-resolution imaging of organoid cup formation, tracking retina cells in combination with membrane labeling of all cells would help elucidate the morphogenetic processes occurring in the organoids. Membrane labeling would also be useful as Prox1 positive lens cells appear elongated in embryos while in the organoids, cell shapes seem less organised, less compact and not elongated (for example as shown in Fig 3f,g).

The organoids could be a useful tool to address how cell fate is linked to cell shape acquisition. In the forming organoids, retinal tissue initially forms on the outside, while non-retinal tissue is located in the centre; this central tissue later expresses lens markers. Do the authors have any insights into why fate acquisition occurs in this pattern? Is there a difference in proliferation rates between the centrally located cells and the external ones? Could it be that highly proliferative cells give rise to neural retina (NR), while lower proliferating cells become lens?

What happens in organoids that do not form lenses? Do these organoids still generate foxe3 positive cells that fail to develop into a proper lens structure? And in the absence of lens formation, does the retina still acquire a cup shape?

The author suggest that lens formation occurs even in the absence of Matrigel. Is the process slower in these conditions? Are the resulting organoids smaller? While there are indeed some LFC expressing cells by day2, these cells are not very well organised and the pattern of expression seems dotty. Moreover, LFC staining seems to localise posterior to the LFC negative, lens-like structure (e.g. Fig.S1 3o'clock).

How do these organoids develop beyond day 4? Do they maintain their structural integrity at later stages?

The role of HEPES in promoting organoid formation is intriguing. Do the authors have any insights into why it is important in this context? Have the authors tried other culture conditions and does culture condition influence the morphogenetic pathways occurring within the organoids?

Significance:

This is a very interesting paper, and it will be important to determine whether this alternative morphogenetic process is specific to medaka or if similar developmental routes can be recapitulated in organoid cultures from other vertebrate species.

Reviewer #3 (Public review):

Summary:

The manuscript by Stahl and colleagues reports an approach to generate ocular organoids composed of retinal and lens structures, derived from Medaka blastula cells. The authors present a comprehensive characterisation of the timeline followed by lens and retinal progenitors, showing these have distinct origins, and that they recapitulate the expression of differentiation markers found in vivo. Despite this molecular recapitulation, morphogenesis is strikingly different, with lens progenitors arising at the centre of the organoid, and subsequently translocating to the outside.

Major Comments:

- The manuscript presents a beautiful set of high-quality images showing expression of lens differentiation markers over time in the organoids. The set of experiments is very robust, with high numbers of organoids analysed and reproducible data. The mechanism by which lens specification is promoted in these organoids is, however, poorly analysed, and the reader does not get a clear understanding of what is different in these experiments, as compared to previous attempts, to support lens differentiation. There is a mention to HEPES supplementation, but no further analysis is provided, and the fact that the process is independent of ECM contradicts, as the authors point out, previous reports. The manuscript would benefit from a more detailed analysis of the mechanisms that lead to lens differentiation in this setting.

- The markers analysed to show onset of lens differentiation in the organoids seem to start being expressed, in vivo, when the lens placode starts invaginating. An analysis of earlier stages is not presented. This would be very informative, allowing to determine whether progenitors differentiate as placode and neuroepithelium first, to subsequently continue differentiating into lens and retina, respectively. Could early placodal and anterior neural plate markers be analysed in the organoids? This would provide a more complete sequence of lens vs retina differentiation in this model.

- The analysis of BMP and Fgf requirement for lens formation and differentiation is suggestive, but the source of these signals is not resolved or mentioned in the manuscript. Are BMP4 and Fgf8 expressed by the organoids? Where are they coming from?

- The fact that the lens becomes specified in the centre of the organoid is striking, but it is for me difficult to visualise how it ends up being extruded from the organoid. Did the authors try to follow this process in movies? I understand that this may be technically challenging, but it would certainly help to understand the process that leads to the final organisation of retinal and lens tissues in the organoid. There is no discussion of why the morphogenetic mechanism is so different from the in vivo situation. The manuscript would benefit from explicitly discussing this.

Significance:

This study describes a reproducible approach to differentiate ocular organoids composed of lens and retinal tissues. The characterisation of lens differentiation in this model is very detailed, and despite the morphogenetic differences, the molecular mechanisms show many similarities to the in vivo situation. The manuscript however does not highlight, in my opinion, why this model may be relevant. Clearly articulating this relevance, particularly in the discussion, will enhance the study and provide more clarity to the readers regarding the significance of the study for the field of organoid research, ocular research and regenerative studies.

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 largely convincing and discussion of the potential explanations for the subtle impacts of individual microexon deletions versus loss-of-function in srrm3 and/or srrm4 is quite comprehensive and thoughtful.

Strengths:

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

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

Reviewer #3 (Public review):

Summary:

Microexons are highly conserved alternative splice variants, the individual functions of which have thus far remained mostly elusive. 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 identifies 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.

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

Reviewer #1 (Public review):

Summary:

This is an interesting and useful review highlighting the complex pathways through which pulmonary colonisation or infection with Mycobacterium tuberculosis (Mtb) may progress to develop symptomatic disease and transmit the pathogen. I found the section on immune correlates associated with individuals who have clearly been exposed to and reacted to Mtb but did not develop latent infections particularly valuable. However, several aspects would benefit from clarification.

Strengths:

The main strengths lie in the arguments presented for a multiplicity of immune pathways to TB disease.

Weaknesses:

The main weaknesses lie in clarity, particularly in the precise meanings of the three figures.

I accept that there is a 'goldilocks zone' that underpins the majority of TB cases we see and predominantly reflects different patterns of immune response, but the analogies used need to be more clearly thought through.

Reviewer #2 (Public review):

Summary:

This is a thought-provoking perspective by Reichmann et al, outlining supportive evidence that Mycobacterium tuberculosis co-evolved with its host Homo Sapiens to both increase susceptibility to infection and reduce rates of fatal disease through decreased virulence. TB is an ancient disease where two modes of virulence are likely to have evolved through different stages of human evolution: one before the Neolithic Demographic Transition, where humans lived in sparse hunter-gatherer communities, which likely selected for prolonged Mtb infection with reduced virulence to allow for transmission across sparse populations. Conversely, following the agricultural and industrial revolutions, Mtb virulence is likely to have evolved to attack a higher number of susceptible individuals. These different disease modalities highlight the central idea that there are different immunological routes to TB disease, which converge on a disease phenotype characterized by high bacterial load and destruction of the extracellular matrix. The writing is very clear and provides a lot of supportive evidence from population studies and the recent clinical trials of novel TB vaccines, like M72 and H56. However, there are areas to support the thesis that have been described only in broad strokes, including the impact of host and Mtb genetic heterogeneity on this selection, and the alternative model that there are likely different TB diseases (as opposed to different routes to the same disease), as described by several groups advancing the concept of heterogeneous TB endotypes. I expand on specific points below.

Strengths:

(1) The idea that Mtb evolved to both increase transmission (and possible commensalism with humans) with low rates of reactivation is intriguing. The heterogeneous TB phenotypes in the collaborative cross model (PMID: 35112666) support this idea, where some genetic backgrounds can tolerate a high bacterial load with minimal pathology, while others show signs of pathogenesis with low bacterial loads. This supports the idea that the underlying host state, driven by a number of factors like genetics and nutrition, is likely to explain whether someone will co-exist with Mtb without pathology, or progress to disease. I particularly enjoyed the discussion of the protective advantages provided by Mtb infection, which may have rewired the human immune system to provide protection against heterologous pathogens- this is supported by recent studies showing that Mtb infection provides moderate protection against SARS-CoV-2 (PMID: 35325013, and 37720210), and may have applied to other viruses that are likely to have played a more significant role in the past in the natural selection of Homo Sapiens.

(2) Modeling from Marcel Behr and colleagues (PMID: 31649096) indeed suggests that there are at least TB clinical phenotypes that likely mirror the two distinct phases of Mtb co-evolution with humans. Most of the TB disease progression occurs rapidly (within 1-2 years of exposure), and the rest are slow cases of reactivation over time. I enjoyed the discussion of the difference between the types of immune hits needed to progress to disease in the two scenarios, where you may need severe immune hits for rapid progression, a phenotype that likely evolved after the Neolithic transition to larger human populations. On the other hand, a series of milder immune events leading to reactivation after a long period of asymptomatic infection likely mirrors slow progression in the hunter-gatherer communities, to allow for prolonged transmission in scarce populations. Perhaps a clearer analysis of these models would be helpful for the reader.

Weaknesses:

(1) The discussion of genetic heterogeneity is limited and only discusses evidence from MSMD studies. Genetics is an important angle to consider in the co-evolution of Mtb and humans. There is a large body of literature on both host and Mtb genetic associations with TB disease. The very fact that host variants in one population do not necessarily cross-validate across populations is evidence in support of population-specific adaptations. Specific Mtb lineages are likely to have co-evolved with distinct human populations. A key reference is missing (PMID: 23995134), which shows that different lineages co-evolved with human migrations. Also, meta-analyses of human GWAS studies to define variants associated with TB are very relevant to the topic of co-evolution (e.g., PMID: 38224499). eQTL studies can also highlight genetic variants associated with regulating key immune genes involved in the response to TB. The authors do mention that Mtb itself is relatively clonal with ~2K SNPs marking Mtb variation, much of which has likely evolved under the selection pressure of modern antibiotics. However, some of this limited universe of variants can still explain co-adaptations between distinct Mtb lineages and different human populations, as shown recently in the co-evolution of lineage 2 with a variant common in Peruvians (PMID: 39613754).

(2) Although the examples of anti-TNF and anti-PD1 treatments are relevant as drivers of TB in limited clinical contexts, the bigger picture is that they highlight major distinct disease endotypes. These restricted examples show that TB can be driven by immune deficiency (as in the case of anti-TNF, HIV, and malnutrition) or hyperactivation (as in the case of anti-PD1 treatment), but there are still certainly many other routes leading to immune suppression or hyperactivation. Considering the idea of hyper-activation as a TB driver, the apparent higher rate of recurrence in the H56 trial referenced in the review is likely due to immune hyperactivation, especially in the context of residual bacteria in the lung. These different TB manifestations (immune suppression vs immune hyperactivation) mirror TB endotypes described by DiNardo et al (PMID: 35169026) from analysis of extensive transcriptomic data, which indicate that it's not merely different routes leading to the same final endpoint of clinical disease, but rather multiple different disease endpoints. A similar scenario is shown in the transcriptomic signatures underlying disease progression in BCG-vaccinated infants, where two distinct clusters mirrored the hyperactivation and immune suppression phenotypes (PMID: 27183822). A discussion of how to think about translating the extensive information from system biology into treatment stratification approaches, or adjunct host-directed therapies, would be helpful.

Reviewer #3 (Public review):

Summary:

This perspective article by Reichmann et al. highlights the importance of moving beyond the search for a single, unified immune mechanism to explain host-Mtb interactions. Drawing from studies in immune profiling, host and bacterial genetics, the authors emphasize inconsistencies in the literature and argue for broader, more integrative models. Overall, the article is thought-provoking and well-articulated, raising a concept that is worth further exploration in the TB field.

Strengths:

Timely and relevant in the context of the rapidly expanding multi-omics datasets that provide unprecedented insights into host-Mtb interactions.

Weaknesses (Minor):

(1) Clarity on the notion of a "unified mechanism". It remains unclear whether prior studies explicitly proposed a single unifying immunological model. While inconsistencies in findings exist, they do not necessarily demonstrate that earlier work was uniformly "single-minded". Moreover, heterogeneity in TB has been recognized previously (PMIDs: 19855401, 28736436), which the authors could acknowledge.

(2) Evolutionary timeline and industrial-era framing. The evolutionary model is outdated. Ancient DNA studies place the Mtb's most recent common ancestor at ~6,000 years BP (PMIDs: 25141181; 25848958). The Industrial Revolution is cited as a driver of TB expansion, but this remains speculative without bacterial-genomics evidence and should be framed as a hypothesis. Additionally, the claim that Mtb genomes have been conserved only since the Industrial Revolution (lines 165-167) is inaccurate; conservation extends back to the MRCA (PMID: 31448322).

(3) Trained immunity and TB infection. The treatment of trained immunity is incomplete. While BCG vaccination is known to induce trained immunity (ref 59), revaccination does not provide sustained protection (ref 8), and importantly, Mtb infection itself can also impart trained immunity (PMID: 33125891). Including these nuances would strengthen the discussion.

Reviewer #1 (Public review):

Summary:

Kang et al. provide the first experimental insights from holographic stimulation of auditory cortex. Using stimulation of functionally-defined ensembles, they test whether overactivation of a specific subpopulation biases simultaneous and subsequent sensory-evoked network activations.

Strengths:

The investigators use a novel technique to investigate the sensory response properties in functionally defined cell assemblies in auditory cortex. These data provide the first evidence of how acutely perturbing specific frequency-tuned neurons impacts the tuning across a broader population. Their revised manuscript appropriately tempers any claims about specific plasticity mechanisms involved.

Weaknesses:

Although the single cell analyses in this manuscript are comprehensive, questions about how holographic stimulation impacts population coding are left to future manuscripts, or perhaps re-analyses of this unique dataset.

Reviewer #2 (Public review):

The goal of HiJee Kang et al. in this study is to explore the interaction between assemblies of neurons with similar pure-tone selectivity in mouse auditory cortex. Using holographic optogenetic stimulation in a small subset of target cells selective for a given pure tone (PTsel), while optically monitoring calcium activity in surrounding non-target cells, they discovered a subtle rebalancing process: co-tuned neurons that are not optogenetically stimulated tend to reduce their activity. The cortical network reacts as if an increased response to PTsel in some tuned assemblies is immediately offset by a reduction in activity in the rest of the PTsel-tuned assemblies, leaving the overall response to PTsel unchanged. The authors show that this rebalancing process affects only the responses of neurons to PTsel, not to other pure tones. They also show that assemblies of neurons that are not selective for PTsel don't participate in the rebalancing process. They conclude that assemblies of neurons with similar pure-tone selectivity must interact in some way to organize this rebalancing process, and they suggest that mechanisms based on homeostatic signaling may play a role.

The authors have successfully controlled for potential artefacts resulting from their optogenetic stimulation. This study is therefore pioneering in the field of the auditory cortex (AC), as it is the first to use single-cell optogenetic stimulation to explore the functional organization of AC circuits in vivo. The conclusions of this paper are very interesting. They raise new questions about the mechanisms that could underlie such a rebalancing process.

(1) This study uses an all-optical approach to excite a restricted group of neurons chosen for their functional characteristics (their frequency tuning), and simultaneously record from the entire network observable in the FOV. As stated by the authors, this approach is applied for the first time to the auditory cortex, which is a tour de force. However, such approach is complex and requires precise controls to be convincing. The authors provide important controls to demonstrate the precise ability of their optogenetic methods. In particular, holographic patterns used to excite 5 cells simultaneously may be associated with out-of-focus laser hot spots. Cells located outside of the FOV could be activated, therefore engaging other cells than the targeted ones in the stimulation. This would be problematic in this study as their tuning may be unrelated to the tuning of the targeted cells. To control for such effect, the authors have decoupled the imaging and the excitation planes, and checked for the absence of out-of-focus unwanted excitation (Suppl Fig1).

(2) In the auditory cortex, assemblies of cells with similar pure-tone selectivity are linked together not only by their ability to respond to the same sound, but also by other factors. This study clearly shows that such assemblies are structured in a way that maintains a stable global response through a rebalancing process. If a group of cells within an assembly increases its response, the rest of the assembly must be inhibited to maintain the total response.<br /> The boundary between assemblies is smooth as the rebalancing process occurring in one assembly seem to affect also the response of the other assembly comprising cells tuned to a the other frequency. This trend is not significant but visible for both tested frenquencies in Fig. 3 and Fig S3.

Reviewer #1 (Public review):

Summary:

The aim of this paper is to develop a simple method to quantify fluctuations in the partitioning of cellular elements. In particular, they propose a flow-cytometry based method coupled with a simple mathematical theory as an alternative to conventional imaging-based approaches.

Strengths:

The approach they develop is simple to understand and its use with flow-cytometry measurements is clearly explained. Understanding how the fluctuations in the cytoplasm partition varies for different kinds of cells is particularly interesting.

Weaknesses:

The theory only considers fluctuations due to cellular division events. Fluctuations in cellular components are largely affected by various intrinsic and extrinsic sources of noise and only under particular conditions does partitioning noise become the dominant source of noise. In the revised version of the manuscript, they argue that in their setup, noise due to production and degradation processes are negligible but noise due to extrinsic sources such as those stemming from cell-cycle length variability may still be important. To investigate the robustness of their modelling approach to such noise, they simulated cells following a sizer-like division strategy, a scenario that maximizes the coupling between fluctuations in cell-division time and partitioning noise. They find that estimates remain within the pre-established experimental error margin.

Reviewer #2 (Public review):

Summary:

The authors present a combined experimental and theoretical workflow to study partitioning noise arising during cell division. Such quantifications usually require time-lapse experiments, which are limited in throughput. To bypass these limitations, the authors propose to use flow-cytometry measurements instead and analyse them using a theoretical model of partitioning noise. The problem considered by the authors is relevant and the idea to use statistical models in combination with flow cytometry to boost statistical power is elegant. The authors demonstrate their approach using experimental flow cytometry measurements and validate their results using time-lapse microscopy. The approach focuses on a particular case, where the dynamics of the labelled component depends predominantly on partitioning, while turnover of components is not taken into account. The description of the methods is significantly clearer than in the previous version of the manuscript. I have only two comments left:

• In eq. (1) the notation has been changed/corrected, but the text immediately after it still refers to the old notation.

• Maybe I don't fully understand the reasoning provided by the authors, but it is still not entirely clear to me why microscopy-based estimates are expected to be larger. Fewer samples will increase the estimation uncertainty, but this can go either way in terms of the inferred variability.

Reviewer #1 (Public review):

Summary:

Planar cell polarity core proteins Frizzled (Fz)/Dishevelled (Dvl) and Van Gogh-like (Vangl)/Prickle (Pk) are localized on opposite sides of the cell and engage in reciprocal repression to modulate cellular polarity within the plane of static epithelium. In this interesting manuscript, the authors explore how the anterior core proteins (Vangl/Pk) inhibit the posterior core protein (Dvl). The authors propose that Pk assists Vangl2 in sequestering both Dvl2 and Ror2, while Ror2 is essential for Dvl to transition from Vangl to Fz in response to non-canonical Wnt signaling. Nevertheless, there are several major and minor points that affect the strength of the author's proposed model (and are listed below).

Strengths:

The strengths of the manuscript are found in the very interesting and new concept along with supportive data for a model of how non-canonical Wnt induces Dvl to transition from Vangl to Fz with an opposing role for PK and Vangl2 to suppress Dvl during convergent extension movements. Ror is key player required for the transition and antagonizes Vangl.

Weaknesses:

The weaknesses are in the clarity and resolution of the data that forms the basis of the model. In addition to general whole embryo morphology that is used as evidence for 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 microscopy would benefit from super resolution microscopy since in many cases the differences in protein localization are not very pronounced. 3) the IP and Western analysis data often shows very subtle differences, and some cases not apparent.

Major points.

(1) Assessment of CE movement

The authors conducted an analysis of the subcellular localization of PCP core proteins, including Vangl2, Pk, Fz, and Dvl, within animal cap explants (ectodermal explants). The authors primarily used the length-to-width ratio (LWR) to evaluate CE movement as a basis for their model. However, LWR can be influenced by multiple factors and is not sufficient to directly and clearly represent CE defects. While the author showed that Prickle knockdown suppresses animal cap elongation mediated by Activin treatment, they did not test their model using standard assays such as animal cap elongation or dorsal marginal zone (DMZ) Keller explants. Furthermore, although various imaging analyses were performed in Wnt11-overexpressing animal caps and DMZ explants, the Wnt11-overexpressing animal caps did not undergo CE movement. Given that this study focuses on the molecular mechanisms of Vangl2 and Ror2 regulation of Dvl2 during CE, the model should be validated in more appropriate tissues, such as DMZ explants.

(2) Overexpression conditions

Another concern is that most analyses were performed with overexpression conditions. PCP core proteins (Vangl2, Pk, Dvl, and Fz receptors) are known to display polarized subcellular localization in both the neural epithelium and DMZ explants (Ref: PCP and Septins govern the polarized organization of the actin cytoskeleton during convergent extension, Current Biology, 2024). However, in this study, overexpressed PCP core proteins failed to show polarized localization. Previous studies, such as those from the Wallingford lab, typically used 10-30 pg of RNA for PCP core proteins, whereas this study injected 100-500 pg, which is likely excessive and may have created artificial conditions that confound the imaging results.

(3) Subtle and insufficient effects

Several of the reported results show quite modest changes in imaging and immunoprecipitation analyses, which are not sufficient to strongly support the proposed molecular model. For example, most Dvl2 remained localized with Fz7 even under Vangl2 and Pk overexpression (Fig. 4). Similarly, Wnt11 overexpression only slightly reduced the association between Vangl2 and Dvl2 (Sup. Fig. 8), and the Ror2-related experiments also produced only subtle effects (Fig. 8, Sup. Fig. 15).

Reviewer #2 (Public review):

The authors use Xenopus embryos to study feedback interactions between the planar cell polarity (PCP) proteins in the context of convergence and extension. They show that binding of the cytoplasmic polarity protein Pk2 to Vangl2 is needed for them to synergistically suppress defects in convergence and extension caused by Dvl overexpression. They then examine protein localizations in animal cap cells, and show that Wnt11-induced accumulation of Fzd7, Ror2 and Dvl into plasma membrane patches is disrupted by the functional Vangl2/Pk complex. This disperses Fzd and causes its endocytosis, while Dvl remains at the plasma membrane. Interestingly, Ror2 and Vangl2 tend to have a broader localization within the membrane patches than Fzd7/Dvl, leading to a model in which Ror2 mediates the transfer of Dvl from Vangl2/Pk to Fzd7 in response to Wnt11.

This work uses a mixture of biochemical approaches, phenotypic assays in Xenopus and imaging. The data is carefully quantitated and the imaging is high quality. This is an interesting paper, showing mechanisms by which Vangl2/Pk can functionally antagonize Fzd/Dvl during planar cell polarity.

Reviewer #1 (Public review):

Summary:

This study investigates plasticity effects in brain function and structure from training in navigation and verbal memory.

The authors used a longitudinal design with a total of 75 participants across two sites. Participants were randomised to one of three conditions: verbal memory training, navigation training, or a video control condition. The results show behavioural effects in relevant tasks following the training interventions. The central claim of the paper is that network-based measures of task-based activation are affected by the training interventions, but structural brain metrics (T2w-derived volume and diffusion-weighted imaging microstructure) are not impacted by any of the training protocols tested.

Strengths:

(1) This is a well-designed study which uses two training conditions, an active control, and randomisation, as appropriate. It is also notable that the authors combined data acquisition across two sites to reach the needed sample size and accounted for it in their statistical analyses quite thoroughly. In addition, I commend the authors on using pre-registration of the analysis to enhance the reproducibility of their work.

(2) Some analyses in the paper are exhaustive and compelling in showcasing the presence of longitudinal behavioural effects, functional activation changes, and lack of hippocampal volume changes. The breadth of analysis on hippocampal volume (including hippocampal subfields) is convincing in supporting the claim regarding a lack of volumetric effect in the hippocampus.

Comments on revisions:

All my comments have been addressed. The evidence regarding lack of a volumetric effect at the whole-brain level now seems more robust. Many details are now clearer, particularly regarding the the volumetric analyses methods and the rationale and timeline of preregistration.

Minor comment:

I appreciate that there are limited possibilities with the available Diffusion-Weighted Imaging data. However, I would recommend the authors remove mentions of "white matter connectivity" in the Abstract and elsewhere, which are misleading if no tractography or voxel-wise analyses are performed.

Reviewer #1 (Public Review):

Summary:

Previous research from the Margoliash laboratory has demonstrated that the intrinsic electrophysiological properties of one class of projection neurons in the song nucleus HVC, HVCX neurons, are similar within birds and differ between birds in a manner that relates to the bird's song. The current study builds on this research by addressing how intrinsic properties may relate to the temporal structure of the bird's song and by developing a computational model for how this can influence sequence propagation of activity within HVC during singing.

First, the authors identify that the duration of the song motif is correlated with the duration of song syllables and particularly the length of harmonic stacks within the song. They next found positive correlations between some of the intrinsic properties, including firing frequency, sag ratio, and rebound excitation area with the duration of the birds' longest harmonic syllable and some other measure of motif duration. These results were extended by examining measures of firing frequency and sag ratio between two groups of birds that were experimentally raised to learn songs that only differed by the addition of a long terminal harmonic stack in one of the groups. Lastly, the authors present an HH-based model elucidating how the timing and magnitude of rebound excitation of HVCX neurons can function to support previously reported physiological network properties of these neurons during singing.

Strengths:

By trying to describe how intrinsic properties (IPs) may relate to the structure of learned behavior and providing a potentially plausible model (see below for more on this) for how differences in IPs can relate to sequence propagation in this neural network, this research is addressing an important and challenging issue. An understanding of how cell types develop IPs and how those IPs relate to the function and output of a network is a fundamental issue. Tackling this in the zebra finch HVC is an elegant approach because it provides a quantifiable and reliable behavior that is explicitly tied to the neurons that the authors are studying. Nonetheless, this is a difficult problem, and kudos to the authors for trying to unravel this.

Correlations between harmonic stack durations and song durations are well-supported and interesting. This provides a new insight that can and will likely be used by other research groups in correlating neuronal activity patterns to song behavior and motif duration. Additionally, correlations between IPs associated with rebound excitation are also well supported in this study.

The HH-model presented is important because it meaningfully relates how high or low rebound excitation can set the integration time window for HVCX neurons. Further, the synaptic connectivity of this model provides at least one plausible way in how this functions to permit the bursting activity of HVCX neurons during singing (and potentially during song playback experiments in sleeping birds). Thus, this model will be useful to the field for understanding how this network activity intersects with 'learned' IPs in an important class of neurons in this circuit.

Comments on revised version:

The authors have adequately addressed my previous concerns.

Reviewer #2 (Public Review):

Intrinsic properties of a neuron refer to the ion channels that a neuron expresses. These ion channels determine how a neuron responds to its inputs. How intrinsic properties link to behavior remains poorly understood. Medina and Margoliash address this question using the zebra finch, a well-studied songbird. Previous studies from their lab and other labs have shown that the intrinsic properties of adult songbird basal-ganglia projecting premotor neurons, are more similar within a bird than across birds. Across birds, this similarity is related to the extent of similarity in the songs; the more similar the song between two birds, the more similar the intrinsic properties between the neurons of these two birds. Finally, the intrinsic properties of these neurons change over the course of development and are sensitive to intact auditory feedback. However, the song features that relate to these intrinsic properties and the function of the within-bird homogeneity of intrinsic properties are unclear.

In this manuscript, the authors address these two questions by examining the intrinsic properties of basal-ganglia projecting premotor neurons in zebra finch brain slices. Specifically, they focus on the Ih current (as this is related to rhythmic activity in many pattern-generating circuits) and correlate the properties of the Ih current with song features. They find that the sag ratio (a measure of the driving force of the Ih current) and the rebound area (a measure of the post-inhibitory depolarisation) are both correlated with the temporal features of the song. First, they show the presence of correlations between the length of the song motif and the length of the longest syllable (most often a harmonic stack syllable). Based on this, they conclude that longer song motifs are composed of longer syllables. Second, they show that HVCX neurons within a bird have more similar sag ratios and rebound areas than across birds. Third, the mean sag ratio and mean rebound areas across birds were correlated with the duration of the longest harmonic stack within the song. These two results suggest that IPs are correlated with the temporal structure of the song. To further test this, the authors used natural and experimental tutoring procedures to have birds that learned two different types of songs that only differed in length; the longer song had an extra harmonic stack at the end. Using these two sets of birds, the authors find larger sag ratios and higher firing frequencies in birds with longer songs. Fifth, they show that the post-inhibitory rebound area allows neurons to respond to excitatory inputs and produce spikes. Neurons with a larger rebound area have a larger time window for responding to excitatory inputs. Based on this, they speculate that HVCX neurons with larger rebound areas integrate over larger time windows. Finally, they make a network model of HVC and show that one specific model could explain sequence-specific bursting of HVCX neurons.

Strengths:

The question being addressed is an interesting question and the authors use appropriate techniques. The authors find a new temporal structure within the song, specifically, they find that longer songs typically have more syllables and longer syllables. As far as I know, this has not been shown earlier. The authors build on existing literature to suggest that IPs of HVCX neurons are correlated with the temporal structure of songs.

Comments on revised version:

I have read through the revised paper and I also feel that my comments have been addressed.

Reviewer #3 (Public Review):

It is rare to find systems in neuroscience where a detailed mechanistic link can be made between the biophysical properties of individual neurons and observable behaviors. In this study, Medina and Margoliash examined how the intrinsic physiological properties of a subclass of neurons in HVC, the main nucleus orchestrating the production of birdsong, might have an effect on the temporal structure of a song. This builds on prior work from this lab demonstrating that intrinsic properties of these neurons are highly consistent within individual animals and more similar between animals with similar songs, by identifying specific acoustic features of the song that covary with intrinsic properties and by setting forth a detailed biophysical network model to explain the relationship.

The main experimental finding is that excitability, hyperpolarization-evoked sag, and rebound depolarization are correlated with song duration and the duration of long harmonic elements. This motivates the hypothesis that rebound depolarization acts as a coincidence detector for the offset of inhibition associated with the previous song element and excitation associated with the start of the next element, with the delay and other characteristics of the window determined primarily by Ih. The idea is then that the temporal sensitivity of coincidence detection, which is common to all HVCx neurons, sets a global tempo that relates to the temporal characteristics of a song. This model is supported by some experimental data showing variation in the temporal integration of rebound spiking and by a Hodgkin-Huxley-based computational model that demonstrates proof of principle, including the emergence of a narrow (~50 ms) post-inhibitory window when excitatory input from other principal neurons can effectively evoke spiking.

Overall, the data are convincing and the model is compelling. The manuscript plays to the strengths of zebra finch song learning and the well-characterized microcircuitry and network dynamics of HVC. Of particular note, the design for the electrophysiology experiments employed both a correlational approach exploiting the natural variation in zebra finch song and a more controlled approach comparing birds that were tutored to produce songs that differed primarily along a single acoustical dimension. The modeling is based on Hodgkin-Huxley ionic conductances that have been pharmacologically validated, and the connections and functional properties of the network are consistent with prior work. This makes for a level of mechanistic detail that will likely be fruitful for future work.

Comments on revised version:

I read through everything and I also feel that my comments have been adequately addressed.

Reviewer #1 (Public review):

Summary:

This paper proposes a new model of perceptual habituation and tests it over two experiments with both infants and adults. The model combines a neural network for visual processing with a Bayesian rational model for attention (i.e., looking time) allocation. This Bayesian framework allows the authors to measure elegantly diverse factors that might drive attention, such as expected information gain, current information gain, and surprise. The model is then fitted to infant and adult participants' data over two experiments, which systematically vary the amount of habituation trials (Experiment 1) and the type of dishabituation stimulus (familiarity, pose, number, identity and animacy). Results show that a model based on (expected) information gain performs better than a model based on surprise. Additionally, while novelty preference is observed when exposure to familiar stimuli is elevated, no familiarity preference is observed when exposure to familiar stimuli is low or intermediate, which is in contrast with past work.

Strengths:

There are three key strengths of this work:

(1) It integrates a neural network model with a Bayesian rational learner, thus bridging the gap between two fields that have often been disconnected. This is rarely seen in the cognitive science field, but the advantages are very clear from this paper: It is possible to have computational models that not only process visual information, but also actively explore the environment based on overarching attentional processes.

(2) By varying parametrically the amount of stimulus exposure and by testing the effects of multiple novel stimulus types, this work allowed the authors to put classical theories of habituation to the test on much finer scales than previous research has done.

(3) The Bayesian model allows the authors to test what specific aspects are different in infants and adults, showing that infants display greater values for the noise parameter.

Weaknesses:

This model pertains visual habituation. What drives infants' (dis)engagement of attention more broadly, for example, when learning the probabilistic structures of the environment around them (e.g., language, action prediction) may follow different principles and dynamics.

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 of 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:

As the authors highlighted in the Discussion section, a limitation of this study is that there is potential sampling bias due to partial sampling of clinical P. aeruginosa isolates. However, the work is still important to showcase the potential benefits of applying genomic sequencing techniques to support infection prevention controls in hospital settings. The limitation on potential sampling bias could inspire further work to explore an optimal clinical isolate sampling framework for genomic analyses to support outbreak investigation. The other limitation that the authors have highlighted in the Discussion session is the lack of epidemiology data to support the interpretation of the inferred patient-to-patient and environment-to-patient transmissions, which emphasised the importance of metadata to complement genomic data analysis in outbreak investigation for future studies.

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.

Comments on revisions:

The paper would be further strengthened from an additional timeline indicating when routine surveillance was introduced and examples of actions or changes guided by the surveillance data that resulted in decrease in ST 621 transmission. This additional information would be useful to support the final statement in the Abstract suggesting "Since initial identification, extensive infection control efforts guided by routine, near real- time surveillance have proved successful at slowing transmission."

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 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 inference of exact transmission routes. Epidemiological data relevant for 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.

Comments on revisions:

Thank you for the careful revision and consideration of my comments.

I am pleased to confirm that all my concerns have been comprehensively addressed.

The changes and additions made have resolved my initial feedback, and I see no need to alter my evaluation.

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.

Comments on revisions:

The authors have addressed my concerns adequately in the revised manuscript.

Reviewer #1 (Public review):

This report addresses a compelling topic. The authors demonstrate that tetanic stimulation of the auditory thalamus induces cortical long-term potentiation (LTP), which can be elicited by either electrical or optical stimulation of the thalamus or by noise bursts. They further show that thalamocortical LTP is abolished when thalamic CCK is knocked down or when cortical CCK receptors are blocked. Notably, in 18-month-old mice, thalamocortical LTP was largely absent but could be restored by cortical application of CCK. The authors conclude that CCK is a critical contributor to thalamocortical plasticity and may enhance this form of plasticity in aged subjects.

The findings presented in this report are valuable and advance our understanding of thalamocortical plasticity.

Reviewer #2 (Public review):

Summary:

This work used multiple approaches to show that CCK is critical for long-term potentiation (LTP) in the auditory thalamocortical pathway. They also showed that the CCK mediation of LTP is age-dependent and supports frequency discrimination. This work is important because is opens up a new avenue of investigation of the roles of neuropeptides in sensory plasticity.

Strengths:

The main strength is the multiple approaches used to comprehensively examine the role of CCK in auditory thalamocortical LTP. Thus, the authors do provide a compelling set of data that CCK mediates thalamocortical LTP in an age-dependent manner.

Weaknesses:

The behavioral assessment is relatively limited, but may be fleshed out in future work.

Reviewer #3 (Public review):

Summary:

Cholecystokinin (CCK) is highly expressed in auditory thalamocortical (MGB) neurons and CCK has been found to shape cortical plasticity dynamics. In order to understand how CCK shapes synaptic plasticity in the auditory thalamocortical pathway, they assessed the role of CCK signaling across multiple mechanisms of LTP induction with the auditory thalamocortical (MGB - layer IV Auditory Cortex) circuit in mice. In these physiology experiments that leverage multiple mechanisms of LTP induction and a rigorous manipulation of CCK and CCK-dependent signaling, they establish an essential role of auditory thalamocortical LTP on the co-release of CCK from auditory thalamic neurons. By carefully assessing the development of this plasticity over time and CCK expression, they go on to identify a window of time that CCK is produced throughout early and middle adulthood in auditory thalamocortical neurons to establish a window for plasticity from 3 weeks to 1.5 years in mice, with limited LTP occurring outside of this window. The authors go on to show that CCK signaling and its effect on LTP in the auditory cortex is also capable of modifying frequency discrimination accuracy in an auditory PPI task. In evaluating the impact of CCK on modulating PPI task performance, it also seems that in mice <1.5 years old CCK-dependent effects on cortical plasticity is almost saturated. While exogenous CCK can modestly improve discrimination of only very similar tones, exogenous focal delivery of CCK in older mice can significantly improve learning in a PPI task to bring their discrimination ability in line with those from young adult mice.

Strengths:

(1) The clarity of the results along with the rigor multi-angled approach provide significant support for the claim that CCK is essential for auditory thalamocortical synaptic LTP. This approach uses a combination of electrical, acoustic, and optogenetic pathway stimulation alongside conditional expression approaches, germline knockout, viral RNA downregulation and pharmacological blockade. Through the combination of these experimental configures the authors demonstrate that high-frequency stimulation-induced LTP is reliant on co-release of CCK from glutamatergic MGB terminals projecting to the auditory cortex.

(2) The careful analysis of the CCK, CCKB receptor, and LTP expression is also a strength that puts the finding into the context of mechanistic causes and potential therapies for age-dependent sensory/auditory processing changes. Similarly, not only do these data identify a fundamental biological mechanism, but they also provide support for the idea that exogenous asynchronous stimulation of the CCKBR is capable of restoring an age-dependent loss in plasticity.

(3) Although experiments to simultaneously relate LTP and behavioral change or identify a causal relationship between LTP and frequency discrimination are not made, there is convincing evidence that CCK signaling in the auditory cortex (known to determine synaptic LTP) is important for auditory processing/frequency discrimination. These experiments are key for establishing the relevance of this mechanism.

Weaknesses:

The following are weaknesses or limitations of the study that may also fall outside of the scope of this work, but which could be addressed in the future.

(1) Given the magnitude of the evoked responses, one expects that pyramidal neurons in layer IV are primarily those that undergo CCK-dependent plasticity, but the degree to which PV-interneurons and pyramidal neurons participate in this process differently is unclear.

(2) While these data support an important role for CCK in synaptic LTP in the auditory thalamocortical pathway, perhaps temporal processing of acoustic stimuli is as or more important than frequency discrimination. Given the enhanced responsivity of the system, it is unclear whether this mechanism would improve or reduce the fidelity of temporal processing in this circuit. Understanding this dynamic may also require consideration of cell type as raised in weakness #1.

(3) In Figure 1, an example of increased spontaneous and evoked firing activity of single neurons after HFS is provided. Yet it is surprising that the group data are analyzed only for the fEPSP. It seems that single neuron data would also be useful at this point to provide insight into how CCK and HFS affect temporal processing and spontaneous activity/excitability.

Reviewer #1 (Public review):

Summary:

This study utilized publicly available Hi-C data to ensemble a comprehensive set of breast cancer cell lines (luminal, Her2+, TNBC) with varying metastatic features to answer whether breast cancer cells would acquire organ-specific feature at the 3D genome level to metastasize to that specific organ. The authors focused on lung metastasis and included several controls as the comparison including normal mammary lines, normal lung epithelial lines, and lung cancer cell lines. Due to the lower resolution at 250KB binning size, the authors only addressed the compartments (A for active compartment and B for inactive compartment) not the other 3D organization of the genome. They started by performing clustering and PCA analysis for the compartment identity and discovered that this panel of cell lines could be well separated based on Her2 and epithelial-mesenchymal features according to the compartment identity. While correlating with the transcriptomic changes, the authors noticed the existence of concordance and divergence between the compartment changes and transcriptomic changes. The authors then switched gear to tackle the core question in metastatic organotropism to the lung. They discovered a set of "lung permissive compartment changes" and concluded that "lung metastatic breast cancer cell lines acquire lung-like genome architecture" and "organotropic 3D genome changes match target organ more than an unrelated organ". To prove the latter point, the authors enlisted additional non-breast cancer cell line (prostate cancer) in the setting of brain metastasis. This is a piece of pure dry computational work without wet bench experiments.

Strengths:

The authors embarked on an ambitious journey to seek for the answer regarding 3D genome changes predisposing metastatic organotropism. The authors succeeded in the assembly of a comprehensive panel of breast cancer cell lines and the aggregation of the 3D genome structure data to conduct a hypothesis driven computation analysis. The authors also achieved in including proper controls representing normal non-cancerous epithelium and the end organ of interest. The authors did well in the citation of relevant references in 3D genome organization and EMT.

Reviewer #2 (Public review):

Summary:

This work addresses an important question of chromosome architecture changes associated with organotopic metastatic traits, showing important trends in genome reorganization. The most important observation is that 3D genome changes consistent with adaptations for new microenvironment, including lung metastatic breast cells exhibiting signatures of the genome architecture typical to a lung cell-like conformation and brain metastatic prostate cancer cells showing compartment shifts toward a brain-like state.

Strengths:

This work presents interesting original results, which will be important for future studies and biomedical implications of epigenetic regulation in norm and pathology.

Reviewer #1 (Public review):

Summary

The manuscript by K.H. Lee et al. presents Spyglass, a new open-source framework for building reproducible pipelines in systems neuroscience. The framework integrates the NWB (Neurodata Without Borders) data standard with the DataJoint relational database system to organize and manage analysis workflows. It enables the construction of complete pipelines, from raw data acquisition to final figures. The authors demonstrate their capabilities through examples, including spike sorting, LFP filtering, and sharp-wave ripple (SWR) detection. Additionally, the framework supports interactive visualizations via integration with Figurl, a platform for sharing neuroscience figures online.

Strengths:

Reproducibility in data analysis remains a significant challenge within the neuroscience community, posing a barrier to scientific progress. While many journals now require authors to share their data and code upon publication, this alone does not ensure that the code will execute properly or reproduce the original results. Recognizing this gap, the authors aim to address the community's need for a robust tool to build reproducible pipelines in systems neuroscience.

Weaknesses:

The issues identified here may serve as a foundation for future development efforts.

(1) User-friendliness:

The primary concern is usability. The manuscript does not clearly define the intended user base within a modern systems neuroscience lab. Improving user experience and lowering the barrier to entry would significantly enhance the framework's potential for broad adoption. The authors provide an online example notebook and a local setup notebook. However, the local setup process is overly complex, with many restrictive steps that could discourage new users. A more streamlined and clearly documented onboarding process is essential. Additionally, the lack of Windows support represents a practical limitation, particularly if the goal is widespread adoption across diverse research environments.

(2) Dependency management and long-term sustainability:

The framework depends on numerous external libraries and tools for data processing. This raises concerns about long-term maintainability, especially given the short lifespan of many academic software projects and the instability often associated with Python's backward compatibility. It would be helpful for the authors to clarify how flexible and modular the pipeline is, and whether it can remain functional if upstream dependencies become deprecated or change substantially.

(3) Extensibility for custom pipelines:

A further limitation is the insufficient documentation regarding the creation of custom pipelines. It is unclear how a user could adapt Spyglass to implement their own analysis workflows, especially if these differ from the provided examples (e.g., spike sorting, LFP analysis that are very specific to the hippocampal field). A clearer explanation or example of how to extend the framework for unrelated or novel analyses would greatly improve its utility and encourage community contributions.

(4) Flexibility vs. Standardization:

The authors may benefit from more explicitly defining the intended role of the framework: is Spyglass designed as a flexible, general-purpose tool for developing custom data analysis pipelines, or is its primary goal to provide a standardized framework for freezing and preserving pipelines post-publication to ensure reproducibility? While both goals are valuable, attempting to fully support both may introduce unnecessary complexity and result in a tool that is not well-suited for either purpose. The manuscript briefly touches on this tradeoff in the introduction, and the latter-pipeline preservation-may be the more natural fit for the package. If so, this intended use should be clearly communicated in the documentation to help users understand its scope and strengths.

Impact:

This work represents a significant milestone in advancing reproducible data analysis pipelines in neuroscience. Beyond reproducibility, the integration of cloud-based execution and shareable, interactive figures has the potential to transform how scientific collaboration and data dissemination are conducted. The authors are at the forefront of this shift, contributing valuable tools that push the field toward more transparent and accessible research practices.

Reviewer #2 (Public review):

Summary:

This valuable paper presents Spyglass, a comprehensive software framework designed to address the critical challenges of reproducibility and data sharing in neuroscience. The authors have developed a robust ecosystem built on community standards such as NWB and DataJoint, and demonstrate its utility by applying it to datasets from two independent labs, successfully validating the framework's ability to reproduce and extend published findings. While the framework offers a powerful blueprint for modern, reproducible research, its immediate broad impact may be tempered by the significant upfront investment required for adoption and its current focus on electrophysiological data. Nevertheless, Spyglass stands as an important and practical contribution, providing a well-documented and thoughtfully designed path toward more transparent and collaborative science.

Strengths:

(1) Principled solution to a foundational challenge:

The work offers a concrete and comprehensive framework for reproducibility in neuroscience, moving beyond abstract principles to provide an implemented, end-to-end ecosystem.

(2) Pragmatic and robust architectural design:

Features such as the "cyclic iteration" motif for spike-sorting curation and the "merge" motif for pipeline consolidation demonstrate deep, practical experience with neurophysiological analysis and address real-world challenges.

(3) Cross-laboratory validation:

The successful replication and extension of published hippocampal decoding findings across independent datasets strongly support the framework's utility and underscore its potential for enabling reproducible science.

(4) Accessibility through documentation and demos:

Extensive tutorials and the availability of a public demo environment lower some of the barriers to adoption.

Weaknesses:

(1) High barrier to adoption:

The requirement to convert all data into NWB, maintain a relational database, and train users in structured workflows is a significant hurdle, particularly for smaller labs.

(2) Limited tool integration:

The current pipelines, while useful, still resemble proof-of-principle demonstrations. Closer integration with established analysis libraries such as Pynapple and others could broaden the toolkit and reduce duplication of effort.

(3) Experimental metadata support:

While NWB provides a solid foundation for storing neurophysiology data streams, it still lacks broad and standardized support for experimental metadata, including descriptions of conditions, subject details, and procedures, as well as links across datasets. This limitation constrains one of Spyglass's key promises: enabling reproducible, cross-laboratory science. The authors should clarify how Spyglass plans to address or mitigate this gap - for example, by adopting or contributing to metadata extensions, providing templates for experimental conditions, or integrating with complementary systems that manage metadata across datasets.

(4) Cross-laboratory interoperability:

While demonstrated across two datasets, the manuscript does not fully address how Spyglass will handle the diversity of metadata standards, acquisition systems, and lab-specific practices that remain major obstacles to reproducibility.

(5) Visualization limitations:

Beyond the export system and Figurl, NWB offers relatively few options for interactive data exploration. The ability to explore data flexibly and discover new phenomena remains limited, which constrains one of the potential strengths of standardized pipelines.

Spyglass is well-positioned to become a community framework for reproducible neuroscience workflows, with the potential to set new standards for transparency and data sharing. With expanded modality coverage, tighter integration of existing community tools, stronger solutions for cross-lab interoperability, and richer visualization capabilities, it could have a transformative impact on the field.

Reviewer #1 (Public review):

Summary:

This paper aims to characterise the physiological and computational underpinnings of the accumulation of intermittent glimpses of sensory evidence.

Strengths:

(1) Elegant combination of electroencephalography and computational modelling.

(2) The authors describe results of two separate experiments, with very similar results, in effect providing an internal replication.

(3) Innovative task design, including different gap durations.

Weaknesses:

(1) The authors introduce the CPP as tracking an intermediary (motor-independent) evidence integration process, and the MBL as motor preparation that maintains a sustained representation of the decision variable. It would help if the authors could more directly and quantitatively assess whether their current data are in line with this. That is, do these signals exhibit key features of evidence accumulation (slope proportional to evidence strength, terminating at a common amplitude that reflects the bound)? Additionally, plotting these signals report locked (to the button press) would help here. What do the results mean for the narrative of this paper?

(2) The novelty of this work lies partly in the aim to characterize how the CPP and MBL interact (page 5, line 3-5). However, this analysis seems to be missing. E.g., at the single-trial level, do relatively strong CPP pulses predict faster/larger MBL? The simulations in Figure 5 are interesting, but more could be done with the measured physiology.

(3) The focus on CPP and MBL is hypothesis-driven but also narrow. Since we know only a little about the physiology during this "gaps" task, have the authors considered computing TFRs from different sensor groupings (perhaps in a supplementary figure?).

(4) The idea of a potential bound crossing during P1 is elegant, albeit a little simplistic. I wonder if the authors could more directly show a physiological signature of this. For example, by focusing on the MBL or occipital alpha split by the LL, LH, HL and HH conditions, and showing this pulse- as well as report-locked. Related, a primacy effect can also be achieved by modelling (i) self-excitation of the current one-dimensional accumulator, or (ii) two competing accumulators that produce winner-take-all dynamics. Is it possible to distinguish between these models, either with formal model comparison or with diagnostic physiological signatures?

(5) The way the authors specify the random effects of the structure of their mixed linear models should be specified in more detail. Now, they write: "Where possible, we included all main effects of interest as random effects to control for interindividual variability." This sounds as if they started with a model with a full random effect structure and dropped random components when the model would not converge. This might not be sufficiently principled, as random components could be dropped in many different orders and would affect the results. Do all main results hold when using classical random effects statistics on subject-wise regression coefficients?

Reviewer #2 (Public review):

Summary:

This manuscript examines decision-making in a context where the information for the decision is not continuous, but separated by a short temporal gap. The authors use a standard motion direction discrimination task over two discrete dot motion pulses (but unlike previous experiments, fill the gaps in evidence with 0-coherence random dot motion of differently coloured dots). Previous studies using this task (Kiani et al., 2013; Tohidi-Moghaddam et al., 2019; Azizi et al., 2021; 2023) or other discrete sample stimuli (Cheadle et al., 2014; Wyart et al., 2015; Golmohamadian et al., 2025) have shown decision-makers to integrate evidence from multiple samples (although with some flexible weighting on each sample). In this experiment, decision-makers tended not to use the second motion pulse for their decision. This allows the separation of neural signatures of momentary decision-evidence samples from the accumulated decision-evidence. In this context, classic electroencephalography signatures of accumulated decision-evidence (central-parietal positivity) are shown to reflect the momentary decision-evidence samples.

Strengths:

The authors present an excellent analysis of the data in support of their findings. In terms of proportion correct, participants show poorer performance than predicted if assuming both evidence samples were integrated perfectly. A regression analysis suggested a weaker weight on the second pulse, and in line with this, the authors show an effect of the order of pulse strength that is reversed compared to previous studies: A stronger second pulse resulted in worse performance than a stronger first pulse (this is in line with the visual condition reported in Golmohamadian et al., 2025). The authors also show smaller changes in electrophysiological signatures of decision-making (central parietal positivity and lateralised motor beta power) in response to the second pulse. The authors describe these findings with a computational model which allows for early decision-commitment, meaning the second pulse is ignored on the majority of trials. The model-predicted electrophysiological components describe the data well. In particular, this analysis of model-predicted electrophysiology is impressive in providing simple and clear predictions for understanding the data.

Weaknesses:

Some readers may be left questioning why behaviour in this experiment is so different from previous experiments, which use almost exactly the same design (Kiani et al., 2013; Tohidi-Moghaddam et al., 2019; Azizi et al., 2021; 2023). The authors suggest this may be due to the staircase procedure used to calibrate the coherence of (single-pulse) dot motion stimuli for individuals at the start of the experiment. But it remains unclear why overall performance in this experiment is so bad. Participants achieved ~85% correct following 400 ms of 33 - 45% coherent motion. In previous work, performance was ~90% correct following 240ms of 12.8% coherent motion. It seems odd that adding the 0% coherent motion in the temporal gaps would impair performance so greatly, given it was clearly colour-coded. There is a lack of detail about the stimulus presentation parameters to understand whether visual processing explains the declined performance, or if there is a more cognitive/motivational explanation.

Reviewer #1 (Public review):

Summary:

This study investigates whether prediction error extends beyond lower-order sensory-motor processes to include higher-order cognitive functions. Evidence is drawn from both task-based and resting-state fMRI, with the addition of resting-state EEG-fMRI to examine power spectral correlates. The results partially support the existence of dissociable connectivity patterns: stronger ventral-dorsal connectivity is associated with high prediction error, while posterior-anterior connectivity is linked to low prediction error. Furthermore, spontaneous switching between these connectivity patterns was observed at rest and correlated with subtle intersubject behavioral variability.

Strengths:

Studying prediction error from the lens of network connectivity provides new insights into predictive coding frameworks. The combination of various independent datasets to tackle the question adds strength, including two well-powered fMRI task datasets, resting-state fMRI interpreted in relation to behavioral measures, as well as EEG-fMRI.

Weaknesses:

Major:

(1) Lack of multiple comparisons correction for edge-wise contrast:

The analysis of connectivity differences across three levels of prediction error was conducted separately for approximately 22,000 edges (derived from 210 regions), yet no correction for multiple comparisons appears to have been applied. Then, modularity was applied to the top 5% of these edges. I do not believe that this approach is viable without correction. It does not help that a completely separate approach using SVMs was FDR-corrected for 210 regions.

(2) Lack of spatial information in EEG:

The EEG data were not source-localized, and no connectivity analysis was performed. Instead, power fluctuations were averaged across a predefined set of electrodes based on a single prior study (reference 27), as well as across a broader set of electrodes. While the study correlates these EEG power fluctuations with fMRI network connectivity over time, such temporal correlations do not establish that the EEG oscillations originate from the corresponding network regions. For instance, the observed fronto-central theta power increases could plausibly originate from the dorsal anterior cingulate cortex (dACC), as consistently reported in the literature, rather than from a distributed network. The spatially agnostic nature of the EEG-fMRI correlation approach used here does not support interpretations tied to specific dorsal-ventral or anterior-posterior networks. Nonetheless, such interpretations are made throughout the manuscript, which overextends the conclusions that can be drawn from the data.

Reviewer #2 (Public review):

Summary:

This paper investigates putative networks associated with prediction errors in task-based and resting-state fMRI. It attempts to test the idea that prediction errors minimisation includes abstract cognitive functions, referred to as the global prediction error hypothesis, by establishing a parallel between networks found in task-based fMRI where prediction errors are elicited in a controlled manner and those networks that emerge during "resting state".

Strengths:

Clearly, a lot of work and data went into this paper, including 2 task-based fMRI experiments and the resting state data for the same participants, as well as a third EEG-fMRI dataset. Overall, well written with a couple of exceptions on clarity, as per below, and the methodology appears overall sound, with a couple of exceptions listed below that require further justification. It does a good job of acknowledging its own weakness.

Weaknesses:

(1) The paper does a good job of acknowledging its greatest weakness, the fact that it relies heavily on reverse inference, but cannot quite resolve it. As the authors put it, "finding the same networks during a prediction error task and during rest does not mean that the networks' engagement during rest reflects prediction error processing". Again, the authors acknowledge the speculative nature of their claims in the discussion, but given that this is the key claim and essence of the paper, it is hard to see how the evidence is compelling to support that claim.

(2) Given how uncontrolled cognition is during "resting-state" experiments, the parallel made with prediction errors elicited during a task designed for that effect is a little difficult to make. How often are people really surprised when their brains are "at rest", likely replaying a previously experienced event or planning future actions under their control? It seems to be more likely a very low prediction error scenario, if at all surprising.

(3) The quantitative comparison between networks under task and rest was done on a small subset of the ROIs rather than on the full network - why? Noting how small the correlation between task and rest is (r=0.021) and that's only for part of the networks, the evidence is a little tenuous. Running the analysis for the full networks could strengthen the argument.

(4) Looking at the results in Figure 2C, the four-quadrant description of the networks labelled for low and high PE appears a little simplistic. The authors state that this four-quadrant description omits some ROIs as motivated by prior knowledge. This would benefit from a more comprehensive justification. Which ROIs are excluded, and what is the evidence for exclusion?

(5) The EEG-fMRI analysis claiming 3-6Hz fluctuations for PE is hard to reconcile with the fact that fMRI captures activity that is a lot slower, while some PEs are as fast as 150 ms. The discussion acknowledges this but doesn't seem to resolve it - would benefit from a more comprehensive argument.

Reviewer #3 (Public review):

Bogdan et al. present an intriguing and timely investigation into the intrinsic dynamics of prediction error (PE)-related brain states. The manuscript is grounded in an intuitive and compelling theoretical idea: that the brain alternates between high and low PE states even at rest, potentially reflecting an intrinsic drive toward predictive minimization. The authors employ a creative analytic framework combining different prediction tasks and imaging modalities. They shared open code, which will be valuable for future work.

However, the current manuscript would benefit from further clarification and empirical grounding, especially with regard to its theoretical framing (that PE-like state fluctuations are intrinsic and help us minimize PE), interpretation of results, and broader functional significance. Below, I outline a few major comments and suggestions that I think would strengthen the contribution.

(1) Consistency in Theoretical Framing

The title, abstract, and introduction suggest inconsistent theoretical goals of the study.

The title suggests that the goal is to test whether there are intrinsic fluctuations in high and low PE states at rest. The abstract and introduction suggest that the goal is to test whether the brain intrinsically minimizes PE and whether this minimization recruits global brain networks. My comments here are that a) these are fundamentally different claims, and b) both are challenging to falsify. For one, task-like recurrence of PE states during resting might reflect the wiring and geometry of the functional organization of the brain emerging from neurobiological constraints or developmental processes (e.g., experience), but showing that mirroring exists because of the need to minimize PE requires establishing a robust relationship with behavior or showing a causal effect (e.g., that interrupting intrinsic PE state fluctuations affects prediction).

The global PE hypothesis-"PE minimization is a principle that broadly coordinates brain functions of all sorts, including abstract cognitive functions"-is more suitable for discussion rather than the main claim in the abstract, introduction, and all throughout the paper.

Given the above, I recommend that the authors clarify and align their core theoretical goals across the title, abstract, introduction, and results. If the focus is on identifying fluctuations that resemble task-defined PE states at rest, the language should reflect that more narrowly, and save broader claims about global PE minimization for the discussion. This hypothesis also needs to be contextualized within prior work. I'd like to see if there is similar evidence in the literature using animal models.

(2) Interpretation of PE-Related Fluctuations at Rest and Its Functional Relevance

It would strengthen the paper to clarify what is meant by "intrinsic" state fluctuations. Intrinsic might mean task-independent, trait-like, or spontaneously generated. Which do the authors mean here? Is the key prediction that these fluctuations will persist in the absence of a prediction task?

Regardless of the intrinsic argument, I find it challenging to interpret the results as evidence of PE fluctuations at rest. What the authors show directly is that the degree to which a subset of regions within a PE network discriminates high vs. low PE during task correlates with the magnitude of separation between high and low PE states during rest. While this is an interesting relationship, it does not establish that the resting-state brain spontaneously alternates between high and low PE states, nor that it does so in a functionally meaningful way that is related to behavior. How can we rule out brain dynamics of other processes, such as arousal, that also rise and fall with PE? I understand the authors' intention to address the reverse inference concern by testing whether "a participant's unique connectivity response to PE in the reward-processing task should match their specific patterns of resting-state fluctuation". However, I'm not fully convinced that this analysis establishes the functional role of the identified modules to PE because of the following:

Theoretically, relating the activities of the identified modules directly to behavior would demonstrate a stronger functional role.

a) Across participants: Do individuals who exhibit stronger or more distinct PE-related fluctuations at rest also perform better on tasks that require prediction or inference? This could be assessed using the HCP prediction task, though if individual variability is limited (e.g., due to ceiling effects), I would suggest exploring a dataset with a prediction task that has greater behavioral variance.

Or even more broadly, does this variability in resting state PE state fluctuations predict general cognitive abilities like WM and attention (which the HCP dataset also provides)? I appreciate the inclusion of the win-loss control, and I can see the intention to address specificity. This would test whether PE state fluctuations reflect something about general cognition, but also above and beyond these attentional or WM processes that we know are fluctuating.

b) Within participants: Do momentary increases in PE-network expression during tasks relate to better or faster prediction? In other words, is there evidence that stronger expression of PE-related states is associated with better behavioral outcomes?

(3) Apriori Hypothesis for EEG Frequency Analysis

It's unclear how to interpret the finding that fMRI fluctuations in the defined modules correlate with frontal Delta/Theta power, specifically in the 3-6 Hz range. However, in the EEG literature, this frequency band is most commonly associated with low arousal, drowsiness, and mind wandering in resting, awake adults, not uniquely with prediction error processing. An a priori hypothesis is lacking here: what specific frequency band would we expect to track spontaneous PE signals at rest, and why? Without this, it is difficult to separate a PE-based interpretation from more general arousal or vigilance fluctuations.

(4) Significance Assessment

The significance of the correlation above and all other correlation analyses should be assessed through a permutation test rather than a single parametric t-test against zero. There are a few reasons: a) EEG and fMRI time series are autocorrelated, violating the independence assumption of parametric tests;<br /> b) Standard t-tests can underestimate the true null distribution's variance, because EEG-fMRI correlations often involve shared slow drifts or noise sources, which can yield spurious correlations and inflating false positives unless tested against an appropriate null.

Building a null distribution that preserves the slow drifts, for example, would help us understand how likely it is for the two time series to be correlated when the slow drifts are still present, and how much better the current correlation is, compared to this more conservative null. You can perform this by phase randomizing one of the two time courses N times (e.g., N=1000), which maintains the autocorrelation structure while breaking any true co-occurrence in patterns between the two time series, and compute a non-parametric p-value. I suggest using this approach in all correlation analyses between two time series.

(5) Analysis choices

If I'm understanding correctly, the algorithm used to identify modules does so by assigning nodes to communities, but it does not itself restrict what edges can be formed from these modules. This makes me wonder whether the decision to focus only on connections between adjacent modules, rather than considering the full connectivity, was an analytic choice by the authors. If so, could you clarify the rationale? In particular, what justifies assuming that the gradient of PE states should be captured by edges formed only between nearby modules (as shown in Figure 2E and Figure 4), rather than by the full connectivity matrix? If this restriction is instead a by-product of the algorithm, please explain why this outcome is appropriate for detecting a global signature of PE states in both task and rest.

When assessing the correspondence across task-fMRI and rs-fMRI in section 2.2.2, why was the pattern during task calculated from selecting a pair of bilateral ROIs (resulting in a group of eight ROIs), and the resting state pattern calculated from posterior-anterior/ventral-dorsal fluctuation modules? Doesn't it make more sense to align the two measures? For example, calculating task effects on these same modules during task and rest?

Reviewer #1 (Public review):

Summary:

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

Strengths:

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

Weaknesses:

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

Reviewer #2 (Public review):

Summary:

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

Strengths:

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

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

Weaknesses:

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

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

The methodology of changing the dynamics through moisture content appears to be slightly underdeveloped, e.g., adding water involves a droplet, and removing water is accomplished by heating (which presumably could cause other effects). Could the dynamics not be controlled more directly by varying the humidity? At the same time, the authors also mention that temperature itself plays a role in shaping the behaviour. What is the mechanism for this? Is it just through evaporation? Since the frequency increases with temperature, could it just be that activity increases with temperature?

Reviewer #3 (Public review):

Summary:

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

Strengths:

The experimental discovery of unidirectionally propagating waves on bacterial biofilms is highly intriguing and represents a significant contribution to both microbiology and active-matter physics. The detailed observations of wave pattern transitions (spiral to target to planar) and their response to various environmental perturbations (water, temperature, PEG) provide valuable empirical data. The identification of type IV pili as the driving force offers a concrete biological mechanism. The observed correlation between frequency gradients and wave direction is a compelling finding with potential for broader implications in understanding biological pattern formation. This work has the potential to stimulate further research in the collective behavior of living systems and the physical principles underlying biological organization.

Weaknesses:

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

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

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

Reviewer #1 (Public review):

Summary:

This paper describes a behavioral platform "BuzzWatch" and its application in long-term behavioral monitoring. The study tested the system with different mosquito species and Aedes aegypti colonies and monitored behavioral response to blood feeding, change in photoperiod, and host-cue application at different times of the day.

Strengths:

BuzzWatch is a novel, custom-built behavioral system that can be used to monitor time-of-day-specific and long-term mosquito behaviors. The authors provide detailed documentation of the construction of the assay and custom flight tracking algorithm on a dedicated website, making them accessible to other researchers in the field. The authors performed a wide range of experiments using the BuzzWatch system and discovered differences in midday activity level among Aedes aegypti colonies, and reversible change in the daily activity profile post-blood-feeding.

Weaknesses:

The authors report the population metric "fraction flying" as their main readout of the daily activity profile. It is worth explaining why conventional metrics like travel distance/activity level are not reported. Alternatively, these metrics could be shown, considering the development and implementation of a flight trajectory tracking pipeline in this paper.

The authors defined the sugar-feeding index using occupancy on the sugar feeder. However, the correlation between landing on the sugar feeder and active sugar feeding is not mentioned or tested in this paper. Is sugar feeding always observed when mosquitoes land on the sugar feeder? Do they leave the sugar feeding surface once sugar feeding is complete? One can imagine that texture preference and prolonged occupancy may lead to inaccurate reporting of sugar feeding. While occupancy on the sugar feeder is an informative behavioral readout, its link with sugar feeding activity (consumption) needs to be evaluated. Otherwise, the authors should discuss the caveats that this method presents explicitly to avoid overinterpretation of their results.

Throughout the manuscript, the authors mentioned existing mosquito activity monitoring systems and their drawbacks. However, many of these statements are misleading and sometimes incorrect. The authors claim that beam-break monitors are "limited to counting active versus inactive states". Though these systems provide indirect readouts that may underreport activity, the number of beam-breaks in a time interval is correlated with activity level, as is commonly used and reported in Drosophila and mosquitoes and a number of reports in mosquitoes an updated LAM system with larger behavioral arenas and multiple infrared beams. The authors also mentioned the newer, camera-based alternatives to beam-break monitors, but again referred to these systems as "only detecting activity when a moving insect blocks a light beam"; however, these systems actually use video tracking (e.g., Araujo et al. 2020).

The fold change in behavior presented in Figure 4D is rather confusing. Under the two different photoperiods, it is not clear how an hourly comparison is justified (i.e., comparing the light-on activity in the 20L4D condition with scotophase activity in the 12L12D condition). The same point applies to Figure 4H.

The behavioral changes after changing photoperiod (Figure 4) require a control group (12L12D throughout) to account for age-related effects. This is controlled for the experiment in Figure 3 but not for Figure 4.

Reviewer #2 (Public review):

Summary:

This study establishes a platform for studying mosquito flight activity over the course of several weeks and demonstrates key applications of such a paradigm: the comparison of daily activity profiles across different Aedes aegypti populations and the quantification of responses to physiological and environmental perturbations.

Strengths:

(1) Overall, the authors succeed in setting up a low-cost, scalable tracking system that stably records mosquito flight activity for several weeks and uses it to demonstrate compelling use cases.

(2) The text is organized well, is easy to read, and is understandable for a broad audience.

(3) Instructions for constructing housing and for performing tracking with a dedicated GUI are available on an accompanying website, with open-source (and well-organized) code.

(4) A complementary pair of methods (one testing for activity signals at specific times of the day, and the other capturing broader daily patterns) is used effectively.

Weaknesses:

(1) In the interval-based GLMM results, since each time interval is tested independently, p-values should be corrected for multiple hypotheses (for instance, through controlling the false discovery rate).

(2) The accompanying GUI application needs some modifications to fully work out of the box on a sample video.

Reviewer #3 (Public review):

Summary:

The authors in this paper introduce BuzzWatch, an open-source, low-cost (200-300 Euros) platform for long-term monitoring of mosquito flight and behavior. They use a Raspberry Pi with a Noirv2 Camera set up under laboratory conditions to observe 3 different species of mosquitoes. The system captures a variety of multimodal data, like flight activity, sugar feeding, and host-seeking responses, with the help of external modules like CO2 and fructose-soaked cottons. They also release a GUI in addition to automated tracking and behaviour analysis, which doesn't run on Pi but rather on a personal laptop.

Four main use cases are demonstrated:

(1) Characterizing diel rhythms in various Aedes aegypti populations.

(2) Differentiating behaviors of native African vs. invasive human-adapted subspecies.

(3) Assessing physiological (blood-feeding) and environmental (light regime) perturbations.

(4) Testing time-of-day variation in responses to host-associated cues like CO₂ and heat.

Description (Strengths):

(1) The authors introduce a low-cost, scalable system that uses flight tracking in 2D as an alternative to 3D multi-camera systems.

(2) Due to the low pixel quality required by the system, they can record for weeks at a time, capturing long temporal and behavioral activities.

(3) They also integrate external modules such as lights, CO2, and heat as a way to measure responses to a variety of stimuli.

(4) They also introduce a wiki as a guide for building replication and a help in using the GUI module.

(5) They implement both GLMM hourly and PCA of behavior data.

Limitations - Major Comments:

(1) Most experiments are only done with single replicates per colony. If the setup is claimed to be cheap and replicable, there should be clearer replicates across experiments.

(2) No external validation for the flight tracking algorithm using manual annotation or comparison with field data. The authors focus early on biological proof of principle, but the validity of the tracking algorithm is not presented. How accurate is the algorithm at classifying behaviours (e.g., vs human ground truth)? How reliable is tracking?

(3) Why develop a custom GUI instead of using established packages such as rethomics (https://rethomics.github.io/) that are already available for behavioral analysis?

(4) Why use RGB light strips when perceptual white light for humans is not relevant for mosquitoes? The choice of lighting should be based on the mosquito's visual perception. - https://pmc.ncbi.nlm.nih.gov/articles/PMC12077400/ .

(5) Why use GLMMs instead of GAMs (with explicit periodic components)? With GLMMs, you do not account for temporal structure, which is highly relevant and autocorrelated in behavioral time series data.

(6) What is the proportion of mosquitoes that stay alive throughout the experiments? How do you address dead animals in tracking? No data are available on whether all mosquitoes made it through the monitoring period. No survival data is mentioned in the paper, and in the wiki, it is not clear how it is used or how it affects the analyses - https://theomaire.github.io/buzzwatch/analyze.html#diff-cond .

(7 )The sugar feeding behavior is not manually validated.

(8) Figure 4d is difficult to understand - how did you align time? Why is ZT4 aligning with ZT0? Should you "warp" the time series to compare them (e.g., from dawn to dusk)?

(9) No video recordings are made available for demonstration or validation purposes.

Appraisal

(1) The core conclusions---that BuzzWatch can capture multiscale mosquito behavioral rhythms and quantify the effect of genetic, environmental, and physiological variation - show promise but require stronger validation.

(2) Statistical approaches (GLMM, PCA) are chosen but may not be optimal for temporal data with autocorrelation.

(3) The host-seeking module shows a differential response, which is a potentially valuable feature.

Reviewer #1 (Public review):

Summary:

The temporal regulation of neuronal specification and its molecular mechanisms are important problems in developmental neurobiology. This study focuses on Kenyon cells (KCs), which form the mushroom body in Drosophila melanogaster, in order to address this issue. Building on previous findings, the authors examine the role of the transcription factor Eip93F in the development of late-born KCs. The authors revealed that Eip93F controls the activity of flies at night through the expression of the calcium channel Ca-α1T. Thus, the study clarifies the molecular machinery that controls temporal neuronal specification and animal behavior.

Strengths:

The convincing results are based on state-of-the-art molecular genetics, imaging, and behavioral analysis.

Weaknesses:

Temporal mechanisms of neuronal specification are found in many nervous systems. However, the relationship between the temporal mechanisms identified in this study and those in other systems remains unclear.

Reviewer #2 (Public review):

Summary:

Understanding the mechanisms of neural specification is a central question in neurobiology. In Drosophila, the mushroom body (MB), which is the associative learning region in the brain, consists of three major cell types: γ, α'/β', and α/β kenyon cells. These classes can be further subdivided into seven subtypes, together comprising ~2000 KCs per hemi-brain. Remarkably, all of these neurons are derived from just four neuroblasts in each hemisphere. Therefore, a lot of endeavors are put into understanding how the neuron is specified in the fly MB.

Over the past decade, studies have revealed that MB neuroblasts employ a temporal patterning mechanism, producing distinct neuronal types at different developmental stages. Temporal identity is conveyed through transcription factor expression in KCs. High levels of Chinmo, a BTB-zinc finger transcription factor, promote γ-cell fate (Zhu et al., Cell, 2006). Reduced Chinmo levels trigger expression of mamo, a zinc finger transcription factor that specifies α'/β' identity (Liu et al., eLife, 2019). However, the specification of α/β neurons remains poorly understood. Some evidence suggests that microRNAs regulate the transition from α'/β' to α/β fate (Wu et al., Dev Cell, 2012; Kucherenko et al., EMBO J, 2012). One hypothesis even proposes that α/β represents a "default" state of MB neurons, which could explain the difficulty in identifying dedicated regulators.

The study by Chung et al. challenges this hypothesis. By leveraging previously published RNA-seq datasets (Shih et al., G3, 2019), they systematically screened BAC transgenic lines to selectively label MB subtypes. Using these tools, they analyzed the consequences of manipulating E93 expression and found that E93 is required for α/β specification. Furthermore, loss of E93 impairs MB-dependent behaviors, highlighting its functional importance.

Strengths:

The authors conducted a thorough analysis of E93 manipulation phenotypes using LexA tools generated from the Janelia Farm and Bloomington collections. They demonstrated that E93 knockdown reduces expression of Ca-α1T, a calcium channel gene identified as an α/β marker. Supporting this conclusion, one LexA line driven by a DNA fragment near EcR (R44E04) showed consistent results. Conversely, overexpression of E93 in γ and α'/β' Kenyon cells led to downregulation of their respective subtype markers.

Another notable strength is the authors' effort to dissect the genetic epistasis between E93 and previously known regulators. Through MARCM and reporter analyses, they showed that Chinmo and Mamo suppress E93, while E93 itself suppresses Mamo. This work establishes a compelling molecular model for the regulatory network underlying MB cell-type specification.

Weaknesses:

The interpretation of E93's role in neuronal specification requires caution. Typically, two criteria are used to establish whether a gene directs neuronal identity:<br /> (1) gene manipulation shifts the neuronal transcriptome from one subtype to another, and<br /> (2) gene manipulation alters axonal projection patterns.

The results presented here only partially satisfy the first criterion. Although markers are affected, it remains possible that the reporter lines and subtype markers used are direct transcriptional targets of E93 in α/β neurons, rather than reflecting broader fate changes. Future studies using single-cell transcriptomics would provide a more comprehensive assessment of neuronal identity following E93 perturbation.

With respect to the second criterion, the evidence is also incomplete. While reporter patterns were altered, the overall morphology of the α/β lobes appeared largely intact after E93 knockdown. Overexpression of E93 in γ neurons produced a small subset of cells with α/β-like projections, but this effect warrants deeper characterization before firm conclusions can be drawn. While the results might be an intrinsic nature of KC types in flies, the interpretation of the reader of the data should be more careful, and the authors should also mention this in their main text.

Reviewer #1 (Public review):

This study provides a thorough analysis of Nup107's role in Drosophila metamorphosis, demonstrating that its depletion leads to developmental arrest at the third larval instar stage due to disruptions in ecdysone biosynthesis and EcR signaling. Importantly, the authors establish a novel connection between Nup107 and Torso receptor expression, linking it to the hormonal cascade regulating pupariation.

The authors have addressed most of the concerns raised in my initial review, particularly those outlined in the public comments. However, I note that they have not directly responded to several specific points raised in the "Author Recommendations" section. That said, a key mechanistic question remains unresolved and deserves further experimental or at least conceptual clarification.

It has been previously shown that Nup107 regulates the nuclear translocation of dpERK (Kim et al., 2010). This observation may provide a mechanistic explanation for the developmental arrest observed upon Nup107 depletion in the prothoracic gland (PG). Given that PG growth and ecdysone biosynthesis are driven by several receptor tyrosine kinases, it is plausible that loss of Nup107 impairs dpERK nuclear translocation, thereby functionally shutting down RTK-dependent transcriptional responses, including those activating Halloween gene expression. This model is supported by the finding that activated Ras (rasV12) can rescue the arrest, likely by generating sufficiently high levels of dpERK such that some fraction enters the nucleus despite impaired translocation. This hypothesis may explain the discrepancy between the complete developmental arrest observed upon Nup107 depletion and the developmental delay seen in Torso mutants.

Similarly, the rescue by Torso, but not EGFR, may reflect differences in receptor activation thresholds. It has been proposed that Torso overexpression might leads to ligand-independent dimerization and constitutive activity, whereas EGFR overexpression may remain ligand-dependent and thus insufficient under compromised dpERK transport conditions. A critical experiment to validate this model would be to examine dpERK localization in PG cells upon Nup107 depletion. This would help establish whether defective nuclear import of dpERK underlies the observed developmental arrest. Even if technically challenging, the authors should at least discuss this hypothesis explicitly in the revised manuscript.

In addition, it has been shown that TGFβ/Activin signaling regulates Torso expression in the prothoracic gland (PG). Therefore, it is plausible that this pathway may also be affected by impaired nuclear translocation of downstream effectors due to Nup107 depletion. This raises the possibility that Nup107 plays a broad regulatory role, impacting multiple signaling cascades-such as RTK and TGFβ/Activin pathways-by controlling the nuclear import of their key effectors.

Reviewer #2 (Public review):

Summary:

The manuscript by Kawadkar et al investigates the role of Nup107 in developmental progression via regulation of ecdysone signaling. The authors identify an interesting phenotype of Nup107 whole body RNAi depletion in Drosophila development - developmental arrest at the late larval stage. Nup107-depleted larvae exhibit mis-localization of the Ecdysone receptor (EcR) from the nucleus to the cytoplasm and reduced expression of EcR taret genes in salivary glands, indicative of compromised ecdysone signaling. This mis-localization of EcR in salivary glands was phenocopied when Nup107 was depleted only in the prothoracic gland (PG), suggesting that it is not nuclear transport of EcR but presence of ecdysone (normally secreted from PG) that is affected. Consistently, whole body levels of ecdysone were shown to be reduced in Nup107 KD, particularly at the late third instar stage when a spike in ecdysone normally occurs. Importantly, the authors could rescue the developmental arrest and EcR mis-localization phenotypes of Nup107 KD by adding exogenous ecdysone, supporting the notion that Nup107 depletion disrupts biosynthesis of ecdysone, which arrests normal development. Additionally, they found that rescue of Nup107 KD phenotype can also be achieved by over-expression of the receptor tyrosine kinase torso, which is thought to be the upstream regulator of ecdysone synthesis in the PG. Transcript levels of torso are also shown to be downregulated in the Nup107KD, as are transcript levels of multiple ecdysone biosynthesis genes. Together, these experiments reveal a new role of Nup107 or nuclear pore levels in hormone-driven developmental progression, likely via regulation of levels of torso and torso-stimulated ecdysone biosynthesis.

Strengths:

The developmental phenotypes of an NPC component presented in the manuscript are striking and novel, and the data appears to be of high quality. The rescue experiments are particularly significant, providing strong evidence that Nup107 functions upstream of torso and ecdysone levels in regulation of developmental timing and progression.

Weaknesses:

The underlying mechanism is however not clear, and any insight into how Nup107 may regulate these pathways would greatly strengthen the manuscript. Some suggestions to address this are detailed below.

Major questions:

(1) Determining how specific this phenotype is to Nup107 vs. to reduced NPC levels overall would give some mechanistic insight. Does knocking down other components of the Nup107 subcomplex (the Y-complex) lead to similar phenotypes? Given the published gene regulatory function of Nup107, do other gene regulatory Nups such as Nup98 or Nup153 produce these phenotypes?

(2) In a related issue, does this level of Nup107 KD produce lower NPC levels? It is expected to, but actual quantification of nuclear pores in Nup107-depleted tissues should be added. These and above experiments would help address a key mechanistic question - is this phenotype the result of lower numbers of nuclear pores or specifically of Nup107?

(3) Additional experiments on how Nup107 regulates torso would provide further insight. Does Nup107 regulate transcription of torso or perhaps its mRNA export? Looking at nascent levels of the torso transcript and the localization of its mRNA can help answer this question. Or alternatively, does Nup107 physically bind torso?

(4) The depletion level of Nup107 RNAi specifically in the salivary gland vs. the prothoracic gland should be compared by RT-qPCR or western blotting.

(5) The UAS-torso rescue experiment should also include the control of an additional UAS construct - so Nup107; UAS-control vs Nup107; UAS-torso should be compared in the context of rescue to make sure the Gal4 driver is functioning at similar levels in the rescue experiment.

Minor:

(6) Figures and figure legends can stand to be more explicit and detailed, respectively.

Comments on revisions:

The revised manuscript addresses several outstanding issues, most importantly the question of whether the developmental delay phenotype of Nup107 is exhibited by other Nups.

I recommend that the authors include the data they provide in the rebuttal letter on Nup153 KD not showing the delay phenotype (Figure R1) into the actual manuscript. It's an important mechanistic question raised by multiple reviewers, and would strengthen the authors' conclusions. Ideally, knock downs of other Nups of the Nup107 complex should be investigated, especially given that all those RNAi lines are publicly available.

Figure 6B should also specify whether the torso transcript being measured is mRNA or nascent, as it would help understand whether it's transcription or mRNA stability that is affected by Nup107 KD.

Reviewer #3 (Public review):

These findings suggest that Nup107 is involved in regulating ecdysone signaling during developmental transitions, with depletion of Nup107 disrupting hormone-regulated processes. Moreover, the rescue experiments hint that Nup107 might directly influence EcR signaling and ecdysone biosynthesis, though the precise molecular mechanism remains unclear.

Overall, the manuscript presents compelling data supporting Nup107's role in regulating developmental transitions.

Comments on revisions:

RNAi specificity: The authors now provide a more thorough discussion of off-target effects and justify their reliance on the Nup107KK RNAi line. The explanation regarding the predicted off-target for the GD line and their choice to use the KK line with a known insertion site is appropriate and adequately addresses the original concern.

NPC component specificity: The authors clarify that among the Nup107 complex members tested, only Nup107 knockdown induced developmental arrest. Their inclusion of Nup153 as a control helps to support the specificity of the phenotype, although expanding this analysis beyond a single additional Nup would further strengthen the claim.

Mechanistic clarity: The authors now distinguish between Nup107's upstream role in regulating torso and ecdysone biosynthetic genes versus direct control of EcR translocation. The clarification that EcR nuclear localization is 20E-dependent but Nup107-independent improves interpretive clarity.

The molecular mechanism linking Nup107 to torso regulation remains somewhat speculative. A deeper exploration of whether Nup107 influences transcriptional regulation through chromatin association (as the authors suggest) would strengthen the mechanistic narrative.

Conclusion:

Overall, the authors have addressed the major concerns raised in the initial review, and the revised manuscript presents a more coherent and compelling case for Nup107 as a regulator of developmental timing via the ecdysone signaling axis. While some mechanistic questions remain, the core findings are supported by the data, and the work provides novel insights into NPC function in development.

Reviewer #1 (Public review):

This well-conceived manuscript investigates the mechanisms that shape the chromatin landscape following fertilization, using the Drosophila embryo as a model system. Importantly, the authors revisit conflicting data using new approaches and analysis to show that the silent H3K27me3 mark deposited by PRC2 is established de novo in the embryo in coordination with the slowing of the nuclear division cycle and activation of zygotic transcription. Unexpectedly, they demonstrate that the transcription factor GAF is not required for the deposition of this mark, but that the well-studied pioneer factor Zelda, which is required for widespread gene expression, is required for H3K27me3 deposition at a subset of regions. The experiments are rigorously performed, and interpretations are clear. Strengths of this manuscript include the rigor of the experimental design, careful analysis, and well-supported conclusions. Some additional citations, analysis, and broadening of the Discussion section to include additional models and data would further strengthen this manuscript.

Reviewer #2 (Public review):

Epigenetic silencing of target genes by the Polycomb pathway is central to maintenance of cell fates during development and depends on repressive chromatin states involving Polycomb complexes and histone modifications. However, the mechanisms by which these chromatin states are built at the earliest stages of development are unclear. Here, Gonzaga-Saavedra and colleagues use the premier experimental system for studying Polycomb gene regulation, Drosophila development, to investigate when Polycomb domains emerge and how they are assembled. Using a combination of CRISPR gene editing, imaging, and genomic profiling, they determine that while H3K27me3 is initially present in the first nuclear cycles, it quickly dissipates and does not re-emerge until mid-nuclear cycle 14, during the major wave of zygotic genome activation (ZGA). This finding helps resolve current discrepancies in the field, informs potential mechanisms of transgenerational inheritance, and indicates that repressive Polycomb domains are built de novo on target genes in embryogenesis. The authors then set out to examine how Polycomb domains are built. Through live imaging and immunofluorescence, they determine that the histone H3K27 methyltransferase, E(z), is present in nuclei at high levels throughout cleavage and blastoderm stages. By contrast, they determine that several Polycomb proteins that bind PREs (cis elements that demarcate Polycomb targets in the genome) are absent from early cleavage nuclei and progressively increase following nuclear cycle 10. These findings suggest that the absence of H3K27me3 in early embryos may be due to failure to assemble functional Polycomb complexes at target genes. Lastly, the authors test the requirement of two transcription factors with important roles in ZGA, GAF, and ZLD. Despite binding to many PREs and regulating chromatin accessibility in early embryos, they find that GAF is largely dispensable for the emergence of H3K27me3 domains. On the other hand, they find that the pioneer factor ZLD is required for proper H3K27me3 emergence; in its absence, some Polycomb domains accumulate greater levels of H3K27me3, whereas other Polycomb domains accumulate less H3K27me3.

Strengths:

The strengths of this study are manifold. It studies an important topic with broad interest to the chromatin and epigenetics fields. It is well-written with detailed method descriptions. In addition, the experimental design and rigor of execution are exceptional despite working with very small amounts of biological material. Example strengths include that the Polycomb proteins studied were tagged with the same epitope, permitting direct quantitative comparisons in imaging and in genomics experiments. Microscopy studies are quantified and performed both via live imaging and via immunofluorescence. The microscopy studies reinforce and extend conclusions made via ChIP. Sophisticated loss-of-function analyses allow for direct mechanistic tests of Polycomb domain emergence.

Weaknesses:

Overall, the study is quite strong already, but it can be further strengthened in several ways. First, several conclusions should be refined based on the data presented. Second, the extent to which ZLD is important for initiating Polycomb domain formation should be made clearer. Third, additional genomic profiling experiments are needed to provide insight into models explaining why H3K27me3 is absent prior to NC14.

Reviewer #3 (Public review):

Gonzaga-Saavedra et al report an analysis on genomic binding of Polycomb group proteins, and of H2Aub1 and H3K27me3 domain formation in the early Drosophila embryo. Using carefully staged embryos during the nuclear cycles (NC) leading up to the cellular blastoderm stage, the authors provide compelling evidence that H3K27me3 domains at PcG target genes are only established during NC14 and do not exist in NC13. In contrast, H2Aub1 domains already start to appear during NC13. The authors show that E(z), the catalytic subunit of the H3K27 histone methyltransferase PRC2, is readily detected in interphase nuclei during the rapid nuclear divisions in pre-blastoderm embryos. In contrast, the DNA-binding proteins Pho, Cg, and GAF that are known (Pho) or have been postulated (Cg, GAF) to anchor PRC2 and PRC1 to Polycomb Response Elements (PREs) in Polycomb target genes only start to show nuclear localization from NC10 onwards with gradually increasing nuclear concentrations, reaching a maximum during NC14. These data strongly corroborate the simple, straightforward view that targeting of PRC2 and PRC1 to PREs by sequence-specific DNA-binding proteins is a prerequisite for the formation of H3K27me3 and H2Aub1 domains at Polycomb target genes.

The authors then explore the potential role of GAF/Trl in this process. They find that in embryos depleted of GAF/Trl, H3K27me3 domain formation is largely unperturbed.

The authors also depleted the pioneer factor Zelda (Zld) and found that removal of Zld results in a more complex outcome. Zelda appears to counteract the accumulation of H3K27me3 at the Polycomb targets eve and zen, but also appears to be required for effective H3K27me3 domain formation at Polycomb targets such as amos or atonal.

This is a very thorough study that reports data of superior technical quality that are highly relevant for the field. The study by Gonzaga-Saavedra et al extends and strengthens previous work from the labs of Eisen (Li et al, eLife 2014) and Zeitlinger (Chen et al, eLife 2013) to convincingly demonstrate that Polycomb domain formation in the early embryo occurs during ZGA but that such domains do not exist prior to ZGA. This should now finally put to rest earlier claims by the Iovino lab (Zenk et al, Science 2017) that H3K27me3 domains present in the zygote nucleus would be propagated and partially maintained during the rapid nuclear cleavage cycles and serve as seeds for H3K27me3 domain formation during ZGA.

The experiments analyzing H3K27me3 domain formation in embryos depleted of GAF/Trl or Zelda will be of great interest to the field.

Reviewer #2 (Public review):

In their study, Avraham-Davidi et al. combined scRNA-seq and spatial mapping studies to profile two preclinical mouse models of colorectal cancer: Apcfl/fl VilincreERT2 (AV) and Apcfl/fl LSL-KrasG12D Trp53fl/fl Rosa26LSL-tdTomato/+ VillinCreERT2 (AKPV). In the first part of the manuscript, the authors describe the analysis of the normal colon and dysplastic lesions induced in these models following tamoxifen injection. They highlight broad variations in immune and stromal cell composition within dysplastic lesions, emphasizing the infiltration of monocytes and granulocytes, the accumulation of IL-17+gdT cells and the presence of a distinct group of endothelial cells. A major focus the study is the remodeling of the epithelial compartment, where most significant changes are observed. Using no-negative matrix factorization, the authors identify molecular programs of epithelial cell functions, emphasizing stemness, Wnt signaling, angiogenesis and inflammation as majors features associated with dysplastic cells. They conclude that findings from scRNA-seq analyses in mouse models are transposable to human CRC. In the second part of the manuscript, the authors aim to provide the spatial contexture for their scRNA-seq findings using Slide-seq and TACCO. They demonstrate that dysplastic lesions are disorganized and contain tumor-specific regions, which contextualize the spatial proximity between specific cell states and gene programs. Finally, they claim that these spatial organizations are conserved in human tumors and associate region-based gene signatures with patient outcome in public datasets. Overall, the data were collected and analyzed using solid and validated methodology to offer a useful resource to the community.

Main comments:

(1) Clarity. The manuscript would benefit from a substantial reorganization to improve clarity and accessibility for a broad readership. The text could be shortened and the number of figure panels reduced to emphasize the novel contributions of this work while minimizing extensive discussions on general and expected findings, such as tissue disorganization in dysplastic lesions. Additionally, figure panels are not consistently introduced in the correct order, and some are not discussed at all (e.g., Fig. S1D; Fig. 3C is introduced before Fig. 3A; several panels in Fig. 4 are not discussed). The annotation of scRNA-seq cell states is insufficiently explained, with no corresponding information about associated genes provided in the figures or tables. Multiple annotations are used to describe cell groups (e.g., TKN01 = γδ T and CD8 T, TKN05 = γδT_IL17+), but these are not jointly accessible in the figures, making the manuscript challenging to follow. It is also not clear what is the respective value of the two mouse models and timepoints of tissue collection in the analysis.

(2) Novelty. While the study is of interest, it does not present major findings that significantly advance the field or motivate new directions and hypotheses. Many conclusions related to tissue composition and patient outcomes, such as the epithelial programs of Wnt signaling, angiogenesis, and stem cells, are well-established and not particularly novel. Greater exploration of the scRNA-seq data beyond cell type composition could enhance the novelty of the findings. For instance, several tumor microenvironment clusters uniquely detected in dysplastic lesions (e.g., Mono2, Mono3, Gran01, Gran02) are identified, but no further investigation is conducted to understand their biological programs, such as applying nNMF as was done for epithelial cells. Additional efforts to explore precise tissue localization and cellular interactions within tissue niches would provide deeper insights and go beyond the limited analyses currently displayed in the manuscript.

(3) Validation. Several statements made by the authors are insufficiently supported by the data presented in the manuscript and should be nuanced in the absence of proper validation. For example: 1.) RNA velocity analyses: The conclusions drawn from these analyses are speculative and need further support. 2.) Annotations of epithelial clusters as dysplastic: These annotations could have been validated through morphological analyses and staining on FFPE slides. 3.) Conservation of mouse epithelial programs in human tumors: The data in Figure S5B does not convincingly demonstrate enrichment of stem cell program 16 in human samples. This should be more explicitly stated in the text, given the emphasis placed on this program by the authors. 4.) Figure S6E: Cluster Epi06 is significantly overrepresented in spatial data compared to scRNA-seq, yet the authors claim that cell type composition is largely recapitulated without further discussion, which reduces confidence in other conclusions drawn.<br /> Furthermore, stronger validation of key dysplastic regions (regions 6, 8, and 11) in mouse and human tissues using antibody-based imaging with markers identified in the analyses would have considerably strengthened the study. Such validation would better contextualize the distribution, composition, and relative abundance of these regions within human tumors, increasing the significance of the findings and aiding the generation of new pathophysiological hypotheses.

Comments on revisions:

The authors have improved the clarity of the manuscript and responded adequately to all my initial comments.<br /> I don't have any other comments. Congratulations to the authors on this work.

Reviewer #1 (Public review):

Summary:

Taber et al report the biochemical characterization of 7 mutations in PHD2 that induce erythrocytosis. Their goal is to provide a mechanism for how these mutations cause the disease. PHD2 hydroxylates HIF1a in the presence of oxygen at two distinct proline residues (P564 and P402) in the "oxygen degradation domain" (ODD). This leads to the ubiquitylation of HIF1a by the VHL E3 ligase and its subsequent degradation. Multiple mutations have been reported in the EGLN1 gene (coding for PHD2), which are associated with pseudohypoxic diseases that include erythrocytosis. Furthermore, 3 mutations in PHD2 also cause pheochromocytoma and paraganglioma (PPGL), a neuroendocrine tumour. These mutations likely cause elevated levels of HIF1a, but their mechanisms are unclear. Here, the authors analyze mutations from 152 case reports and map them on the crystal structure. They then focus on 7 mutations, which they clone in a plasmid and transfect into PHD2-KO to monitor HIF1a transcriptional activity via a luciferase assay. All mutants show impaired activation. Some mutants also impaired stability in pulse chase turnover assays (except A228S, P317R, and F366L). In vitro purified PHD2 mutants display a minor loss in thermal stability and some propensity to aggregate. Using MST technology, they show that P317R is strongly impaired in binding to HIF1a and HIF2a, whereas other mutants are only slightly affected. Using NMR, they show that the PHD2 P317R mutation greatly reduces hydroxylation of P402 (HIF1a NODD), as well as P562 (HIF1a CODD), but to a lesser extent. Finally, BLI shows that the P317R mutation reduces affinity for CODD by 3-fold, but not NODD.

Strengths:

(1) Simple, easy-to-follow manuscript. Generally well-written.

(2) Disease-relevant mutations are studied in PHD2 that provide insights into its mechanism of action.

(3) Good, well-researched background section.

Weaknesses:

(1) Poor use of existing structural data on the complexes of PHD2 with HIF1a peptides and various metals and substrates. A quick survey of the impact of these mutations (as well as analysis by Chowdhury et al, 2016) on the structure and interactions between PHD2 peptides of HIF1a shows that the P317R mutation interferes with peptide binding. By contrast, F366L will affect the hydrophobic core, and A228S is on the surface, and it's not obvious how it would interfere with the stability of the protein.

(2) To determine aggregation and monodispersity of the PHD2 mutants using size-exclusion chromatography (SEC), equal quantities of the protein must be loaded on the column. This is not what was done. As an aside, the colors used for the SEC are very similar and nearly indistinguishable.

(3) The interpretation of some mutants remains incomplete. For A228S, what is the explanation for its reduced activity? It is not substantially less stable than WT and does not seem to affect peptide hydroxylation.

(4) The interpretation of the NMR prolyl hydroxylation is tainted by the high concentrations used here. First of all, there is a likely a typo in the method section; the final concentration of ODD is likely 0.18 mM, and not 0.18 uM (PNAS paper by the same group in 2024 reports using a final concentration of 230 uM). Here, I will assume the concentration is 180 uM. Flashman et al (JBC 2008) showed that the affinity of the NODD site (P402; around 10 uM) for PHD2 is 10-fold weaker than CODD (P564, around 1 uM). This likely explains the much faster kinetics of hydroxylation towards the latter. Now, using the MST data, let's say the P317R mutation reduces the affinity by 40-fold; the affinity becomes 400 uM for NODD (above the protein concentration) and 40 uM for CODD (below the protein concentration). Thus, CODD would still be hydroxylated by the P317R mutant, but not NODD.

(5) The discrepancy between the MST and BLI results does not make sense, especially regarding the P317R mutant. Based on the crystal structures of PHD2 in complex with the ODD peptides, the P317R mutation should have a major impact on the affinity, which is what is reported by MST. This suggests that the MST is more likely to be valid than BLI, and the latter is subject to some kind of artefact. Furthermore, the BLI results are inconsistent with previous results showing that PHD2 has a 10-fold lower affinity for NODD compared to CODD.

(6) Overall, the study provides some insights into mutants inducing erythrocytosis, but the impact is limited. Most insights are provided on the P317R mutant, but this mutant had already been characterized by Chowdhury et al (2016). Some mutants affect the stability of the protein in cells, but then no mechanism is provided for A228S or F366L, which have stabilities similar to WT, yet have impaired HIF1a activation.

Comments on revision:

While the authors have addressed my concerns regarding the SEC experiments and the structural interpretation of most mutants, I remain unconvinced by their interpretation of the P317R mutant and affinity measurements. The BLI and MST data remain inconsistent for P317R binding to CODD, and the authors' response is essentially that the fluorescent labeling of P317R (but not other mutants) uniquely interferes with binding to the NODD/CODD peptides, which does not make a lot of sense. The fluorescent labeling target lysine residues; while there are lysine in PHD2 in proximity to the peptide binding site, labeling these sites would affect binding to all mutants, not only P317R (which does not introduce any new labeling site). Furthermore, the authors did not really address the discrepancy with the observations by Flashman et al (2008) that NODD binds more weakly than CODD, which is inconsistent with their BLI results. Another point that makes me doubt the validity of the BLI results is the poor fit of the sensorgrams and the slow dissociation kinetics, which is inconsistent with the relatively low affinity in the 2-6 uM range.

Reviewer #2 (Public review):

Summary:

Mutations in the prolyl hydroxylase, PHD2, cause erythrocytosis and, in some cases, can result in tumorigenesis. Taber and colleagues test the structural and functional consequences of seven patient-derived missense mutations in PHD2 using cell-based reporter and stability assays, and multiple biophysical assays, and find that most mutations are destabilizing. Interestingly, they discover a PHD2 mutant that can hydroxylate the C-terminal ODD, but not the N-terminal ODD, which suggests the importance of N-terminal ODD for biology. A major strength of the manuscript is the multidisciplinary approach used by the authors to characterize the functional and structural consequences of the mutations. However, the manuscript had several major weaknesses, such as an incomplete description of how the NMR was performed, a justification for using neighboring residues as a surrogate for looking at prolyl hydroxylation directly, or a reference to the clinical case studies describing the phenotypes of patient mutations. Additionally, the experimental descriptions for several experiments are missing descriptions of controls or validation, which limits their strength in supporting the claims of the authors.

Strengths:

(1) This manuscript is well-written and clear.

(2) The authors use multiple assays to look at the effects of several disease-associated mutations, which support the claims.

(3) The identification of P317R as a mutant that loses activity specifically against NODD, which could be a useful tool for further studies in cells.

Weaknesses:

Major:

(1) The source data for the patient mutations (Figure 1) in PHD2 is not referenced, and it's not clear where this data came from or if it's publicly available. There is no section describing this in the methods.

(2) The NMR hydroxylation assay.

A. The description of these experiments is really confusing. The authors have published a recent paper describing a method using 13C-NMR to directly detect proly-hydroxylation over time, and they refer to this manuscript multiple times as the method used for the studies under review. However, it appears the current study is using 15N-HSQC-based experiments to track the CSP of neighboring residues to the target prolines, so not the target prolines themselves. The authors should make this clear in the text, especially on page 9, 5th line, where they describe proline cross-peaks and refer to the 15N-HSQC data in Figure 5B.<br /> B. The authors are using neighboring residues as reporters for proline hydroxylation, without validating this approach. How well do CSPs of A403 and I566 track with proline hydroxylation? Have the authors confirmed this using their 13C-NMR data or mass spec?<br /> C. Peak intensities. In some cases, the peak intensities of the end point residue look weaker than the peak intensities of the starting residue (5B, PHD2 WT I566, 6 ct lines vs. 4 ct lines). Is this because of sample dilution (i.e., should happen globally)? Can the authors comment on this?

(3) Data validating the CRISPR KO HEK293A cells is missing.

(4) The interpretation of the SEC data for the PHD2 mutants is a little problematic. Subtle alterations in the elution profiles may hint at different hydrodynamic radii, but as the samples were not loaded at equal concentrations or volumes, these data seem more anecdotal, rather than definitive. Repeating this multiple times, using matched samples, followed by comparison with standards loaded under identical buffer conditions, would significantly strengthen the conclusions one could make from the data.

Minor:

(1) Justification for picking the seven residues is not clearly articulated. The authors say they picked 7 mutants with "distinct residue changes", but no further rationale is provided.

(2) A major finding of the paper is that a disease-associated mutation, P317R, can differentially affect HIF1 prolyhydroxylation, however, additional follow-up studies have not been performed to test this in cells or to validate the mutant in another method. Is it the position of the proline within the catalytic core, or the identity of the mutation that accounts for the selectivity?

Comments on revision:

The revised manuscript addresses most of my concerns, i.e performing SEC experiments under matched sample concentrations, and incorporating additional data to justify the use of surrogate residues to monitor proline hydroxylation. I appreciate the improvements in the text to clarify the NMR experiments, but I still find their description confusing. Although the authors are using neighboring residues to monitor proline hydroxylation (which they justify convincingly using supplementary data), the language in the text suggests they are (and can?) monitor them directly (i.e. referring to proline cross-peaks in an 15N-HSQC spectrum). The axis labels in Figure 5B also seem to have become mislabeled in this revised version.

Reviewer #3 (Public review):

Summary:

This is an interesting and clinically relevant in vitro study by Taber et al., exploring how mutations in PHD2 contribute to erythrocytosis and/or neuroendocrine tumors. PHD2 regulates HIFα degradation through prolyl-hydroxylation, a key step in the cellular oxygen-sensing pathway.

Using a time-resolved NMR-based assay, the authors systematically analyze seven patient-derived PHD2 mutants and demonstrate that all exhibit structural and/or catalytic defects. Strikingly, the P317R variant retains normal activity toward the C-terminal proline but fails to hydroxylate the N-terminal site. This provides the first direct evidence that N-terminal prolyl-hydroxylation is not dispensable, as previously thought.

The findings offer valuable mechanistic insight into PHD2-driven effects and refine our understanding of HIF regulation in hypoxia-related diseases.

Strengths:

The manuscript has several notable strengths. By applying a novel time-resolved NMR approach, the authors directly assess hydroxylation at both HIF1α ODD sites, offering a clear functional readout. This method allows them to identify the P317R variant as uniquely defective in NODD hydroxylation, despite retaining normal activity toward CODD, thereby challenging the long-held view that the N-terminal proline is biologically dispensable. The work significantly advances our understanding of PHD2 function and its role in oxygen sensing, and might help in the future interpretation and clinical management of associated erythrocytosis.

Weaknesses:

There is a lack of in vivo/ex vivo validation. This is actually required to confirm whether the observed defects in hydroxylation-especially the selective NODD impairment in P317R-are sufficient to drive disease phenotypes such as erythrocytosis.

The reliance on HRE-luciferase reporter assays may not reliably reflect the PHD2 function and highlights a limitation in the assessment of downstream hypoxic signaling.

The study clearly documents the selective defect of the P317R mutant, but the structural basis for this selectivity is not addressed through high-resolution structural analysis (e.g., cryo-EM).

Given the proposed central role of HIF2α in erythrocytosis, direct assessment of HIF2α hydroxylation by the mutants would have strengthened the conclusions.

Comments on revision:

The revised manuscript by Taber et al. addresses the key points raised during the review process in a comprehensive and appropriate manner. While some limitations remain, such as the lack of in vivo validation or direct HIF2α assessment, I agree with the authors that these are beyond the scope of the current in vitro-focused study. The authors' primary goal was to define the structural and functional defects caused by disease-associated PHD2 mutations. In this respect, the evidence they present is largely convincing and methodologically appropriate. Additional clarifications and an expanded discussion of the luciferase assay's limitations and the P317R structural context strengthen the manuscript further.

Reviewer #2 (Public review):

Summary:

The authors show that a combination of arginine methyltransferase inhibitors synergize with PARP inhibitors to kill ovarian and triple negative cancer cell lines in vitro and in vivo using preclinical mouse models.

Strengths and weaknesses

The experiments are well-performed, convincing and have the appropriate controls (using inhibitors and genetic deletions) and use statistics.

They identify the DNA damage protein ERCC1 to be reduced in expression with PRMT inhibitors. As ERCC1 is known to be synthetic lethal with PARPi, this provides a mechanism for the synergy. They use cell lines only for their study in 2D as well as xenograph models.

Comments on revisions:

The authors have addressed by final concerns.

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 better understand the evolution of the matrisome and of ECM proteins, an important endeavor to better understand structure/function relationships. Toward this goal, the authors provide a comprehensive list with extensive annotations and cross-referencing of the 551 genes encoding matrisome proteins in the sea anemone genome.

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.

Weakness:

- 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 and accurately evaluating protein quantification. 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. While the authors in their response state that the inclusion of these PTMs only led to a modest increase in protein identification, they do not comment on the impact of including these PTMs on PSMs or protein abundance (precursor ion intensity).

Reviewer #1 (Public review):

Summary:

The study examines how pyruvate, a key product of glycolysis that influences TCA metabolism and gluconeogenesis, impacts cellular metabolism and cell size. It primarily utilizes the Drosophila liver-like fat body, which is composed of large post-mitotic cells that are metabolically very active. The study focuses on the key observations that over-expression of the pyruvate importer MPC complex (which imports pyruvate from the cytoplasm into mitochondria) can reduce cell size in a cell-autonomous manner. They find this is by metabolic rewiring that shunts pyruvate away from TCA metabolism and into gluconeogenesis. Surprisingly, mTORC and Myc pathways are also hyper-active in this background, despite the decreased cell size, suggesting a non-canonical cell size regulation signaling pathway. They also show a similar cell size reduction in HepG2 organoids. Metabolic analysis reveals that enhanced gluconeogenesis suppresses protein synthesis. Their working model is that elevated pyruvate mitochondrial import drives oxaloacetate production and fuels gluconeogenesis during late larval development, thus reducing amino acid production and thus reducing protein synthesis.

Strengths:

The study is significant because stem cells and many cancers exhibit metabolic rewiring of pyruvate metabolism. It provides new insights into how the fate of pyruvate can be tuned to influence Drosophila biomass accrual, and how pyruvate pools can influence the balance between carbohydrate and protein biosynthesis. Strengths include its rigorous dissection of metabolic rewiring and use of Drosophila and mammalian cell systems to dissect carbohydrate:protein crosstalk.

Comments on revised version:

The study remains an important dissection of how metabolic compartmentalization can influence cell size. It nicely uses Drosophila and a variety of metabolic approaches. The various pathway analyses and rigorous quantitation are strengths.

Reviewer #2 (Public review):

In this manuscript, the authors leverage multiple cellular models including the drosophila fat body and cultured hepatocytes to investigate the metabolic programs governing cell size. By profiling gene programs in the larval fat body during the third instar stage - in which cells cease proliferation and initiate a period of cell growth - the authors uncover a coordinated downregulation of genes involved in mitochondrial pyruvate import and metabolism. Enforced expression of the mitochondrial pyruvate carrier restrains cell size, despite active signaling of mTORC1 and other pathways viewed as traditional determinants of cell size. Mechanistically, the authors find that mitochondrial pyruvate import restrains cell size by fueling gluconeogenesis through the combined action of pyruvate carboxylase and phosphoenolpyruvate carboxykinase. Pyruvate conversion to oxaloacetate and use as a gluconeogenic substrate restrains cell growth by siphoning oxaloacetate away from aspartate and other amino acid biosynthesis, revealing a tradeoff between gluconeogenesis and provision of amino acids required to sustain protein biosynthesis. Overall, this manuscript is extremely rigorous, with each point interrogated through a variety of genetic and pharmacologic assays. The major conceptual advance is uncovering the regulation of cell size as a consequence of compartmentalized metabolism, which is dominant even over traditional signaling inputs. The work has implications for understanding cell size control in cell types that engage in gluconeogenesis but more broadly raise the possibility that metabolic tradeoffs determine cell size control in a variety of contexts.

Comments on revised version:

I have had a chance to review the manuscript and response to reviewer comments. I was extremely positive about this manuscript at first submission, and thought that the manuscript rigorously reported a surprising observation with broad implications across fields. The notion that intracellular metabolic networks can be dominant determinants of cell size, even over traditional signaling inputs, is surprising and important. The authors also provide convincing mechanistic insights into how the observed metabolic changes could affect cell size regulation. I think my previous comments and summary remain applicable for the revised manuscript.

Reviewer #3 (Public review):

Summary:

In this article, Toshniwal et al. investigate the role of pyruvate metabolism in controlling cell growth. They find that elevated expression of the mitochondrial pyruvate carrier (MPC) leads to decreased cell size in the Drosophila fat body, a transformed human hepatocyte cell line (HepG2), and primary rat hepatocytes. Using genetic approaches and metabolic assays, the authors find that elevated pyruvate import into cells with forced expression of MPC increases the cellular NADH/NAD+ ratio, which drives the production of oxaloacetate via pyruvate carboxylase. Genetic, pharmacological, and metabolic approaches suggest that oxaloacetate is used to support gluconeogenesis rather than amino acid synthesis in cells over-expressing MPC. The reduction in cellular amino acids impairs protein synthesis, leading to impaired cell growth.

Strengths:

This study shows that the metabolic program of a cell, and especially its NADH/NAD+ ratio, can play a dominant role in regulating cell growth.

The combination of complementary approaches, ranging from Drosophila genetics to metabolic flux measurements in mammalian cells, strengthens the findings of the paper and shows a conservation of MPC effects across evolution.

Reviewer #1 (Public review):

Summary:

This manuscript describes a chemical screen for activators of the eIF2 kinase GCN2 (EIF2AK4) in the integrated stress response (ISR). Recently, reported inhibitors of GCN2 and other protein kinases have been shown at certain concentrations to paradoxically activate GCN2. The study uses CHO cells and ISR reporter screens to identify a number of GCN2 activator compounds, including a potent "compound 20." These activators have implications for the development of new therapies for ISR-related diseases. For example, although not directly pursued in this study, these GCN2 activators could be helpful for the treatment of PVOD, which is reported for patients with certain GCN2 loss-of-function mutations. The identified activators are also suggested to engage with the GCN2 directly and can function while devoid of GCN1, a co-activator of GCN2.

Strengths:

The manuscript appears to be a largely rigorous study that flows in a logical manner. The topic is interesting and significant.

Weaknesses:

Portions of the manuscript are not fully clear. There are some experimental presentation and design concerns that should be addressed to support the stated conclusions.

Reviewer #2 (Public review):

Summary:

In this manuscript, Zhu, Emanuelli, and colleagues describe a novel pharmacological activator of the Integrated Stress Response kinase GCN2. The work is conclusive and biochemically solid. This work significantly adds to the pharmacological arsenal targeting the ISR and, in particular, GCN2.

Strengths:

Strong biochemistry, novel molecular activator of GCN2 (GCN1 independent).

Weaknesses:

The rationale for the screen is not exploited in the results (e.g., pathogenic GCN2 mutants), and lots of cell-based read-outs are not endogenous.

Major points

(1) Regarding the justification of the work. Since the authors justify the screen for GCN2 activators with loss-of-function mutants associated with diseases, it would be of interest to evaluate whether the best compounds identified in the study are indeed able to prompt activation of those mutants (or at least of the most prevalent). This approach could actually go in parallel with the docking experiments carried out in the last figure of the manuscript, where mutants could be modelized as well.

(2) The compounds are only tested using « artificial » proximal signaling outputs. It would be interesting to evaluate whether the best identified compounds are capable of prompting endogenous eIF2alpha phosphorylation in cellular models.

(3) Other GCN2 activators (other than GCN2iB, e.g., HC-7366) were recently identified. In this context, it would be of interest to carry out a small benchmarking study to evaluate how the compounds identified in the current study perform against the previously identified molecules.

Reviewer #3 (Public review):

Summary:

In this manuscript, the authors describe the results of a high-throughput screen for small-molecule activators of GCN2. Ultimately, they find 3 promising compounds. One of these three, compound 20 (C20), is of the most interest both for its potency and specificity. The major new finding is that this molecule appears to activate GCN2 independent of GCN1, which suggests that it works by a potentially novel mechanism. Biochemical analysis suggests that each binds in the ATP-binding pocket of GCN2, and that at least in vitro, C20 is a potent agonist. Structural modeling provides insight into how the three compounds might dock in the pocket and generates testable hypotheses as to why C20 perhaps acts through a different mechanism than other molecules.

Strengths:

Of the 3 compounds identified by the authors, C20 is the most interesting, not just for its intriguing mechanistic distinction as being GCN1-independent (shown genetically in two distinct cell lines, CHO and 293T in Figure 4, and in contrast to other GCN2 activators) but also for its potency. In in-cellulo assays, compound 21 appears as more of an ISR enhancer than an activator per se, and although compound 18 and compound 21 lead to upregulation of the ISR targets (Figure 2), that degree of upregulation is probably not significantly different from that induced by those compounds in Gcn2-/- cells. For C20, the effect appears stronger (although it is unclear whether the authors performed statistical analysis comparing the two genotypes in Figure 2D). In Figure 3, only C20 activates the ISR robustly in both CHO and 293T. Ultimately, C20 might be a tool for providing mechanistic insight into the details of GCN2 activation and regulation, and could be exploited therapeutically.

Weaknesses:

There are some limitations to the existing work. As the authors acknowledge, they do not use any of the compounds in animals; their in vivo efficacy, toxicity, and pharmacokinetics are unknown. But even in the context of the in cellulo experiments, it is puzzling that none of the three compounds, including C20, has any effects in HeLa cells when Neratinib does. It's beyond the scope of this paper to address definitively why that is, but it would at least be reassuring to know that C20 activates the ISR in a wider range of cells, including ideally some primary, non-immortalized cells. In addition, the ISR is a complex, feedback-regulated response whose output varies depending on the time point examined. The in cellulo analysis in this paper is limited to reporter assays at 18 hours and qRT-PCR assays at 4 and 8 hours. A more extensive examination of the behavior of the relevant ISR mRNAs and proteins (eIF2, ATF4, CHOP, cell viability, etc.) for C20 across a more extensive time course would give the reader a clearer sense of how this molecule affects ISR output. I also find it a bit strange that the authors describe C20 as "demonstrat(ing) weak inhibition of ... PKR"-the measured IC50 is ~4 μM, which is right around its EC50 for GCN2 activation. This raises the confounding possibility that C20 would simultaneously activate GCN2 while inhibiting PKR. While perhaps inhibition of PKR is not relevant under the conditions when GCN2 would be activated either experimentally or therapeutically, examining in cells the effects of C20 on GCN2 and PKR across a dose range would shed light on whether this cross-reactivity is likely to be of concern.

Reviewer #1 (Public review):

Summary:

The study by Raiola et al. conducted a quantitative analysis of tissue deformation during the formation of the primitive heart tube from the cardiac crescent in mouse embryos. Using the tools developed to analyze growth, anisotropy, strain, and cell fate from time-lapse imaging data of mouse embryos, the authors elucidated the compartmentalization of tissue deformation during heart tube formation and ventricular expansion. This paper describes how each region of the cardiac tissue changes to form the heart tube and ventricular chamber, contributing to our understanding of the earliest stages of cardiac development.

Strengths:

In order to understand tissue deformation in cardiac formation, it is commendable that the authors effectively utilized time-lapse imaging data, a data pipeline, and in silico fate mapping.

The study clarifies the compartmentalization of tissue deformation by integrating growth, anisotropy, and strain patterns in each region of the heart.

Weaknesses:

The significance of the compartmentalization of tissue deformation for the heart tube formation remains unclear.

Reviewer #2 (Public review):

The authors address an important challenge in developmental biology: the quantitative description of tissue deformation during organogenesis. They have developed a new pipeline to quantify early heart tube morphogenesis in the mouse, with cellular resolution. They adopt an elegant approach by integrating multiple 3D time-lapse datasets into a dynamic atlas of cardiac morphogenesis in order to compute spatio-temporal deformation patterns. The main findings highlight a strong compartmentalization of cell behaviors, with tissue growth and anisotropy exhibiting complementary and spatially segregated patterns. Using these data, the authors developed an in-silico fate mapping tool to interrogate cell displacement within the myocardium. This virtual model provides new mechanistic insights into how the bilateral cardiac primordia converge and transform into a three-dimensional heart tube. The authors identify "belt-like" constraints at the arterial and venous poles that prevent tissue expansion and thus shape the ventricular barrel morphology.

The computational framework is highly innovative and impressive, providing an unprecedented 3D model of tissue deformation during heart morphogenesis. It also opens avenues for testing hypotheses regarding tissue growth and the forces that cause cell motion. However, the proposed model of ventricular chamber formation with the two constraining belts remains hypothetical, lacking biological validation and requiring strengthening or modulation.

Overall, this carefully performed study provides a new model for exploring tissue deformation during organogenesis and will be of broad interest to computational and developmental biologists.

Reviewer #3 (Public review):

Summary:

The manuscript by Raiola and colleagues entitled "Quantitative computerized analysis demonstrates strongly compartmentalized tissue deformation patterns underlying mammalian heart tube formation" takes a highly quantitative approach to interrogating the earliest stages of cardiogenesis (12 hours, from early cardiac crescent to early heart tube) in a new and innovative way. The paper presents a new computational framework to help identify both regional and temporal patterns of tissue deformation at cellular resolution. The method is applied to live embryo imaging data (newly generated and from the group's previous pioneering work). In the initial setup, the new model was applied directly to raw time-lapse data, and the results were compared to actual cell tracks identified manually, showing close correlations of the model with the manual tracking. Next, they integrated spatial and temporal information from different embryos to generate a new model for tissue movement, driven by parameters such as tissue growth and anisotropy. Key findings from their model suggest that there are distinct compartments of tissue deformation patterns as the bilateral cardiac crescent develops into the linear heart tube, and that the ventricular chamber forms by a defined expansion pattern, as a 'hemi-barrel shape', with the aterial and venous poles (IFT and OFT) acting as the harnessing belts constraining the expansion of the chamber further. Lastly, the model is tested for its ability to predict future residence of cardiac crescent cells in the heart tube, which it seems to be able to do successfully based on fate tracking validation experiments.

Strengths:

The manuscript provides an exceptionally careful analysis of a critical stage during heart development - that of the earliest stages of morphogenesis, when the heart forms its first tube and chamber structures. While numerous studies have interrogated this stage of heart development, few studies have performed time-lapse imaging, and, to my knowledge, no other report has performed such in in-depth quantitative analysis and modeling of this complex process. The computational model applied to normal heart development of the myocardium (labelled by Nkx2-5) has revealed multiple new and interesting concepts, such as the distinct compartments of tissue deformation patterns and the growth trajectories of the emerging ventricle. The fact that the model operates at cellular resolution and over a nearly continuous time period of approximately 12 hours allows for unprecedented depth of the analysis in a largely unbiased manner. Going forward, one can imagine such models revealing additional information on these processes, performing analyses of subpopulations that form the heart, and maybe most importantly, applying the model to various perturbation models (genetic or otherwise). The manuscript is very well written, and the data display is accessible and transparent.

Weaknesses:

No major weaknesses are noted with the study. It would have been very exciting to see the model applied to any kind of perturbation, for example, a left-right defect model, or a model with compromised cardiac progenitor populations. However, the amount of live imaging required for such analyses renders this out of scope for the current study.

Reviewer #1 (Public review):

Summary:

The authors demonstrate the stereoselective role of D-serine in 1C metabolism, showing that D-serine competes with L-serine and inhibits mitochondrial L-serine transport. They observe expression of 1C metabolites in their metabolomics approach in primary cortical neurons treated with L-serine, D-serine, and a mixture of both. Their conclusions are based on the reduction in levels of glycine, polyamines, and their intermediates and formate. Single-cell RNA sequencing of N2a cells showed that cells treated with D-serine enhanced expression of genes associated with mitochondrial functions, such as respiratory chain complex assembly, and mitochondrial functions, with downregulation of genes related to amino acid transport, cellular growth, and neuron projection extension. Their work demonstrates that D-serine inhibits tumor cell proliferation and induces apoptosis in neural progenitor cells, highlighting the importance of D-serine in neurodevelopment.

Strengths:

D-amino acids are a marvel of nature. It is fascinating that nature decided to make two versions of the same molecule, in this case, an amino acid. While the L-stereoisomer plays well-known roles in biology, the D-stereoisomer seems to function in obscurity. Research into these novel signaling molecules is gathering momentum, with newer stereoisomers being discovered. D-serine has been the most well-studied among the different stereoisomers, and we still continue to learn about this novel neurotransmitter. The roles of these molecules in the context of metabolism is not well studied. The authors aim to elucidate the metabolic role of D-serine in the context of neuronal maturation with implications for 1C metabolism and in cell proliferation. The metabolic role of these molecules is just beginning to be uncovered, especially in the context of mammalian biology. This is the strength of the manuscript. The authors have done important work in prior publications elucidating the role of D-amino acids. The advancement of the field of D-amino acids in mammalian biology is significant, as not much is known. The presentation of RNA seq data is a valuable resource to the community, however, with caveats as mentioned below.

Weaknesses:

The following are some of the issues that come out in a critical reading of the manuscript. Addressing these would only strengthen and clarify the work.

(1) Kinetic assessment of D-serine versus L-serine: While the authors mention that D-serine is not a good substrate for SHMT2 compared to L-serine, the kinetic data are presented for only D-serine. In a substrate comparison with an enzyme, data must be presented for L-serine as well to make the conclusion about substrate specificity and affinity. Since the authors talk about one versus another substrate, there needs to be a kinetic comparison of both with Km (affinity). (Ref Figure 2 panel).

(2) Molecular Dynamics simulations, while a good first step in modeling interactions at the active site, rely on force fields. These force fields are approximations and do not represent all interactions occurring in the natural world. Setting up the initial conditions in the simulations can impact the final results in non-equilibrium scenarios. The basic question here is this: Is the simulated trajectory long enough so that the system reaches thermodynamic equilibrium and the measured properties converge? Prior studies have shown mixed results with the conclusion that properties of biological systems tend to converge in multi-second trajectories (not nanosecond scales as reported by the authors) and transition rates to low probability conformations require more time. (Ref Figure 2C).

(3) The authors use N2a cell line to demonstrate D-serine burden on primary cortical neurons. N2a is an immortalized cell line, and its properties are very different from primary neurons. The authors need to mention a rationale for the use of an immortalized cell line versus primary neurons. The transcriptomic profile of an immortalized cell line is different compared to a primary cell. Hence, the response to D-serine may vary between the two different cell types.

(4) In Figure 4D, the authors mention that D-serine activates the cleavage of caspase 3. Figure 4D shows only cleaved caspase 3 as a single band. They need to show the full blot that contains the cleaved fragments along with the major caspase 3 band.

(5) In Figure panel 4, the authors use neural progenitor cells (NPCs). They need to demonstrate that the population they are working with is NPCs and not primary neurons. There must be a figure panel staining for NPC markers like SOX2 and PAX6. Also, Figure S5 needs to be properly labeled. It is confusing from the legend what panels B-E refer to? Also, scale bars are not indicated.

(6) In Supplementary Figure panel 7F, the authors mention phosphatidyl L-serine and phosphatidyl D-serine. A chromatogram of the two species would clarify their presence as they used 2D-HPLC. On an MS platform, these 2 species are not distinguishable. Including a chromatogram of the 2 species would be helpful to the readers.

(7) The authors mention about enantiomeric shift of serine metabolism during neural development, which appears to be a discussion of prior published data from Hubbard et al, 2013, Burk et al, 2020, and Bella et a,l 2021 in Supplementary Figure panels 8 A-E. This should not be presented as a figure panel, as it gives the false impression that the authors have performed the experiment, which is clearly not the case. However, its discussion can well serve as part of the manuscript in the discussion section.

(8) The entire presentation of the section on enantiomeric shift of serine metabolism during neural development (lines 274-312) is a discussion and should be part of the discussion section and not in the results section. This is misleading.

(9) The discussion section is not well written. There is no mention of recent work related to D-serine that has a direct bearing on its metabolic properties. In the discussion section, paragraph 1, the authors mention that their work demonstrates the selective synthesis of D-serine in mature neurons as opposed to neural progenitor cells. This concept has been referred to in prior publications:

(a) Spatiotemporal relationships among D-serine, serine racemase, and D-amino acid oxidase during mouse postnatal development. PMID:14531937.

(b) D-cysteine is an endogenous regulator of neural progenitor cell dynamics in the mammalian brain. PMID:34556581.

(10) In the abstract, in lines 101 and 102, the authors mention "how D-serine contributes to cellular metabolism beyond neurotransmission remains largely unknown". In 2023, a paper in Stem Cell Reports by Roychaudhuri et al (PMID:37352848) showed that D and L-serine availability impacts lipid metabolism in the subventricular zone in mice, affecting proliferative properties of stem-cell derived neurons using a comprehensive lipidomics approach. There is no mention of this work even in the discussion section, as it bears directly on L and D-serine availability in neurons, which the authors are investigating. In the discussion section in lines 410-411, the authors mention the role of D-serine in neurogenesis, but surprisingly don't refer to the above reference. The role of D-serine in neurogenesis has been demonstrated in the Sultan et al (lines 855-857) and Roychaudhuri et al references.

(11) Both D-serine and the structurally similar stereoisomer D-cysteine (sulfur versus oxygen atom) have a bearing on 1C metabolism and the folate cycle. With reference to the folate cycle, Roychaudhuri et al in 2024 (PMID:39368613) have shown in rescue experiments in mice that supplementing a higher methionine diet provides folate cycle precursors to rescue the high insulin phenotype in SR-deficient mice. Since 1C metabolism is being discussed in this manuscript, the authors seem to overlook prior work in the field and not include it in their discussion, even when it is the same enzyme (SR) that synthesizes both serine and cysteine. Since the field of D-amino acid research is in its infancy, the authors must make it a point to include prior work related to D-serine at least, and not claim that it is not known. The known D-stereoisomers are not many, hence any progress in the area must include at least a discussion of the other structurally related stereoisomers.

(12) Racemases (serine and aspartate) in general are promiscuous enzymes and known to synthesize other stereoisomers in addition to D-serine, D-cysteine, and D-aspartate. A few controls, like D-aspartate, D-cysteine, or even D-alanine must be included in their study to demonstrate the specific actions of D-serine, especially in the N2a cell treatment experiments. Cysteine and Serine are almost identical in structure (sulfur versus oxygen atom), and both are synthesized by serine racemase (published). Cysteine has also been very recently shown to inhibit tumor growth and neural progenitor cell proliferation. (PMIDs: 40797101 and 34556581). How the authors' work relates to the existing findings must be discussed, and this would put things in perspective for the reader.

Reviewer #2 (Public review):

Summary:

This study by Suzuki et al. reports an interesting stereo-selective role of D-serine in regulating one-carbon metabolism during neurodevelopment to adapt the functional transition, probably through the competition with mitochondrial transport of L-serine. The authors provide a multi-layered set of evidence, including metabolomics, enzyme assays, mitochondrial transport competition, and functional assays in immature/neural progenitor cells, to build up a conceptual integration of D-serine as both a neurotransmitter and a metabolic regulator in the central neural system, which raises a broad potential interest to the neuroscience and metabolism communities.

Strengths:

This work provides a conceptual advance that D-serine not only serves as a traditional neurotransmitter in the central neural system but also critically contributes to metabolic regulation of neural cells. The authors performed solid metabolomic assays to validate the suppressive effect of D-serine on the one-carbon metabolic pathway, providing some evidence that D-serine competitively inhibits mitochondrial serine transport, but not directly impairs SHMT2 enzymatic activity. All these data indicate a critical role of D-serine synthesis during neural maturation and suggest a potential translational strategy for targeting serine metabolism in neural tumors.

Weaknesses:

(1) The detailed mechanism by which D-serine competes with L-serine for its mitochondrial transport is not investigated. For example, although the authors made some discussion, they did not provide direct genetic or biochemical evidence linking these effects to the specific transporters, such as SFXN1.

(2) Unlike tumor cells, where SHMT2 usually plays a predominant role in catalyzing serine/THF-derived one-carbon metabolism, normal cells may employ both SHMT1 and SHMT2 to do the work. Even under certain conditions that SHMT2-mediated one-carbon metabolism is suppressed, the activity of SHMT1 could be elevated for compensation. Thus, it is important to investigate whether D-serine affects SHMT1 activity or changes the balance between SHMT1- and SHMT2-mediated one-carbon metabolism. To this aim, the authors are strongly encouraged to perform a metabolic flux assay (MFA) by using 13C-labeled L-serine in the model cells in the presence and absence of D-serine.

(3) A defect in serine-derived one-carbon metabolism may cause multiple cellular stress responses. It is valuable to detect whether cellular NADPH/NADH, GSH, or ROS is altered before and after D-serine treatment.

(4) The physiological relevance between D-serine and neural cell maturation/death should be further tested and discussed, since the dosage of D-serine used in the in vitro assay is much higher than that in physiological conditions.

Reviewer #3 (Public review):

Summary:

This manuscript presents a comprehensive and well-executed investigation into the metabolic role of D-serine in the central nervous system. The authors provide solid evidence that D-serine competitively inhibits mitochondrial L-serine transport, thereby impairing one-carbon metabolism. This stereoselective mechanism reduces glycine and formate production, suppresses cellular proliferation, and induces apoptosis in immature neural cells and glioblastoma stem cells. Developmental analyses further reveal a physiological enantiomeric shift in serine metabolism during neurogenesis, aligning with the transition from proliferation to maturation. Overall, the study bridges developmental neurobiology, cancer metabolism, and amino acid transport, uncovering a previously unrecognized metabolic function of D-serine beyond its role in neurotransmission.

Strengths:

(1) The discovery that D-serine inhibits one-carbon metabolism by competing for mitochondrial L-serine transport-rather than through enzymatic inhibition or receptor-mediated signaling-represents a significant and previously underappreciated mechanism. This finding has broad implications for understanding metabolic regulation during neurodevelopment and offers potential relevance for targeting metabolic vulnerabilities in cancer.

(2) The authors integrate metabolomics, mitochondrial transport assays, molecular dynamics simulations, genetic and pharmacologic perturbations, transcriptomics, and both in vitro and ex vivo models. The breadth of experimental approaches, combined with the coherence of the findings across systems, provides strong support for the central conclusions and enhances the overall impact of the study.

(3) The temporal shift in D-/L-serine levels during neurodevelopment is elegantly linked to the transition from proliferative to mature neuronal states. The selective vulnerability of neural progenitors and tumor cells-contrasted with the resistance of mature neurons-highlights a biologically meaningful and potentially targetable metabolic distinction.

Weaknesses:

(1) While the authors attribute D-serine's metabolic effects to competition with mitochondrial L-serine transport, the specific identity of the transporter(s) mediating this process remains undefined. This represents a meaningful mechanistic gap, as the central conclusion depends on D-serine limiting mitochondrial L-serine availability to inhibit one-carbon metabolism.

(2) The effective concentrations of D-serine used in vitro (IC₅₀ ≈ 1-2 mM) exceed typical brain levels (~0.3 mM). While the authors acknowledge this, a more focused discussion on whether higher local D-serine concentrations could arise in specific microenvironments - such as synaptic compartments, tumor niches, or pathological states-would help contextualize the in vitro findings and strengthen their physiological relevance. For example, disruptions in D-serine clearance or altered expression of serine racemase and transporters in disease contexts could lead to localized accumulation. Moreover, differences between extracellular and intracellular D-serine pools - and the mechanisms governing their regulation - may further influence its metabolic impact in vivo.

(3) While the manuscript focuses on neural stem/progenitor cells and neural tumors, it remains unclear whether the anti-proliferative effects of D-serine are specific to neural lineages or extend to other highly proliferative non-neural cell types. A brief discussion addressing this point would help clarify the scope of D-serine's metabolic impact and whether its mechanism of action reflects a unique vulnerability in neural cells or a more general feature of proliferative metabolism. This distinction is particularly relevant for assessing the broader therapeutic potential of targeting mitochondrial L-serine transport.

Reviewer #1 (Public review):

Summary:

Plasmodesmata are channels that allow cell-cell communication in plants; based on the functional similarities between facilitated transport within plasmodesmata and into the nucleus, the authors speculate that nuclear pore complex proteins might be involved in plasmodesmata function. In this manuscript, they localize nuclear pore complex proteins to plasmodesmata using proteomics and heterologous overexpression. They also document a possible plasmodesmata transport defect in a mutant affecting one nuclear pore complex protein.

Strengths:

The main strength of this manuscript is the interesting and novel hypothesis. This work could open exciting new directions in our understanding of plasmodesmata function and cell-cell communication in plants. They also localized many NUPs (12/35 Arabidopsis NUPs).

Weaknesses:

The main weakness of this manuscript is that the data are incomplete. While the authors appropriately and frequently acknowledge caveats to their data, two controls are essential to interpret the results that fluorescently-tagged NUPs localize to the plasmodesmata: (1) assessment of the expression level of these fluorescently-tagged NUPs to determine whether the plasmodesmata localization might be an overexpression artefact; (2) assessment of the function of the fluorescently-tagged NUPs, either by molecular complementation of a knockout mutant phenotype or by biochemical methods to test whether the fluorescently-tagged NUP incorporates into nuclear pore complexes. Conducting these experiments for even one fluorescently-tagged NUP would substantially strengthen this manuscript.

Reviewer #2 (Public review):

Summary:

The authors aim to address whether nuclear pore complex components localize and function at PD in plant cells to mediate cell-to-cell communication.

Strengths:

(1) Novelty and Significance:<br /> The core hypothesis, drawing parallels between PD and NPC transport, is highly original and addresses a critical gap in understanding plant intercellular communication. The idea that phase-separated domains formed by FG-NUPs could act as diffusion barriers at PD offers a plausible and sophisticated explanation for their complex transport properties, including size exclusion and facilitated translocation. This could fundamentally change how we view PD function.

(2) Comprehensive Evidence:<br /> The study employs a rigorous and diverse set of experimental approaches, including a comprehensive bioinformatic analysis of both moss and Arabidopsis NUPs in available PD proteomic datasets, extensive imaging analysis of Nup localization in vivo, and functional transport assays using a loss-of-function nup mutant (cpr5). The transport assay is particularly important to provide functional evidence linking CPR5 to PD-mediated transport. The finding that callose levels were not significantly different in cpr5 mutants under these conditions is helpful and supports a distinct, callose-independent mechanism of transport regulation.

(3) Objectivity:<br /> The authors are forthright in discussing the limitations and potential artifacts of their own data, clearly distinguishing between observations and definitive conclusions.

Weaknesses:

While the claims are generally justified as hypotheses or consistent observations, the authors themselves extensively detail the caveats, which are worth reiterating for clarity:

(1) Potential Overexpression Artifacts in Localization:<br /> Although efforts were made to control expression levels, the authors acknowledge that transient overexpression could still lead to NUP accumulation at PD, either as a physiologically relevant accumulation under excess conditions or due to mis-targeting, or even as storage depots. The resolution of confocal microscopy also does not allow for a definitive conclusion on the nature of the location.

(2) Proteomics Purity:<br /> The authors note that the presence of NUPs in PD fractions/proteomics cannot definitively rule out contamination, as PD cannot currently be purified to absolute homogeneity and is often contaminated with other organelles, including the nucleus.

(3) CPR5 Mutant Interpretation:<br /> While cpr5 mutants exhibited reduced macromolecular transport, the authors state that they cannot exclude that the reduced transport is due to secondary effects in the cpr5 mutants, which show rather severe phenotypic defects. This is an important distinction, as CPR5 has known roles in defense responses and hormone signaling that could indirectly influence PD integrity, independent of callose deposition. The lack of effect on small molecule transport is a good control, but the broader pleiotropic effects of cpr5 mutants remain a consideration.

(4) Conceptual Distinction between NPC and PD:<br /> The authors correctly point out that while similarities exist, the physical assembly of NUPs at PD must differ from that at the NPC due to the presence of the desmotubule and smaller cytoplasmic sleeve width at PD. Moreover, nucleocytoplasmic transport depends on karyopherin proteins that interact with the NPC central channel to complete the transport. Yet the role of karyopherins in this case is not clear. Therefore, the proposed "PD pore complex" may bear some NPC features, but not be identical.

Reviewer #3 (Public review):

Summary:

This manuscript presents a step towards testing the hypothesis that plasmodesmata have homology to nuclear pores. The similarities between the two structures have long been noted as both structures allow the transport of proteins and nucleic acids, and both structures are composed of curved membranes. The manuscript has identified nuclear pore proteins (NUPs) in plasmodesmal protein fractions and uses live imaging in a non-endogenous system and functional assays of a mutant to propose that this might be a bona fide association.

The conclusions the authors seek to draw are that: NUPs are present in plasmodesmal protein fractions; NUPs localise at plasmodesmata; NUPs might form a pore-gating complex at plasmodesmata, regulating non-specific (2xGFP) and specific (SHR) transport through plasmodesmata

The authors then use these conclusions to propose the possibility that phase separation mediates transport through plasmodesmata. If there is phase separation at plasmodesmata or a nuclear pore-like complex, it would revolutionise the community. However, this data is insufficient to act as a cornerstone for such a discovery.

Strengths:

The strength of the manuscript lies in the boldness and novelty of the idea.

Weaknesses:

The weaknesses lie in the lack of informative controls. The authors' own assessments of their data suggest they agree with this - in their abstract alone, they point out that the transport defects they observe might be off-target effects, and suggest there is a requirement in the future to determine whether the NUPs are bona fide PD components.

Across the proteomic and live imaging experiments, the conclusions could be stronger if they compared the NUP localisation and accumulation with ER proteins - the question of whether NUPs behave like other ER proteins is not addressed. As NUPs reside in the nuclear envelope, continuous with the ER, and the ER traverses plasmodesmata, a comparison between the NUPs and ER proteins would be extremely informative.

Regarding the proteomic identification of NUPs in plasmodesmal fractions, the authors place significant weight on their own metric for PD enrichment, the PD score. As I understand it, this a metric derived from addition of two factors: a two component enrichment score that is the difference between intensity of peptides of a given protein in the PD fraction and cell wall fraction, added to the difference between intensity of peptides of a given protein in the PD fraction and total cell fraction, and a feature score that is a factor that describes representation of protein domains contained in said given protein in the plasmodesmal fraction relative to the representation of that domain in proteins in the whole proteome. The features chosen for analysis are not indicated, and the feature factor, as I understand it, is a score common to all proteins with a given feature. While each of the factors carries a measure of meaning and information, I do not understand how adding them is mathematically or biologically meaningful.

Reviewer #1 (Public review):

Summary:

The manuscript presents a comprehensive study on the developing synthetic gene circuits targeting mutant RAS expressing cells. The aim of this study is to use these RAS targeting circuits as cancer cell classifiers and enable the selective expression of an output protein in correlation with RAS activity. The system is based on the bacterial two-component system NarX/NarL. A RAS-binding domain is fused to a NarX mutant either defective in the ATP binding (N509A) or the phosphorylation site (H399Q). Nanocluster formation of RAS-GTP reconstitutes an active histidine kinase sensor dimer that phosphorylates the response regulator NarL thus leading to the expression of an output protein. The integration of RAS-dependent MAPK responsive elements to express the RAS sensor components generates RAS circuits with an extended dynamic range between mutant and wild-type RAS. The selectivity of the RAS circuits is confirmed in a set of cancer cell lines expressing endogenous levels of mutant or wild-type RAS or oncogenes affecting RAS signaling upstream or downstream. Expression of the suicide gene HSV thymidine kinase as an outcome protein kills RAS-driven cancer cells demonstrating the functionality of the system.

Strengths:

This proof-of-concept study convincingly demonstrates the potential of synthetic gene circuits to target oncogenic RAS in tumor cell lines, act as RAS mutant cell classifier, and induce the killing of RAS-driven cells.

Weaknesses:

A therapeutic strategy based on of this four-plasmid system may be difficult to implement in RAS-driven solid cancers. However, potential solutions are discussed.

Reviewer #2 (Public review):

The manuscript describes an interesting approach towards designing genetic circuits to sense different RAS mutants in the context of cancer therapeutics. The authors created sensors for mutant RAS and incorporated feed-forward control that leverages endogenous RAS/MAPK signaling pathways in order to dramatically increase the circuits' dynamic range. The modularity of the system is explored through the individual screening of several RAS binding domains, transmembrane domains, and MAPK response elements, and the author further extensively screened different combinations of circuit components. This is an impressive synthetic biology demonstration that took it all the way to cancer cell lines. However, given the sole demonstrated output in the form of fluorescent proteins, the authors' claims related to therapeutic implications require additional empirical evidence or, otherwise, expository revision.

Major comments:

"These therapies are limited to cancers with KRASG12C mutations" is technically accurate. However, in this fast-moving field, there are examples such as MRTX1133 which holds the promise to target the very G12D mutation that is the focus of this paper. There are broader efforts too. It would help the readers better appreciate the background if the authors could update the intro to reflect the most recent landscape of RAS-targeting drugs.

Only KRASG12D was used as a model in the design and optimization work of the genetic circuits. Other mutations should be quite experimentally feasible and comparisons of the circuits' performances across different KRAS mutations would allow for stronger claims on the circuits' generalizability. Particularly, the cancer cell line used for circuit validation harbored a KRASG13D mutation. While the data presented do indeed support the circuit's "generalizability," the model systems would not have been consistent in the current set of data presented.

In Figure 2a, the text claims that "inactivation of endogenous RAS with NF1 resulted in a lower YFP/RBDCRD-NarX expression," but Figure 2a does not show a statistically significant reduction in expression of SYFP (measured by "membrane-to-total signal ratio [RU]).

The therapeutic index of the authors' systems would be better characterized by a functional payload, other than florescent proteins, that for example induce cell death, immune responses, etc.

Regarding data presented in "Mechanism of action" (Figure 2), the observations are interesting and consistent across different fluorescent reporters. However, with regard to interpretations of the underlying molecular mechanisms, it is not clear whether the different output levels in 2b, 2c, and 2d are due to the pathway as described by the authors or simply from varied expression levels of RBDCRD-NarX itself (2a) that is nonlinearly amplified by the rest of the circuit. From a practical standpoint, this caveat is not critical with respect to the signal-to-noise ratios in later parts of the paper. From a mechanistic interpretation standpoint, claims made forth in this section are not clearly substantiated. Some additional controls would be nice. For example, if the authors express NarXs that constitutively dimerize on the membrane, what would the RasG12D-responsiveness look like? Does RasG12D alter the input-output curve of NarL-RE? How would Figure 4f compare to a NaxR constitutively dimerized control that only relies on transcriptional amplification of the Ras-dependent promoters? It's also possible that these Ras could affect protein production at the post-transcriptional or even post-translational levels, which were not adequately considered.

The text claims that "in contrast to what we saw in HEK293 overexpressing RAS (Figure 5d), the "AND-gate" RAS-targeting circuits do not generate higher output than the EF1a-driven, binding-triggered RAS sensor in HCT-116. Instead, the improved dynamic range results from decreased leakiness in HCT- 116k.o." Comparing the experiment from Figure 5d, which looks at activation in KRASG12D and KRASWT, to the experiments in Figure 6b-d, which looks at activation in HCT-116WT and HCT-116KO is misleading. In Fig 5d., cells are transfected with KRASG12D and KRASWT to emulate high levels of mutant RAS and high levels of wild-type RAS. In Figures 6b-d, HCT-116WT has endogenous levels of mutant RAS, while the KCT-116KO is a knock-out cell line, and does not have mutant or WT RAS. Therefore, the improved dynamic range or "decreased leakiness in HCT-116KO" in comparison to Figure 5d. is more comparable to the NF1 condition from Figure 2, which deactivates endogenous RAS. While this may not be feasible, the most accurate comparison would have been an HCT-116KO line with KRASWT stably integrated.

We couldn't locate the citation or discussion of Figure 4d in the text. Conversely, based on the text description, Figure 6g would contain exciting results. But we couldn't find Figure 6g anywhere ... unless it was a typo and the authors meant Figure 6f, in which case the cool results in Figure S8 could use more elaboration in the main text.

Comments on revisions:

Now that the authors have extensively addressed my comments through text and additional experiments, I am supportive of its conclusions. I thank them for the rigorous updates and congratulate them on an important piece demonstrating the potential of synthetic biology circuits.

Reviewer #3 (Public review):

Summary:

Mutations that result in consistent RAS activation constitute a major driver of cancer. Therefore, RAS is a favorable target for cancer therapy. However, since normal RAS activity is essential for the function of normal cells, a mechanism that differentiates aberrant RAS activity from normal one is required to avoid severe adverse effects. To this end, the authors designed and optimized a synthetic gene circuit that is induced by active RAS-GTP. The circuit components, such as RAS-GTP sensors, dimerization domains, and linkers. To enhance the circuit selectivity and dynamic range, the authors designed a synthetic promoter comprised of MAPK-responsive elements to regulate the expression of the RAS sensors, thus generating a feed-forward loop regulating the circuit components. Circuit outputs with respect to circuit design modification were characterized in standard model cell lines using basal RAS activity, active RAS mutants, and RAS inactivation.

This approach is interesting. The design is novel and could be implemented for other RAS-mediated applications. The data support the claims, and while this circuit may require further optimization for clinical application, it is an interesting proof of concept for targeting of aberrant RAS activity. I therefore recommend accepting this paper.

Strengths:

Novel circuit design, through optimization and characterization of the circuit components, solid data.

Weaknesses:

This manuscript could significantly benefit from testing the circuit performance in more realistic cell lines, such as patient-derived cells driven by RAS mutations, as well as in corresponding non-cancer cell lines with normal RAS activity. Furthermore, testing with therapeutic output proteins in vitro, and especially in vivo, would significantly strengthen the findings and claims.

Summary:

Given the revision made, I would recommend a minor revision that discusses the specificity limitations of this experimental setup.

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.

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 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 have addressed weaknesses in the revised version.

Reviewer #3 (Public review):

Summary:

This manuscript reports the discovery of new compounds that selectively inhibit SMARCA4/SMARCA2 ATPase activity and have pronounced effects on uveal melanoma cell proliferation. They induce apoptosis and suppress tumor growth, with no toxicity in vivo. The report provides biological significance by demonstrating that the drugs alter chromatin accessibility at lineage specific gene enhancer regions and decrease expression of lineage specific genes, including SOX10 and SOX10 target genes.

Strengths:

The study provides compelling evidence for the therapeutic use of these compounds and does a thorough job at elucidating the mechanisms by which the drugs work. The study will likely have a high impact on the chromatin remodeling and cancer fields. The datasets will be highly useful to these communities.

Weaknesses:

The authors have addressed all my concerns.

Reviewer #1 (Public review):

The manuscript "Heterozygote advantage cannot explain MHC diversity, but MHC diversity can explain heterozygote advantage" explores two topics. First, it is claimed that the recently published conclusion by Mattias Siljestam and Claus Rueffler (in the following referred to as [SR] for brevity) that heterozygote advantage explains MHC diversity does not withstand even a very slight change in ecological parameters. Second, a modified model that allows an expansion of the MHC gene family shows that homozygotes outperform heterozygotes. This is an important topic and could be of potential interest to readers if the conclusions are valid and non-trivial.

Let me first comment on the second part of the manuscript that describes the fitness advantage of the 'gene family expansion'. I think this, by itself, is a totally predictable result. 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. Yet, as I understood the narrative of the manuscript, the expansion of the gene family serves as a mere counter-example to the disputed finding of [SR], rather than a systematic study of the eco-evolutionary consequences of this process.

Now to the first part of the manuscript, which claims that the point made in [RS] is not robust and breaks down under a small change in the parameters. 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. The only piece of information given in the manuscript is that, unlike in [SR], the adjustable parameter c_{max} is kept constant when the number of pathogens is changed.

In my opinion, the information provided in the manuscript does not allow one to conclude anything about the relevance and the validity of its main claim. At the same time, the simulations done in [SR] are described with a fair amount of detail. Which allows me to assume that the conclusions made in [SR] are fairly robust and, in particular, have been demonstrated not to be too sensitive to changes in the main "suspect', c_{max}. Let me briefly justify my point.

First, it follows from Eqs (4,5) in the main text and (A12-A13) in the Appendix that c_{max} and K do not independently affect the dynamics of the model, but it's rather their ratio K/c_max that matters. It can be seen by dividing the numerator and denominator of (5) by c_max. Figure 3 shows the persistent branching for 4 values of K that cover 4 decades. As it appears from the schemes in the top row of Figure 3, those simulations are done for the same positions and widths/virulences of pathogens. So the position of x* should be the same in all 4 cases, presumably being at the center of pathogens, (x*,x*) = (0,0). According to the definition of x* given in the Appendix after Eqs (A12-A13), this means that c_max remains the same in all 4 cases. So one can interpret the 4 scenarios shown in Figure 3 as corresponding not to various K, but to various c_max that varied inversely to K. That is, the results would have been identical to those shown in Figure 3 if K were kept constant and c_max were multiplied by 0.1, 1, 10, and 100, or scaled as 1/K. This begs the conclusion that the branching remains robust to changes in c_max that span 4 decades as well.

Naturally, most, if not all, the dynamics will break down if one of the ecological characteristics changes by a factor of 10^43, as it is reported in the submitted manuscript. 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. In [SP], it is clearly shown where the pathogens are.

Another argument that makes me suspicious in the utility of the conclusions made in the manuscript and plays for the validity of [SP] is the adaptive dynamics derivation of the branching conditions. It is confirmed by numerics with sufficient accuracy, and as it stands in its simple form of the inequality between two widths, the branching condition appears to be pretty robust with respect to reasonable changes in parameters.

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].

Reviewer #2 (Public review):

Summary:

This study addresses the population genetic underpinnings of the extraordinary diversity of genes in the MHC, which is widespread among jawed vertebrates. This topic has been widely discussed and studied, and several hypotheses have been suggested to explain this diversity. One of them is based on the idea that heterozygote genotypes have an advantage over homozygotes. While this hypothesis lost early on support, a reason study claimed that there is good support for this idea. The current study highlights an important aspect that allows us to see results presented in the earlier published paper in a different light, changing strongly the conclusions of the earlier study, i.e., there is no support for a heterozygote advantage. This is a very important contribution to the field. Furthermore, this new study presents an alternative hypothesis to explain the maintenance of MHC diversity, which is based on the idea that gene duplications can create diversity without heterozygosity being important. This is an interesting idea, but not entirely new.

Strengths:

(1) A careful re-evaluation of a published model, questioning a major assumption made by a previous study.

(2) A convincing reanalysis of a model that, in the light of the re-analysis-loses all support.

(3) A convincing suggestion for an alternative hypothesis.

Weaknesses:

(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).

(2) The title of the study is very catchy, but it needs to be explained better in the text.

Reviewer #3 (Public review):

This manuscript describes a careful and thorough evaluation of an evolutionary simulation model published previously. The model and this report address the question, whether heterozygote advantage (HA) by itself as a selection mechanism can explain a substantial level of allelic diversity as it is often seen in MHC immune genes. Despite decades of research on the topic of pathogen-mediated selection for MHC diversity, it remains an open question by which specific selection mechanisms this exceptional allelic diversity is maintained.

The previously published paper posits, in contrast to various previous studies, that HA is, in fact, able to maintain a level of allelic diversity as seen in many populations, just by itself, given certain conditions. The current manuscript now challenges this conclusion by highlighting that the previous model results only hold under very narrow parameter ranges.

Besides criticizing some of the conceptual points of the previous paper, the author carefully rebuilt the previously published model and replicated their results, before then evaluating the robustness of the model results to reasonable variation in different parameters. From this evaluation, it becomes clear that the previously reported results hinge strongly on a certain scaling or weighing factor that is adjusted for every parameter setting and essentially counteracts the changes induced by changing the parameters. The critical impact of this one parameter is not clearly stated in the previous paper, but raises serious doubts about the generalizability of the model to explain MHC allelic variation across diverse vertebrate species.

Given the fact that the MHC genes are among the most widely studied genes in vertebrates, and that understanding their evolution will shed light on their association with various complex diseases, the insights from this report and the general discussion of how MHC diversity evolved are of interest to at least some of the community. The manuscript is very well written and makes it easy to follow the theoretical and methodological details of the model and the arguments. I have only a few minor comments that I am detailing below. Furthermore, I would be very interested to read a response by the previous authors, especially on the relevance of this scaling/weighing factor that they introduced into their model, as it is possible that I might have missed something about its meaning.

Reviewer #1 (Public review):

Summary:

Laura Morano and colleagues have performed a screen to identify compounds that interfere with the formation of TopBP1 condensates. TopBP1 plays a crucial role in the DNA damage response, and specifically the activation of ATR. They found that the GSK-3b inhibitor AZD2858 reduced the formation of TopBP1 condensates and activation of ATR and its downstream target CHK1 in colorectal cancer cell lines treated with the clinically relevant irinotecan active metabolite SN-38. This inhibition of TopBP1 condensates by AZD2858 was independent from its effect on GSK-3b enzymatic activity. Mechanistically, they show that AZD2858 thus can interfere with intra-S-phase checkpoint signaling, resulting in enhanced cytostatic and cytotoxic effects of SN-38 (or SN-38+Fluoracil aka FOLFIRI) in vitro in colorectal carcinoma cell lines.

Comments on latest version:

The requested plots are in figure S7 of the latest manuscript version, and look convincing. My last point is now adequately addressed.

Reviewer #2 (Public review):

Summary:

In 2021 (PMID: 33503405) and 2024 (PMID: 38578830) Constantinou and colleagues published two elegant papers in which they demonstrated that the Topbp1 checkpoint adaptor protein could assemble into mesoscale phase-separated condensates that were essential to amplify activation of the PIKK, ATR, and its downstream effector kinase, Chk1, during DNA damage signalling. A key tool that made these studies possible was the use of a chimeric Topbp1 protein bearing a cryptochrome domain, Cry2, which triggered condensation of the chimeric Topbp1 protein, and thus activation of ATR and Chk1, in response to irradiation with blue light without the myriad complications associated with actually exposing cells to DNA damage.

In this current report Morano and co-workers utilise the same optogenetic Topbp1 system to investigate a different question, namely whether Topbp1 phase-condensation can be inhibited pharmacologically to manipulate downstream ATR-Chk1 signalling. This is of interest, as the therapeutic potential of the ATR-Chk1 pathway is an area of active investigation, albeit generally using more conventional kinase inhibitor approaches.

The starting point is a high throughput screen of 4730 existing or candidate small molecule anti-cancer drugs for compounds capable of inhibiting the condensation of the Topbp1-Cry2-mCherry reporter molecule in vivo. A surprisingly large number of putative hits (>300) were recorded, from which 131 of the most potent were selected for secondary screening using activation of Chk1 in response to DNA damage induced by SN-38, a topoisomerase inhibitor, as a surrogate marker for Topbp1 condensation. From this the 10 most potent compounds were tested for interactions with a clinically used combination of SN-38 and 5-FU (FOLFIRI) in terms of cytotoxicity in HCT116 cells. The compound that synergised most potently with FOLFIRI, the GSK3-beta inhibitor drug AZD2858, was selected for all subsequent experiments.

AZD2858 is shown to suppress the formation of Topbp1 (endogenous) condensates in cells exposed to SN-38, and to inhibit activation of Chk1 without interfering with activation of ATM or other endpoints of damage signalling such as formation of gamma-H2AX or activation of Chk2 (generally considered to be downstream of ATM). AZD2858 therefore seems to selectively inhibit the Topbp1-ATR-Chk1 pathway without interfering with parallel branches of the DNA damage signalling system, consistent with Topbp1 condensation being the primary target. Importantly, neither siRNA depletion of GSK3-beta, or other GSK3-beta inhibitors were able to recapitulate this effect, suggesting it was a specific non-canonical effect of AZD2858 and not a consequence of GSK3-beta inhibition per se.

To understand the basis for synergism between AZD2858 and SN-38 in terms of cell killing, the effect of AZD2858 on the replication checkpoint was assessed. This is a response, mediated via ATR-Chk1, that modulates replication origin firing and fork progression in S-phase cell under conditions of DNA damage or when replication is impeded. SN-38 treatment of HCT116 cells markedly suppresses DNA replication, however this was partially reversed by co-treatment with AZD2858, consistent with the failure to activate ATR-Chk1 conferring a defect in replication checkpoint function.

Figures 4 and 5 demonstrate that AZD2858 can markedly enhance the cytotoxic and cytostatic effects of SN-38 and FOLFIRI through a combination of increased apoptosis and growth arrest according to dosage and treatment conditions. Figure 6 extends this analysis to cells cultured as spheroids, sometimes considered to better represent tumor responses compared to single cell cultures.

Significance:

Liquid phase separation of protein complexes is increasingly recognised as a fundamental mechanism in signal transduction and other cellular processes. One recent and important example was that of Topbp1, whose condensation in response to DNA damage is required for efficient activation of the ATR-Chk1 pathway. The current study asks a related but distinct question; can protein condensation be targeted by drugs to manipulate signalling pathways which in the main rely on protein kinase cascades?

Here, the authors identify an inhibitor of GSK3-beta as a novel inhibitor of DNA damage-induced Topbp1 condensation and thus of ATR-Chk1 signalling.

This work will be of interest to researchers in the fields of DNA damage signalling, biophysics of protein condensation, and cancer chemotherapy.

Comments on latest version:

Having read the revised manuscript and rebuttal I am satisfied that the authors have resolved my various original concerns through a combination of clarification/ explanation and textual changes necessary to make the description of certain data precise. My impression is that they have also largely or completely satisfied the concerns of the other reviewers, with the possible exception of reviewer 1's point about the relative toxicity of AZD and FOLFIRI in colorectal cancer cell lines versus the untransformed CCD841 cell line. This is of course an important point with respect to the possible practical application of this combination for cancer therapy, however this seems somewhat subsidiary to the main novelty and significance of the findings, which are that protein liquid phase separation/ condensation can be manipulated pharmacologically to modify signal transduction processes and that existing drugs can be re-purposed to this end.

Reviewer #3 (Public review):

Summary:

The authors have extended their previous research to develop TOPBP1 as a potential drug target for colorectal cancer by inhibiting its condensation. Utilizing an optogenetic approach, they identified the small molecule AZD2858, which inhibits TOPBP1 condensation and works synergistically with first-line chemotherapy to suppress colorectal cancer cell growth. The authors investigated the mechanism and discovered that disrupting TOPBP1 assembly inhibits the ATR/Chk1 signaling pathway, leading to increased DNA damage and apoptosis, even in drug-resistant colorectal cancer cell lines.

Comments on latest version:

This reviewer does not have further comments to the paper.

Reviewer #1 (Public review):

Summary:

The authors use Dyngo-4a, a known Dynami inhibitor to test its influence on caveolar assembly and surface mobility. They investigate whether it incorporates into membranes with Quartz-Crystal Microbalance, they investigate how it is organized in membranes using simulations. Finally, they use lipid-packing sensitive dyes to investigate lipid packing in the presence of Dyngo-4a, membrane stiffness using AFM and membrane undulation using fluorescence microscopy. They also use a measure they call "caveola duration time" to claim that something happens to caveolae after Dyngo-4a addition and using this parameter, they do indeed see an increase in it in response to Dyngo-4a, which is reduced back to the baseline after addition of cholesterol.

Overall, the authors claim: 1) Dyngo-4a inserts into the membrane and this 2) results in "a dramatic dynamin-independent inhibition of caveola scission". 3) Dyngo-4a was inserted and positioned at the level of cholesterol in the bilayer and 4) Dyngo-4a-treatment resulted in decreased lipid packing in the outer leaflet of the plasma membrane 5) but Dyngo-4a did not affect caveola morphology, caveolae-associated proteins, or the overall membrane stiffness 6) acute addition of cholesterol counteracts the block in caveola scission caused by Dyngo-4a.

Overall, in this reviewers opinion, claims 1, 3, 4, 5 are well-supported by the presented data from electron and live cell microscopy, QCM-D and AFM.

However, there is no convincing assay for caveolar endocytosis presented besides the "caveola duration" which although unclearly described seems to be the time it takes in imaging until a caveolae is not picked up by the tracking software anymore in TIRF microscopy.

Since the main claim of the paper is a mechanism of caveolar endocytosis being blocked by Dyngo-4a, a true caveolar internalization assay is required to make this claim. This means either the intracellular detection of not surface connected caveolar cargo or the quantification of caveolar movement from TIRF into epifluorescence detection in the fluorescence microscope. Otherwise, the authors could remove the claim and just claim that caveolar mobility is influenced.

Significance:

A number of small molecule inhibitors for the GTPase dynamics exist, that are commonly used tools in the investigation of endocytosis. This goes as far that the use of some of these inhibitors alone is considered in some publications as sufficient to declare a process to be dynamin-dependent. However, this is not correct, as there are considerable off-target effects, including the inhibition of caveolar internalization by a dynamin-independent mechanism. This is important, as for example the influence of dynamin small molecule inhibitors on chemotherapy resistance is currently investigated (see for example Tremblay et al., Nature Communications, 2020).

The investigation of the true effect of small molecules discovered as and used as specific inhibitors and their offside effects is extremely important and this reviewer applauds the effort. It is important that inhibitors are not used alone, but other means of targeting a mechanism are exploited as well in functional studies. The audience here thus is besides membrane biophysicists interested in the immediate effect of the small molecule Dyngo-4a also cell biologists and everyone using dynamic inhibitors to investigate cellular function.

Comments on revised version:

Please include the promised data on caveolar internalization and remove the above mentioned claim on membrane undulations from the text.

Reviewer #2 (Public review):

Summary:

In this manuscript, the authors probe the mechanisms by which Dyngo-4a, a dynamin inhibitor used to block endocytosis, disrupts caveolae dynamics. They provide compelling evidence that Dyngo-4a inhibits caveolae dynamics and endocytosis (as well as several other aspects of plasma membrane dynamics) by a dynamin-independent mechanism. They also provide strong computational and experimental data showing that Dyngo-4a inserts into membranes and decreases lipid packing in the outer leaflet of the plasma membrane. Finally, they demonstrate that the addition of excess cholesterol to cells reverses the effects of Dyngo-4a on caveolae dynamics, presumably by reversing lipid packing defects. Based on these findings they conclude that lipid packing regulates caveolae dynamics and endocytosis in a cholesterol-dependent manner.

This work should be of value to cell biologists interested in plasma membrane remodeling and membrane trafficking, biophysicists that study small molecule/membrane interactions and membrane remodeling processes, and chemists interested in designing drugs to target membrane trafficking machinery and pathways.

Strengths:

This work addresses the important topic of how a widely used endocytic inhibitor actually works. In the process of addressing this question, the authors uncover unexpected connections between how lipids are packed in cell membranes and membrane dynamics. The methods are appropriate and many of the claims made in this work are well supported by data.

Weaknesses:

I appreciate that the manuscript has already gone through one round of revisions and that many of the concerns from the previous reviewers appear to have been addressed. However, as an interested reader, I would like to offer several additional comments for the authors to consider.

(1) It is not clear based on the data presented whether the effects of Dyngo-4a on lipid packing give rise to defects in caveolae dynamics or if these effects are merely correlated. To show this more definitively, one might expect additional experimental approaches to be used to perturb lipid packing. I appreciate this is probably beyond the scope of the current study. However, it seems important for the manuscript to be clear about how far this interpretation can be pushed in the absence of additional independent lines of evidence.

(2) On a related note, it is not obvious how changes in lipid packing in the outer leaflet could impact caveolae dynamics. It would be helpful to include a cartoon illustrating how this might work.

(3) The authors note that Dyngo-4a inhibits several dynamic processes including generalized plasma membrane mobility (Fig 4A&B), transferrin uptake (Fig S4C), and fusion of fusogenic liposomes (Fig S4G). This clearly indicates there is a major disruption of the plasma membrane going on here that is not limited to caveolae. They go on to show that the addition of cholesterol reverses the effects of Dyngo-4a on caveolae dynamics. However, they do not discuss whether adding back cholesterol has similar effects on plasma membrane mobility and transferrin uptake. This information could help to further pinpoint whether the mechanisms of action are shared, and if the role of cholesterol is more general in controlling these events or is instead specific to caveolae.

(4) In Fig 4C, the morphology of the neck region of the Dyngo04a treated caveolae structure appears to be "pinched" compared to the control. I appreciate that more EM studies are underway. It would be useful to specifically compare the morphology of the caveolae as part of those studies.

(5) In Line 91, a statement is made that 8S complex formation requires cholesterol. This is debatable, as they appear to form in E. coli in the absence of cholesterol (reference 14).

Reviewer #1 (Public review):

Summary:

This study uses a novel DNA origami nanospring to measure the stall force and other mechanical parameters of the kinesin-3 family member, KIF1A, using light microscopy. The key is to use SNAP tags to tether a defined nanospring between a motor-dead mutant of KIF5B and the KIF1A to be integrated. The mutant KIF5B binds tightly to a subunit of the microtubule without stepping, thus creating resistance to the processive advancement of the active KIF1A. The nanospring is conjugated with 124 Cy3 dyes, which allows it to be imaged by fluorescence microscopy. Acoustic force spectroscopy was used to measure the relationship between the extension of the NS and force as a calibration. Two different fitting methods are described to measure the length of the extension of the NS from its initial diffraction-limited spot. By measuring the extension of the NS during an experiment, the authors can determine the stall force. The attachment duration of the active motor is measured from the suppression of lateral movement that occurs when the KIF1A is attached and moving. There are numerous advantages of this technology for the study of single molecules of kinesin over previous studies using optical tweezers. First, it can be done using simple fluorescence microscopy and does not require the level of sophistication and expense needed to construct an optical tweezer apparatus. Second, the force that is experienced by the moving KIF1A is parallel to the plane of the microtubule. This regime can be achieved using a dual beam optical tweezer set-up, but in the more commonly used single-beam set-up, much of the force experienced by the kinesin is perpendicular to the microtubule. Recent studies have shown markedly different mechanical behaviors of kinesin when interrogated by the two different optical tweezer configurations. The data in the current manuscript are consistent with those obtained using the dual-beam optical tweezer set-up. In addition, the authors study the mechanical behavior of several mutants of KIF1A that are associated with KIF1A-associated neurological disorder (KAND).

Strengths:

The technique should be cheaper and less technically challenging than optical tweezer microscopy to measure the mechanical parameters of molecular motors. The method is described in sufficient detail to allow its use in other labs. It should have a higher throughput than other methods.

Weaknesses:

The experimenter does not get a "real-time" view of the data as it is collected, which you get from the screen of an optical tweezer set-up. Rather, you have to put the data through the fitting routines to determine the length of the nanospring in order to generate the graphs of extension (force) vs time. No attempts were made to analyze the periods where the motor is actually moving to determine step-size or force-velocity relationships.

Reviewer #2 (Public review):

Summary:

This work is important because it complements other single-molecule mechanics approaches, in particular optical trapping, which inevitably exerts off-axis loads. The nanospring method has its own weaknesses (individual steps cannot be seen), but it brings new clarity to our picture of KIF1A and will influence future thinking on the kinesins-3 and on kinesins in general.

Strengths:

By tethering single copies of the kinesin-3 dimer under test via a DNA nanospring to a strong binding mutant dimer of kinesin-1, the forces developed and experienced by the motor are constrained into a single axis, parallel to the microtubule axis. The method is imaging-based, which should improve accessibility. In principle, at least, several single-motor molecules can be simultaneously tested. The arrangement ensures that only single molecules can contribute. Controls establish that the DNA nanospring is not itself interacting appreciably with the microtubule. Forces are convincingly calibrated, and reading the length of the nanospring by fitting to the oblate fluorescent spot is carefully validated. The excursions of the wild-type KIF1A leucine zipper-stabilised dimer are compared with those of neuropathic KIF1A mutants. These mutants can walk to a stall plateau, but the force is much reduced. The forces from mutant/WT heterodimers are also reduced.

Weaknesses:

The tethered nanospring method has some weaknesses; it only allows the stall force to be measured in the case that a stall plateau is achieved, and the thermal noise means that individual steps are not apparent. The nanospring does not behave like a Hookean spring - instead linearly increasing force is reported by exponentially smaller extensions of the nanospring under tension. The estimated stall force for Kif1A (3.8 pN) is in line with measurements made using 3-bead optical trapping, but those earlier measurements were not of a stall plateau, but rather of limiting termination (detachment) force, without a stall plateau. More confidence in the 3.7 pN stall plateau determined in the current work could be obtained by demonstrating that a stall at a higher force is obtained using the nanospring method on kinesin-1, which stalls at >7 pN in single bead optical trapping.

Reviewer #1 (Public review):

Summary:

It is well known that autophagosomes/autolysosomes move along microtubules. However, as these previous studies did not distinguish between autophagosomes and autolysosomes, it remains unknown whether autophagosomes begin to move after fusion with lysosomes or even before fusion. In this manuscript, the authors show using fusion-deficient vps16a RNAi cells that both pre-fusion autophagosomes and lysosomes can move along the microtubules towards the minus end. This was confirmed in snap29 RNAi cells. By screening motor proteins and Rabs, the authors found that autophagosomal traffic is primarily regulated by the dynein-dynactin system and can be counter-regulated by kinesins. They also show that Rab7-Epg5 and Rab39-ema interactions are important for autophagosome trafficking.

Strengths:

This study uses reliable Drosophila genetics and high-quality fluorescence microscopy. The data are properly quantified and statistically analyzed. It is a reasonable hypothesis that gathering pre-fusion autophagosomes and lysosomes in close proximity improves fusion efficiency.

Weaknesses:

(1) This study investigates the behavior of pre-fusion autophagosomes and lysosomes using fusion-incompetent cells (e.g., vps16a RNAi cells). However, the claim that these cells are truly fusion-incompetent relies on citations from previous studies. Since this is a foundational premise of the research, it should be rigorously evaluated before interpreting the data. It's particularly awkward that the crucial data for vps16a RNAi is only presented at the very end of Figure 10-S1; this should be among the first data shown (the same for SNAP29). It would be important to determine the extent to which autophagosomes and lysosomes are fusing (or tethered in close proximity), within each of these cell lines.

(2) In the new Figures 8 and 9, the authors analyze autolysosomes without knocking down Vps16A (i.e., without inhibiting fusion). However, as this reviewer pointed out in the previous round, it is highly likely that both autophagosomes and autolysosomes are present in these cells. This is particularly relevant given that the knockdown of dynein-dynactin, Rab7, and Epg5 only partially inhibits the fusion of autophagosomes and lysosomes (Figure 10H). If the goal is to investigate the effects of fusion, it would be more appropriate to analyze autolysosomes and autophagosomes separately. The authors mention that they can differentiate these two structures based on the size of mCherry-Atg8a structures. If this is the case, they should perform separate analyses for both autophagosomes and autolysosomes.

(3) This is also a continued Issue from the previous review. The authors suggest that autophagosome movement is crucial for fusion, based on the observed decrease in fusion rates in Rab7 and Epg5 knockdown cells (Fig. 10). However, this conclusion is not well supported. It is known that Rab7 and Epg5 are directly involved in the fusion process itself. Therefore, the possibility that the observed decrease is simply due to a direct defect in fusion, rather than an impairment of movement, has not been ruled out.

(4) The term "autolysosome maturation" appears multiple times, yet its meaning remains unclear. Does it refer to autolysosome formation (autophagosome-lysosome fusion), or does it imply a further maturation process occurring after autolysosome formation? This is not a commonly used term in the field, so it requires a clear definition.

(5) In Figure 1-S1D, the authors state that the disappearance of the mCherry-Atg8a signal after atg8a RNAi indicates that the observed structures are not non-autophagic vacuoles. This reasoning is inappropriate. Naturally, knocking down Atg8 will abolish its signal, regardless of the nature of the vacuoles. This does not definitively distinguish autophagic from non-autophagic structures.

Reviewer #2 (Public review):

Summary:

This manuscript by Boda et al. describes the results of a targeted RNAi screen in the background of Vps16A-depleted Drosophila larval fat body cells. In this background, lysosomal fusion is inhibited, allowing the authors to analyze the motility and localization specifically of autophagosomes, prior to their fusion with lysosomes to become autolysosomes. In this Vps16A-deleted background, mCherry-Atg8a labeled autophagosomes accumulate in the perinuclear area, through an unknown mechanism.

The authors found that depletion of multiple subunits of the dynein/dynactin complex caused an alternation of this mCherry-Atg8a localization, moving from the perinuclear region to the cell periphery. Interactions with kinesin overexpression suggest these motor proteins may compete for autophagosome binding and transport. The authors extended these findings by examining potential upstream regulators including Rab proteins and selected effectors, and they also examined effects on lysosomal movement and autolysosome size. Altogether, the results are consistent with a model in which specific Rab/effector complexes direct movement of lysosomes and autophagosomes toward the MTOC, promoting their fusion and subsequent dispersal throughout the cell.

Strengths:

Although previous studies of the movement of autophagic vesicles have identified roles for microtubule-based transport, this study moves the field forward by distinguishing between effects on pre- and post-fusion autophagosomes, and by its characterization of the roles of specific Dynein, Dynactin, and Rab complexes in regulating movement of distinct vesicle types. Overall, the experiments are well controlled, appropriately analyzed, and largely support the authors' conclusions..

Weaknesses:

One limitation of the study is the genetic background that serves as basis for the screen. In addition to preventing autophagosome-lysosome fusion, disruption of Vps16A has been shown to inhibit endosomal maturation and to block trafficking of components to the lysosome from both the endosome and Golgi apparatus. Additional effects previously reported by the authors include increased autophagosome production and reduced mTOR signaling. Thus Vps16A-depleted cells have a number of endosome, lysosome and autophagosome-related defects, with unknown downstream consequences. Additionally, the cause and significance of the perinuclear localization of autophagosomes in this background is unclear. Thus, interpretations of the observed reversal of this phenotype are difficult, and have the caveat that they may apply only to this condition, rather than to normal autophagosomes. Additional experiments to observe autophagosome movement or positioning in a more normal environment would improve the manuscript.

Comments on revision:

The revised manuscript and author responses have satisfactorily met my concerns. I have no further issues and congratulate the authors on this work.

Reviewer #3 (Public review):

Summary:

In multicellular organisms, autophagosomes are formed throughout the cytosol, while late endosomes/lysosomes are relatively enriched in the perinuclear region. It is known that autophagosomes gain access to the lysosome-enriched region by microtubule-based trafficking. The mechanism by which autophagosomes move along microtubules remains incompletely understood. In this manuscript, Péter Lőrincz and colleagues investigated the mechanism driving the movement of nascent autophagosomes along microtubule towards non-centrosomal microtubule organizing center (ncMTOC) using fly fat body as a model system. The authors took an approach by examining autophagosome positioning in cells where autophagosome-lysosome fusion was inhibited by knocking down the HOPS subunit Vps16A. Despite being generated at random positions in the cytosol, autophagosomes accumulate around the nucleus when Vps16A is depleted. They then performed an RNA interference screen to identify the factors involved in autophagosome positioning. They found that the dynein-dynactin complex is required for trafficking of autophagosomes toward ncMTOC. Dynein loss leads to the peripheral relocation of autophagosomes. They further revealed that a pair of small GTPases and their effectors, Rab7-Epg5 and Rab39-ema, are required for bidirectional autophagosome transport. Knockdown of these factors in Vps16a RNAi cells causes scattering of autophagosomes throughout the cytosol.

Strengths:

The data presented in this study help us to understand the mechanism underlying the trafficking and positioning of autophagosomes.

Weaknesses:

(1) The experiments were performed in Vps16A RNAi KD cells. Vps16A knockdown blocks fusion of vesicles derived from the endolysosomal compartments such as fusion between lysosomes. The pleiotropic effect of Vps16A RNAi may complicate the interpretation.

(2) In this study, the transport of autophagosomes is investigated in fly fat cells. In fat cells, a large number of large lipid droplets accumulate and the endomembrane systems are distinct from that in other cell types. The knowledge gain from this study may not apply to other cell types.

Reviewer #1 (Public review):

In this manuscript, the authors employ a combined proteomic and genetic approach to identify the glycoprotein QC factor malectin as an important protein involved in promoting coronavirus infection. Using proteomic approaches, they show that the non-structural protein NSP2 and malectin interact in the absence of viral infection, but not in the presence of viral infection. However, both NSP2 and malectin engage the OST complex during viral infection, with malectin also showing reduced interactions with other glycoprotein QC proteins. Malectin KD reduce replication of coronaviruses, including SARS-COV2. Collectively, these results identify Malectin as a glycoprotein QC protein involved in regulating coronavirus replication that could potentially be targeted to mitigate coronavirus replication.

In the revised manuscript, the authors have addressed many of my comments from the previous submission. Notably, they've provided some additional mechanistic data, focused primarily on the activation of different stress signaling pathways, to help define malectin impacts viral replication, although this is mostly suggests that activation of these pathways may not be the main mechanism of malectin-dependent reductions in viral replication. Regardless, I'm sure this mechanism will be the focus of continued efforts on this project. They have also addressed other concerns related to interactions between OST and malectin, as well as the curious interactions between non-structural proteins with both ER and mitochondrial proteins. Overall, the authors have been responsive to my comments and comments from other reviewers, and the manuscript has been improved. It will be a good addition to eLife.

Reviewer #3 (Public review):

Summary:

In their revised manuscript, the authors addressed most of the reviewers' concerns. One concern was the emphasis on increased MLEC-OST interactions during infection, which the authors toned down in the revision. They clarified that MLEC interaction with OST is maintained-rather than increased-during infection, while its interaction with other QC factors decreases. They also added context and discussion of the co-localization of viral proteins with ER and mitochondrial proteins, noting that both nsp2 and MLEC localize to mitochondria-associated membranes (MAMs), providing a plausible explanation for these interactions.

Another concern involved the effects of MLEC KD on the cellular environment. To address this, the authors analyzed stress pathway activation and glycosylation of endogenous proteins in MLEC KD cells. They found only modest upregulation of the HSF1 pathway and no changes in the UPR or other stress responses, suggesting MLEC KD does not broadly disrupt ER proteostasis. Additionally, glycopeptide profiling showed only minor changes in host protein glycosylation, supporting a more direct role for MLEC in viral replication rather than general host glycoprotein disruption.

However, some weaknesses remain. Direct interaction between MLEC and nsp2 during infection was not detected, and the identified viral glycopeptides were limited to only five Spike sites. Furthermore, the mechanism by which MLEC promotes viral replication is still unclear.

In summary, the authors strengthened the manuscript by addressing reviewers' concerns through additional data, clarified language, and expanded discussion. While the overall support for MLEC's pro-viral role is solid, its precise mechanism of action remains speculative. Future work will be needed to directly link MLEC's activity to specific steps in viral protein biogenesis and replication.

Original summary: In this study, Davies and Plate set out to discover conserved host interactors of coronavirus non-structural proteins (Nsp). They used 293T cells to ectopically express flag-tagged Nsp2 and Nsp4 from five human and mouse coronaviruses, including SARS-CoV-1 and 2, and analyzed their interaction with host proteins by affinity purification mass-spectrometry (AP-MS). To confirm whether such interactors play a role in coronavirus infection, the authors measured the effects of individual knockdowns on replication of murine hepatitis virus (MHV) in mouse Delayed Brain Tumor cells. Using this approach, they identified a previously undescribed interactor of Nsp2, Malectin (Mlec), which is involved in glycoprotein processing and shows a potent pro-viral function in both MHV and SARS-CoV-2. Although the authors were unable to confirm this interaction in MHV-infected cells, they show that infection remodels many other Mlec interactions, recruiting it to the ER complex that catalyzes protein glycosylation (OST). Mlec knockdown reduced viral RNA and protein levels during MHV infection, although such effects were not limited to specific viral proteins. However, knockdown reduced the levels of five viral glycopeptides that map to Spike protein, suggesting it may be affected by Mlec.

Strengths:

This is an elegant study that uses a state-of-the-art quantitative proteomic approach to identify host proteins that play critical roles in viral infection. Instead of focusing on a single protein from a single virus, it compares the interactomes of two viral proteins from five related viruses, generating a high confidence dataset. The functional follow-ups using multiple live and reporter viruses, including MHV and CoV2 variants, convincingly depict a pro-viral role for Mlec, a protein not previously implicated in coronavirus biology.

Weaknesses:

Although a commonly used approach, AP-MS of ectopically expressed viral proteins may not accurately capture infection-related interactions. The authors observed Mlec-Nsp2 interactions in transfected 293T cells (1C) but were unable to reproduce those in mouse cells infected with MHV (3C). EIF4E2/GIGYF2, two bonafide interactors of CoV2 Nsp2 from previous studies, are listed as depleted compared to negative controls (S1D). Most other CoV2 Nsp2 interactors are also depleted by the same analysis (S1D). Previously reported MERS Nsp2 interactors, including ASCC1 and TCF25, are also not detected (S1D). Furthermore, although GIGYF2 was not identified as an interactor of MHV Nsp2/4 in human cells (S1D), its knockdown in mouse cells reduced MHV titers about 1000 fold (S4). The authors should attempt to explain these discrepancies.

More importantly, the authors were unable to establish a direct link between Mlec and the biogenesis of any viral or host proteins, by mass-spectrometry or otherwise. Although it is clear that Mlec promotes coronavirus infection, the mechanism remains unclear. Its knockdown does not affect the proteome composition of uninfected cells (S15B), suggesting it is not required for proteome maintenance under normal conditions. The only viral glycopeptides detected during MHV infection originated from Spike (5D), although other viral proteins are also known to be glycosylated. Cells depleted for Mlec produce ~4-fold less Spike protein (4E) but no more than 2-fold less glycosylated spike peptides (5D), compounding the interpretation of Mlec effects on viral protein biogenesis. Furthermore, Spike is not essential for the pro-viral role of Mlec, given that Mlec knockdown reduces replication of SARS-CoV-2 replicons that express all viral proteins except for Spike (6A/B).

Any of the observed effects on viral protein levels could be secondary to multiple other processes. Interventions that delay infection for any reason could lead to imbalance of viral protein levels, because Spike and other structural proteins are produced at a much higher rate than non-structural proteins due to the higher abundance of their cognate subgenomic RNAs. Similarly, the observation that Mlec depletion attenuates MHV-mediated changes to the host proteome (S15C/D) can also be attributed to indirect effects on viral replication, regardless of glycoprotein processing. In the discussion, the authors acknowledge that Mlec may indirectly affect infection through modulation of replication complex formation or ER stress, but do not offer any supporting evidence. Interestingly, plant homologs of Mlec are implicated in innate immunity, favoring a more global role for Mlec in mammalian coronavirus infections.

Finally, the observation that both Nsp2 (3C) and Mlec (3E/F) are recruited to the OST complex during MHV infection neither support nor refute any of these alternate hypotheses, given that Mlec is known to interact with OST in uninfected cells and that Nsp2 may interact with OST as part of the full length unprocessed Orf1a, as it co-translationally translocates into the ER.

Therefore, the main claims about the role of Mlec in coronavirus protein biogenesis are only partially supported.

Comments on revisions:

Figure 7B should be revised to show that MLEC maintains interactions with rather than recruited to the OST.

Reviewer #1 (Public review):

Summary:

The authors were attempting to identify the molecular and cellular basis for why modulators of the HR pathway, specifically PARPi, are not effective in CDK12 deleted or mutant prostate cancers and they seek to identify new therapeutic agents to treat this subset of metastatic prostate cancer patients. Overall, this is an outstanding manuscript with a number of strengths and in my opinion represents a significant advance in the field of prostate cancer biology and experimental therapeutics.

Strengths:

The patient data cohort size and clinical annotation from Figure 1 are compelling and comprehensive in scope. The associations between tandem duplications and amplifications of oncogenes that have been well-credentialed to be drivers of cancer development and progression are fascinating and the authors identify that in those that have AR amplification for example, there is evidence for AR pathway activation. The association between CDK12 inactivation and various specific gene/pathway perturbations is fascinating and is consistent with previously published studies - it would be interesting to correlate these changes with cell line-based studies in which CDK12 is specifically deleted or inhibited with small molecules to see how many pathways/gene perturbations are shared between the clinical samples and cell and mouse models with CDK12 perturbation. The short-term inhibitor studies related to changes in HRD genes and protein expression with CDK12/13 inhibition are fascinating and suggest differential pathway effects between short inhibition of CDK12/13 and long-term loss of CDK12. The in vivo studies with the inhibitor of CDK12/13 are intriguing but not definitive

Weaknesses:

Given that there are different mutations identified at different CDK12 sites as illustrated in Figure 1B it would be nice to know which ones have been functionally classified as pathogenic and for which ones that the pathogenicity has not been determined. This would be especially interesting to perform in light of the differences in the LOH scores and WES data presented - specifically, are the pathogenic mutations vs the mutations for which true pathogenicity is unknown more likely to display LOH or TD? For the cell inhibition studies with the CDK12/13 inhibitor, more details characterizing the specificity of this molecule to these targets would be useful. Additionally, could the authors perform short-term depletion studies with a PROTAC to the target or short shRNA or non-selected pool CRISPR deletion studies of CDK12 in these same cell lines to complement their pharmacological studies with genetic depletion studies? Also perhaps performing these same inhibitor studies in CDK12/13 deleted cells to test the specificity of the molecule would be useful. Additionally, expanding these studies to additional prostate cancer cell lines or organdies models would strengthen the conclusions being made. More information should be provided about the dose and schedule chosen and the rationale for choosing those doses and schedules for the in vivo studies proposed should be presented and discussed. Was there evidence for maximal evidence of inhibition of the target CDK12/13 at the dose tested given the very modest tumor growth inhibition noted in these studies?

Reviewer #2 (Public review):

Summary:

The study explores the functional consequence of CDK12 loss in prostate cancer. While CDK12 loss has been shown to confer homologous recombination (HR) deficiency through premature intronic polyadenylation of HR genes, the response of PARPi monotherapy has failed. This study therefore performed an in-depth analysis of genomic sequencing data from mCRPC patient tumors, and showed that tumors with CDK12 loss lack pertinent HR signatures and scars. Furthermore, functional exploration in human prostate cancer cell lines showed that while the acute inhibition of CDK12 resulted in aberrant polyadenylation of HR genes like BRCA1/2, HR-specific effects were overall modest or absent in cell lines or xenografts adapted to chronic CDK12 loss. Instead, vulnerability to genetically targeting CDK13 resulted in a synthetic lethality in tumors with CDK12 loss, as shown in vivo with SR4825, a CDK12/13 inhibitor - thus serving as a potential therapeutic avenue.

The evidence supporting this study is based on in-depth genomic analyses of human patients, acute knockdown studies of CDK12 using a CDK12/13 inhibitors SR4835, adaptive knockout of CDK12 using LuCaP 189.4_CL and inducible re-expression of CDK12, CDK12 single clones in 22Rv1 (KO2 and KO5) and Skov3 (KO1), Tet-inducible knockdown of BRCA2 or CDK12 followed by ionizing radiation and measurement of RAD51 foci, lack of sensitivity generally to PARPi and platinum chemotherapy in cells adapted to CDK12 loss, loss of viability of CDK13 knockout in CDK12 knockout cells, and in vivo testing of SE4825 in LuCaP xenografts with intact and CDK12 loss.

Strengths:

Overall, this study is robust and of interest to the broader homologous recombination and CDK field. First, the topic is clinically relevant given the lack of PARPi response in CDK12 loss tumors. Second, the strength of the genomic analysis in CDK12 lost PCa tumors is robust with clear delineation that BRCA1/2 genes and maintenance of most genes regulating HR are intact. Specifically, the authors find that there is no mutational signature or genomic features suggestive of HR, such as those found in BRCA1/2 tumors. Lastly, novel lines are generated in this study, including de novo LuCaP 189.4_CL with CDK12 loss that can be profound for potential synthetic lethalities.

Weakness:

One caveat that continues to be unclear as presented, is the uncoupling of cell cycle/essentiality of CDK12/13 from HR-directed mechanisms. Is this purely a cell cycle arrest phenotype acutely with associated down-regulation of many genes?

While the RAD51 loading ssRNA experiments are informative, the Tet-inducible knockdown of BRCA2 and CDK12 is confusing as presented in Figure 5, shBRCA2 + and -dox are clearly shown. However, were the CDK12_K02 and K05 also knocked down using inducible shRNA or a stable knockout? The importance of this statement is the difference between acute and chronic deletion of CDK12. Previously, the authors showed that acute knockdown of CDK12 led to an HR phenotype, but here it is unclear whether CDK12-K02/05 are acute knockdowns of CDK12 or have been chronically adapted after single cell cloning from CRISPR-knockout.

Given the multitude of lines, including some single-cell clones with growth inhibitory phenotypes and ex-vivo derived xenografts, the variability of effects with SR4835, ATM, ATR, and WEE1 inhibitors in different models can be confusing to follow. Overall, the authors suggest that the cell lines differ in therapeutic susceptibility as they may have alternate and diverse susceptibilities. It may be possible that the team could present this more succinctly and move extraneous data to the supplement.

The in-vitro data suggests that SR4835 causes growth inhibition acutely in parental lines such as 22RV1. However, in vivo, tumor attenuation appears to be observed in both CDK12 intact and deficient xenografts, LuCAP136 and LuCaP 189.4 (albeit the latter is only nominally significant). Is there an effect of PARPi inhibition specifically in either model? What about the the 22RV1-K02/05? Do these engraft? Given the role of CDK12/13 in RNAP II, these data might suggest that the window of susceptibility in CDK12 tumors may not be that different from CDK12 intact tumors (or intact tissue) when using dual CDK12/13 inhibitors but rather represent more general canonical essential functions of CDK12 and CDK13 in transcription. From a therapeutic development strategy, the authors may want to comment in the discussion on the ability to target CDK13 specifically.

Reviewer #3 (Public review):

Significance:

About 5% of metastatic castration-resistant prostate cancers (mCRPC) display genomic alterations in the transcriptional kinase CDK12. The mechanisms by which CDK12 alterations drive tumorigenesis in this molecularly-defined subset of mCRPC have remained elusive. In particular, some studies have suggested that CDK12 loss confers a homologous recombination deficiency (HRd) phenotype, However, clinical studies have not borne out the benefit to PARP inhibitors in patients with CDK12 alterations, despite the fact that these agents are typically active against tumors with HRd.

In this study, Frank et al. reconcile these findings by showing that: (1) tumors with biallelic CDK12 alterations do not have genomic features of HRd; (2) in vitro, HR gene downregulation occurs with acute depletion of CDK12 but is far less pronounced with chronic CDK12 loss; (3) CDK12-altered cells are uniquely sensitive to genetic or pharmacologic inhibition of CDK13.

Strengths:

Overall, this is an important study that reconciles disparate experimental and clinical observations. The genomic analyses are comprehensive and conducted with a high degree of rigor and represent an important resource to the community regarding the features of this molecular subtype of mCRPC.

Weaknesses:

(1) It is generally assumed that CDK12 alterations are inactivating, but it is noteworthy that homozygous deletions are comparatively uncommon (Figure 1a). Instead many tumors show missense mutations on either one or both alleles, and many of these mutations are outside of the kinase domain (Figure 1b). It remains possible that the CDK12 alterations that occur in some tumors may retain residual CDK12 function, or may confer some other neomorphic function, and therefore may not be accurately modeled by CDK12 knockout or knockdown in vitro. This would also reconcile the observation that knockout of CDK12 is cell-essential while the human genetic data suggest that CDK12 functions as a tumor suppressor gene.

(2) It is not entirely clear whether CDK12 altered tumors may require a co-occurring mutation to prevent loss of fitness, either in vitro or in vivo (e.g. perhaps one or more of the alterations that occur as a result of the TDP may mitigate against the essentiality of CDK12 loss).

Reviewer #1 (Public review):

Summary:

Hurtado et al. show that Sox9 is essential for retinal integrity, and its null mutation causes the loss of the outer nuclear layer (ONL). The authors then show that this absence of the ONL is due to apoptosis of photoreceptors and a reduction in the numbers of other retinal cell types such as ganglion cells, amacrine cells and horizontal cells. They also describe that Müller Glia undergoes reactive gliosis by upregulating the Glial Fibrillary Acidic Protein. The authors then show that Sox9+ progenitors proliferate and differentiate to generate the corneal cells through Sox9 lineage-tracing experiments. They validate Sox9 expression and characterize its dynamics in limbal stem cells using an existing single-cell RNA sequencing dataset. Finally, the authors show that Sox9 deletion causes progenitor cells to lose their clonogenic capacity by comparing the sizes of control and Sox9-null clones. Overall, Hurtado et al. underline the importance of Sox9 function in retinal cells.

Strengths:

The authors have characterized a myriad of striking phenotypes due to Sox9 deletion in the retina and limbal stem cells which will serve as a basis for future studies.

Weaknesses:

Hurtado et al. highlight the importance of Sox9 in the retina and limbal stem cells by describing several affects of Sox9 depletion in the adult eye. However, it is unclear how or where Sox9 precisely acts as a mechanistic investigation of the transcription factor's role in this tissue is lacking.

Reviewer #2 (Public review):

Summary:

Sox9 is a transcription factor crucial for development and tissue homeostasis, and its expression continues in various adult eye cell types, including retinal pigmented epithelium cells, Müller glial cells, and limbal and corneal basal epithelia. To investigate its functional roles in the adult eye, this study employed inducible mouse mutagenesis. Adult-specific Sox9 depletion led to severe retinal degeneration, including the loss of Müller glial cells and photoreceptors. Further, lineage tracing revealed that Sox9 is expressed in a basal limbal stem cell population that supports stem cell maintenance and homeostasis. Mosaic analysis confirmed that Sox9 is essential for the differentiation of limbal stem cells. Overall, the study highlights that Sox9 is critical for both retinal integrity and the differentiation of limbal stem cells in the adult mouse eye.

Strengths:

In general, inducible genetic approaches in the adult mouse nervous system are rare and difficult to carry out. Here, the authors employ tamoxifen-inducible mouse mutagenesis to uncover the functional roles of Sox9 in the adult mouse eye.

Careful analysis suggests that two degeneration phenotypes (mild and severe) are detected in the adult mouse eye upon tamoxifen-dependent Sox9 depletion. Phenotype severity nicely correlates with the efficiency of Cre-mediated Sox9 depletion.

Molecular marker analysis provides strong evidence of Mueller cell loss and photoreceptor degeneration.

A clever genetic tracing strategy uncovers a critical role for Sox9 in limbal stem cell differentiation.

Comments on revised submission:

The revised manuscript is very much improved and has addressed all my concerns.

Reviewer #1 (Public review):

Summary:

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 staring 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:

- 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.

- 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 evaluation of future returns.

Weakness:

- 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.

- It is currently unclear how (whether) the proposed model corresponds to neurobiological (rather than behavioral) findings, different from the analysis by Akiti et al.

Comments on revisions:

The authors have adequately replied to all the concerns that I raised in my review of the original manuscript. I do not have any remaining concern, and I am now more convinced that this work provides novel important insights and stimulates future experimental and theoretical examinations.

Reviewer #3 (Public review):

Summary:

The manuscript presents computational modelling of the behaviour of mice during encounters with novel and familiar objects, originally reported in Akiti et al. (Neuron 110, 2022). Mice typically perform short bouts of approach followed by retreat to a safe distance, presumably to balance exploration to discover possible reward 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:

- Individual differences in exploratory behaviour are an interesting, important, and under-studied topic.

- 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.

- Thoughtful discussion of the results in the context of prior literature.

Limitations:

- 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.

Comments on revisions:

All recommendations to authors from the first review were addressed in the revised manuscript.

Editorial note: To ensure a thorough evaluation of the revised manuscript, we invited a third reviewer to assess whether the authors had sufficiently addressed the concerns raised in the initial round of peer review. This additional reviewer confirmed that the authors responded partially to the original reviewers requests. While he/she also provided a set of new comments, these do not alter the original assessment or editorial decision regarding the manuscript. For transparency and completeness, the additional comments are included below.

Reviewer #3 (Public Review):

Summary:

In this manuscript, Li and coworkers present experiments generated with human induced pluripotent stem cells (iPSCs) differentiated to astrocytes through a three-step protocol consisting of neural induction/midbrain patterning, switch to expansion of astrocytic progenitors, and terminal differentiation to astroglial cells. They used lineage tracing with a LMX1A-Cre/AAVS1-BFP iPSCs line, where the initial expression of LMX1A and Cre allows the long-lasting expression of BFP, yielding BFP+ and BFP- populations, that were sorted when in the astrocytic progenitor expansion. BFP+ showed significantly higher number of cells positive to NFIA and SOX9 than BFP- cells, at 45 and 98 DIV. However, no significant differences in other markers such as AQP4, EAAT2, GFAP (which show a proportion of less than 10% in all cases) and S100B were found between BFP-positive or -negative, at these differentiation times. Intriguingly, non-patterned astrocytes produced higher proportions of GFAP positive cells than the midbrain-induced and then sorted populations. BFP+ cells have enhanced calcium responses after ATP addition, compared to BFP- cells. Single-cell RNA-seq of early and late cells from BFP- and BFP+ populations were compared to non-patterned astrocytes and neurons differentiated from iPSCs. Bioinformatic analyses of the transcriptomes resulted in 9 astrocyte clusters, 2 precursor clusters and one neuronal cluster. DEG analysis between BFP+ and BFP- populations showed some genes enriched in each population, which were subject to GO analysis, resulting in biological processes that are different for BFP+ or BFP- cells.

Strengths:

The manuscript tries to tackle an important aspect in Neuroscience, namely the importance of patterning in astrocytes. Regionalization is crucial for neuronal differentiation and the presented experiments constitute a trackable system to analyze both transcriptional identities and functionality on astrocytes.

Weaknesses:

The presented results have several fundamental issues, to be resolved, as listed in the following major points:

(1) It is very intriguing that GFAP is not expressed in late BFP- nor in BFP+ cultures, when authors designated them as mature astrocytes.<br /> (2) In Fig. 2D, authors need to change the designation "% of positive nuclei".<br /> (3) In Fig. 2E, the text describes a decrease caused by 2APB on the rise elicited by ATP, but the graph shows an increase with ATP+2APB. However, in Fig. 2F, the peak amplitude for BFP+ cells is higher in ATP than in ATP+2APD, which is mentioned in the text, but this is inconsistent with the graph in 2E.<br /> (4) The description of Results in the single-cell section is confusing, particularly in the sorted CD49 and unsorted cultures. Where do these cells come from? Are they BFP-, BFP+, unsorted for BFP, or non-patterned? Which are the "all three astrocyte populations"? A more complete description of the "iPSC-derived neurons" is required in this section to allow the reader to understand the type and maturation stage of neurons, and if they are patterned or not.<br /> (5) A puzzling fact is that both BFP- and BFP- cells have similar levels of LMX1A, as shown in Fig. S6F. How do authors explain this observation?<br /> (6) In Fig. 3B, the non-patterned cells cluster away from the BFP+ and BFP-; on the other hand, early and late BFP- are close and the same is true for early and late BFP+. A possible interpretation of these results is that patterned astrocytes have different paths for differentiation, compared to non-patterned cells. If that can be implied from these data, authors should discuss the alternative ways for astrocytes to differentiate.<br /> (7) Fig. 3D shows that cluster 9 is the only one with detectable and coincident expression of both S100B and GFAP expression. Please discuss why these widely-accepted astrocyte transcripts are not found in the other astrocytes clusters. Also, Sox9 is expressed in neurons, astrocyte precursors and astrocytes. Why is that?<br /> (8) Line 337, Why authors selected a log2 change of 0.25? Typically, 1 or a higher number is used to ensure at least a 2-fold increase, or a 50% decrease. A volcano plot generated by the comparison of BFP+ with BFP- cells would be appropriate. The validation of differences by immunocytochemistry, between BFP+ and BFP-, is inconclusive. The staining is blur in the images presented in Fig. S8C. Quantification of the positive cells, without significant background signal, in both populations is required.<br /> (9) Lines 349-351: BFP+ cells did not show higher levels of transcripts for LMX1A nor FOXA2. This fact jeopardizes the claim that these cells are still patterned. In the same line, there are not significant differences with cortical astrocytes, indicating a wider repertoire of the initially patterned cells, that seems to lose the midbrain phenotype. Furthermore, common DGE shared by BFP- and BFP+ cells when compared to non-patterned cells indicate that after culture, the pre-pattern in BFP+ cells is somehow lost, and coincides with the progression of BFP- cells.<br /> (10) For the GO analyses, How did authors select 1153 genes? The previous section mentioned 287 genes unique for BFP+ cells. The Results section should include a rationale for performing a wider search for the enriched processes.<br /> (11) For Fig. 4C and 4D, both p values and the number of genes should be indicated in the graph. I would advise to select the 10 or 15 most significant categories, these panels are very difficult to read. Whereas the listed processes for BFP+ have a relation to Parkinson disease, the ones detected for BFP- cells are related to extracellular matrix and tissue development. Does it mean that BFP+ cells have impaired formation of this matrix, or defective tissue development? This is in contradiction of enhanced calcium responses of BFP+ cells compared to BFP- cells.<br /> (12) Both the comparison between midbrain and cortical astrocytes in Fig. S8A, and the volcano plot in S8B do not show consistent changes. For example, RCAN2 in Fig. S8A has the same intensity for cortical and midbrain cells, but is marked as an enriched gene in midbrain in the p vs log2FC graph in Fig. S8B.

Reviewer #1 (Public review):

This study elucidates the molecular linkage between the mobilization of damaged rDNA from the nucleolus to its periphery and the subsequent repair process by HDR. The authors demonstrate that the nucleolar adaptor protein Treacle mediates rDNA mobilization, and the MDC1-RNF8-RNF168 pathway coordinates the recruitment of the BRCA1-PALB2-BRCA2 complex and RAD51 loading. This stepwise regulation appears to prevent aberrant recombination events between rDNA repeats. This work provides compelling evidence for the recruitment of the Treacle-TOPBP1-NBS1 complex to rDNA DSBs and demonstrates the critical role of MDC1 in the rDNA damage response. There are some issues with the over-interpretation of results as described subsequently. Some aspects could be strengthened, for example, a potential role of the RAP80-Abraxas axis, the origin of the repair synthesis (HDR vs. NHEJ)

Reviewer #2 (Public review):

Summary:

DNA double-strand breaks (DSB) in repeated DNA pose a challenge for repair by homologous recombination (HR) due to the potential of generating chromosomal aberrations, especially involving repeats on different chromosomes. This conceptual caveat led to a long-held notion that HR is not active in repeated DNA, which was disproven in groundbreaking work by Chiolo showing in Drosophila that DSBs in pericentromeric repeats are mobilized to the nuclear periphery for repair by HR. A similar mechanism operates in mouse cells, as shown by the Gautier laboratory, but the mobilization goes to the nucleolar periphery, called nucleolar caps. In this manuscript, the authors reexamine the role of MDC1 in the mobilization of DSBs in rDNA in human cells. Previous work has shown that MDC1 is replaced by Treacle, the gene associated with Treacher Collins syndrome 1, in its role as the main adaptor of the DNA damage response, and these results are confirmed here. The novelty of this contribution lies in the discovery that MDC1 is required downstream in the recruitment of BRCA1 and RAD51 to nucleolar DSBs that were mobilized to the nucleolar cap. Using multiple MCD knockout models and DSBs induced by the nuclease PpoI, which cleaves at nuclear sites as well as in the 28S rDNA, convincingly documents this role of MDC1 and shows that it acts upstream of the RNF8-RNF168 ubiquitylation axis. Using a proxy assay of co-localization of EdU incorporation at DSBs (gammaH2AX), evidence is provided that MDC1 is required for HR in rDNA. MDC1 was not required for RAD51 recruitment to IR-induced foci, but it is unclear whether this is related to the different DSB chemistry (enzymatic versus IR) or to the localization of the DSB (rDNA versus unique sequence genome).

Strengths:

(1) The manuscript is well-written, and the experimental evidence is nicely presented.

(2) Multiple MDC1 knockout models are used to validate the results.

(3) Convincing back-complementation data clarify the relationship between MDC1 and RNF8.

Weaknesses:

(1) The recruitment of BRCA2 was not directly demonstrated. This caveat could be recognized, as IF for BRCA2 is challenging.

(2) PpoI also induces DSBs in the non-rDNA genome. These DSBs would be an ideal control to establish nucleolar specificity of the events described and clarify whether the difference between IR and PpoI is the chemical structure of the DSB or the location of the DSB.

Reviewer #1 (Public review):

The authors present an approach that uses the transformer architecture to model epistasis in deep mutational scanning datasets. This is an original and very interesting idea. Applying the approach to 10 datasets, they quantify the contribution of higher-order epistasis, showing that it varies quite extensively.

Suggestions:

(1) The approach taken is very interesting, but it is not particularly well placed in the context of recent related work. MAVE-NN, LANTERN, and MoCHI are all approaches that different labs have developed for inferring and fitting global epistasis functions to DMS datasets. MoCHI can also be used to infer multi-dimensional global epistasis (for example, folding and binding energies) and also pairwise (and higher order) specific interaction terms (see 10.1186/s13059-024-03444-y and 10.1371/journal.pcbi.1012132). It doesn't distract from the current work to better introduce these recent approaches in the introduction. A comparison of the different capabilities of the methods may also be helpful. It may also be interesting to compare the contributions to variance of 1st, 2nd, and higher-order interaction terms estimated by the Epistatic transformer and MoCHI.

(2) https://doi.org/10.1371/journal.pcbi.1004771 is another useful reference that relates different metrics of epistasis, including the useful distinction between biochemical/background-relative and background-averaged epistasis.

(3) Which higher-order interactions are more important? Are there any mechanistic/structural insights?

Reviewer #2 (Public review):

Summary:

This paper presents a novel transformer-based neural network model, termed the epistatic transformer, designed to isolate and quantify higher-order epistasis in protein sequence-function relationships. By modifying the multi-head attention architecture, the authors claim they can precisely control the order of specific epistatic interactions captured by the model. The approach is applied to both simulated data and ten diverse experimental deep mutational scanning (DMS) datasets, including full-length proteins. The authors argue that higher-order epistasis, although often modest in global contribution, plays critical roles in extrapolation and capturing distant genotypic effects, especially in multi-peak fitness landscapes.

Strengths:

(1) The study tackles a long-standing question in molecular evolution and protein engineering: "how significant are epistatic interactions beyond pairwise effects?" The question is relevant given the growing availability of large-scale DMS datasets and increasing reliance on machine learning in protein design.

(2) The manuscript includes both simulation and real-data experiments, as well as extrapolation tasks (e.g., predicting distant genotypes, cross-ortholog transfer). These well-rounded evaluations demonstrate robustness and applicability.

(3) The code is made available for reproducibility.

Weaknesses:

(1) The paper mainly compares its transformer models to additive models and occasionally to linear pairwise interaction models. However, other strong baselines exist. For example, the authors should compare baseline methods such as "DANGO: Predicting higher-order genetic interactions". There are many works related to pairwise interaction detection, such as: "Detecting statistical interactions from neural network weights", "shapiq: Shapley interactions for machine learning", and "Error-controlled non-additive interaction discovery in machine learning models".

(2) While the transformer architecture is cleverly adapted, the claim that it allows for "explicit control" and "interpretability" over interaction order may be overstated. Although the 2^M scaling with MHA layers is shown empirically, the actual biological interactions captured by the attention mechanism remain opaque. A deeper analysis of learned attention maps or embedding similarities (e.g., visualizations, site-specific interaction clusters) could substantiate claims about interpretability.

(3) The distinction between nonspecific (global) and specific epistasis is central to the modeling framework, yet it remains conceptually underdeveloped. While a sigmoid function is used to model global effects, it's unclear to what extent this functional form suffices. The authors should justify this choice more rigorously or at least acknowledge its limitations and potential implications.

(4) The manuscript refers to "pairwise", "3-4-way", and ">4-way" interactions without always clearly defining the boundaries of these groupings or how exactly the order is inferred from transformer layer depth. This can be confusing to readers unfamiliar with the architecture or with statistical definitions of interaction order. The authors should clarify terminology consistently. Including a visual mapping or table linking a number of layers to the maximum modeled interaction order could be helpful.

Reviewer #3 (Public review):

Summary:

Sethi and Zou present a new neural network to study the importance of epistatic interactions in pairs and groups of amino acids to the function of proteins. Their new model is validated on a small simulated data set and then applied to 10 empirical data sets. Results show that epistatic interactions in groups of amino acids can be important to predict the function of a protein, especially for sequences that are not very similar to the training data.

Strengths:

The manuscript relies on a novel neural network architecture that makes it easy to study specifically the contribution of interactions between 2, 3, 4, or more amino acids. The study of 10 different protein families shows that there is variation among protein families.

Weaknesses:

The manuscript is good overall, but could have gone a bit deeper by comparing the new architecture to standard transformers, and by investigating whether differences between protein families explain some of the differences in the importance of interactions between amino acids. Finally, the GitHub repository needs some more information to be usable.

Reviewer #1 (Public review):

Summary:

This manuscript uses adaptive sampling simulations to understand the impact of mutations on the specificity of the enzyme PDC-3 β-lactamase. The authors argue that mutations in the Ω-loop can expand the active site to accommodate larger substrates.

Strengths:

The authors simulate an array of variants and perform numerous analyses to support their conclusions.

The use of constant pH simulations to connect structural differences with likely functional outcomes is a strength.

Weaknesses:

I would like to have seen more error bars on quantities reported (e.g., % populations reported in the text and Table 1).

Reviewer #1 (Public review):

Summary:

This manuscript uses adaptive sampling simulations to understand the impact of mutations on the specificity of the enzyme PDC-3 β-lactamase. The authors argue that mutations in the Ω-loop can expand the active site to accommodate larger substrates.

Strengths:

The authors simulate an array of variants and perform numerous analyses to support their conclusions.

The use of constant pH simulations to connect structural differences with likely functional outcomes is a strength.

Weaknesses:

I would like to have seen more error bars on quantities reported (e.g., % populations reported in the text and Table 1).

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.

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.

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.

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.

Reviewer #1 (Public review):

Summary:

Frelih et al. investigated both periodic and aperiodic activity in EEG during working memory tasks. In terms of periodic activity, they found post-stimulus decreases in alpha and beta activity, while in terms of aperiodic activity, they found a bi-phasic post-stimulus steepening of the power spectrum, which was weakly predictive of performance. They conclude that it is crucial to properly distinguish between aperiodic and periodic activity in event-related designs as the former could confound the latter. They also add to the growing body of research highlighting the functional relevance of aperiodic activity in the brain.

Strengths:

This is a well-written, timely paper that could be of interest to the field of cognitive neuroscience, especially to researchers investigating the functional role of aperiodic activity. The authors describe a well-designed study that looked at both the oscillatory and non-oscillatory aspects of brain activity during a working memory task. The analytic approach is appropriate, as a state-of-the-art toolbox is used to separate these two types of activity. The results support the basic claim of the paper that it is crucial to properly distinguish between aperiodic and periodic activity in event-related designs as the former could confound the latter. They also add to the growing body of research highlighting the functional relevance of aperiodic activity in the brain. Commendably, the authors include replications of their key findings on multiple independent data sets.

Comments on the previous version:

The authors have addressed several of the weaknesses I noted in my original review, specifically, they softened their claims regarding the theta findings, while simultaneously strengthening these findings with additional analyses (using simulations as well as a new measure of rhythmicity, the phase autocorrelation function, pACF). Most of the other suggested control analyses were also implemented. While I believe the fact that the participants in the main sample were not young adults could be made even more explicit, and the potential interaction between age and aperiodic changes could be unpacked a little in the discussion, the age of the sample is definitely addressed upfront.

Reviewer #2 (Public review):

Summary:

In this manuscript, Frelih et al, investigate the relationship between aperiodic neural activity, as measured by EEG, and working memory performance, and compares this to the more commonly analyzed periodic, and in particular theta, measures that are often associated with such tasks. To do so, they analyze a primary dataset of 57 participants engaging in an n-back task, as well as a replication dataset, and use spectral parameterization to measure periodic and aperiodic features of the data, across time. In the revision, the authors have clarified some key points, and added a series of additional analyses and controls, including the use of an additional method, that helps to complement the original analyses and further corroborates their claims. In doing so, they find both periodic and aperiodic features that relate to the task dynamics, but importantly, the aperiodic component appears to explain away what otherwise looks like theta activity in a more traditional analysis. This study therefore helps to establish that aperiodic activity is a task-relevant dynamic feature in working memory tasks and may be the underlying change in many other studies that reported 'theta' changes, but did not use methods that could differentiate periodic and aperiodic features.

Strengths:

Key strengths of this paper include that it addresses an important question - that of properly adjudicating which features of EEG recordings relate to working memory tasks - and in doing so provides a compelling answer, with important implications for considering prior work and contributing to understanding the neural underpinnings of working memory. The revision is improved by showing this using an additional analysis method. I do not find any significant faults or error with the design, analysis, and main interpretations as presented by this paper, and as such, find the approach taken to be a valid and well-enacted. The use of multiple variants of the working memory task, as well as a replication dataset significantly strengthens this manuscript, by demonstrating a degree of replicability and generalizability. This manuscript is also an important contribution to motivating best practices for analyzing neuro-electrophysiological data, including in relation to using baselining procedures. I think the updates in the revision have helped to clarify the findings and impact of this study.

Weaknesses:

Overall, I do not find any obvious weaknesses with this manuscript and it's analyses that challenge the key results and conclusions. Updates through the revision have addressed my previous points about adding some additional notes on the methods and conclusions.

Reviewer #3 (Public review):

Summary:

Using a specparam (1/f) analysis of task-evoked activity, the authors propose that "substantial changes traditionally attributed to theta oscillations in working memory tasks are, in fact, due to shifts in the spectral slope of aperiodic activity." This is a very bold and ambitious statement, and the field of event-related EEG would benefit from more critical assessments of the role of aperiodic changes during task events. Unfortunately, the data shown here does not support the main conclusion advanced by the authors.

Strengths:

The field of event-related EEG would benefit from more critical assessments of the role of aperiodic changes during task events. The authors perform a number of additional control analyses, including different types of baseline correction, ERP subtraction, as well as replication of the experiment with two additional datasets.

Comments on previous revisions:

The authors have completed a substantial revision based on the comments from all of the reviewers. Overall, the major claims of the initial report have been profoundly tempered.

[Editors' note: We determined that this revised version appropriately tempers some of the prior claims and addresses the concerns raised by the reviewers through two rounds of review.]

Reviewer #1 (Public review):

The authors tried to quantify the difference between human complex traits by calculating genetic overlap scores between a pair of traits. Sherlock-II was devised to integrate GWAS with eQTL signals. The authors claim that Sherlock-II is superior to the previous version (robustness, accuracy, etc). It appears that their framework provides a reasonable solution to this important question, although the study needs further clarification and improvements.

(1) Sherlock-II incorporates GWAS and eQTL signals to better quantify genetic signals for a given complex trait. However, this approach is based on the hypothesis that "all GWAS signals confer association to complex trait via eQTL", which is not true (PMID: 37857933). This should be acknowledged (through mentioning in the text) and incorporated into the current setup (through differential analysis - for example, with or without eQTL signals, or with strong colocalization only).

(2) When incorporating eQTL, why did the authors use the top p-value tissues for eQTL? This approach seems simpler and probably more robust. But many eQTLs are tissue-specific. Therefore, it would also be important to know if eQTLS from appropriate tissues were incorporated instead.

(3) One of the main examples is the novel association between Alzheimer's disease and breast cancer. Although the authors provided a molecular clue underlying the association, it is still hard to comprehend the association easily, as the two diseases are generally known to be exclusive to each other. This is probably because breast cancer GWAS is performed for germline variants and does not consider the contribution of somatic variants.

(4) It would help readers understand the story better if a summary figure of the entire process were provided. The current Figure 1 does not fulfil that role.

(5) Figure 2 is not very informative. The readers would want to know more quantitative information rather than a heatmap-style display. Is there directionality to the relationship, or is it always unidirectional?

(6) In Figure 3, readers may want to know more specific information. For example, what gene signals are really driving the hypoxia signal in Alzheimer's disease vs breast cancer? And what SNP signals are driving these gene-level signals?

Reviewer #2 (Public review):

Summary:

The authors introduce a gene-level framework to detect shared genetic architecture between complex traits by integrating GWAS summary statistics with eQTL data via a new algorithm, Sherlock-II, which aggregates signals from multiple (cis/trans) eSNPs to produce gene-phenotype p-values. Shared pathways are identified with Partial-Pearson-Correlation Analysis (PPCA).

Strengths:

The authors show the gene-based approach is complementary and often more sensitive than SNP-level methods, and discuss limitations (in terms of no directionality, dependence on eQTL coverage).

Weaknesses:

(1) How do the authors explain data where missing tissues or sparse eQTL mapping are available? Would that bias as to which genes/traits can be linked and may produce false negatives or tissue-specific false positives?

(2) Aggregating SNP-level signals into gene scores can be confounded by LD; for example, a nearby causal variant for a different gene or non-expression mechanism may drive a gene's score, producing spurious gene-trait links. How do the authors prevent this?

(3) How the SNPs are assigned to genes would affect results, this is because different choices can change which genes appear shared between traits. The authors can expand on these.

(4) Many reported novel trait links remain speculative without functional or orthogonal validation (e.g., colocalization, perturbation data). Thus, the manuscript's claims are inconclusive and speculative.

(5) It would be best to run LD-aware colocalization and power-matched simulations to check for robustness.

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. 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 line,s 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. I have a few comments and suggestions for the authors.

Strengths and Weaknesses:

(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.

(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.

(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?

(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.

(5) Does hypoxia cause any changes to inhibitory neurogenesis (earlier stages than migration?) - this might always be known, but was not discussed.

(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.

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.

Reviewer #1 (Public review):

Summary:

Inhibitory hM4Di and excitatory hM3Dq DREADDs are currently the most commonly utilized chemogenetic tools in the field of nonhuman primate research, but there is a lack of available information regarding the temporal aspects of virally-mediated DREADD expression and function. Nagai et al. investigated the longitudinal expression and efficacy of DREADDs to modulate neuronal activity in the macaque model. The authors demonstrate that both hM4Di and hM3Dq DREADDs reach peak expression levels after approximately 60 days and that stable expression was maintained for up to two years for hM4Di and at least one year for hM3Dq DREADDs. During this period, DREADDs effectively modulated neuronal activity, as evidenced by a variety of measures, including behavioural testing, functional imaging, and/or electrophysiological recording. Notably, some of the data suggest that DREADD expression may decline after two-three years. This is a novel finding and has important implications for the utilization of this technology for long-term studies, as well as its potential therapeutic applications. Lastly, the authors highlight that peak DREADD expression may be significantly influenced by the presence of fused or co-expressed protein tags, emphasizing the importance of careful design and selection of viral constructs for neuroscientific research. This study represents a critical step in the field of chemogenetics, setting the scene for future development and optimization of this technology.

Strengths:

The longitudinal approach of this study provides important preliminary insights into the long-term utility of chemogenetics, which has not yet been thoroughly explored.

The data presented are novel and inclusive, relying on well-established in vivo imaging methods as well as behavioral and immunohistochemical techniques. The conclusions made by the authors are generally supported by a combination of these techniques. In particular, the utilization of in vivo imaging as a non-invasive method is translationally relevant and likely to make an impact in the field of chemogenetics, such that other researchers may adopt this method of longitudinal assessment in their own experiments. Rigorous standards have been applied to the datasets, and the appropriate controls have been included where possible.

The number of macaque subjects (20) from which data was available is also notable. Behavioral testing was performed in 11 subjects, FDG-PET in 5, electrophysiology in 1, and [11C]DCZ-PET in 15. This is an impressive accumulation of work that will surely be appreciated by the growing community of researchers using chemogenetics in nonhuman primates.

The implication that chemogenetic effects can be maintained for up to 1.5-2 years, followed by a gradual decline beyond this period, is an important development in knowledge. The limited duration of DREADD expression may present an obstacle in the translation of chemogenetic technology as a potential therapeutic tool, and it will be of interest for researchers to explore whether this limitation can be overcome. This study therefore represents a key starting point upon which future research can build.

Weaknesses:

None.

Reviewer #2 (Public review):

Summary:

This paper reports histological, PET imaging, functional and behavioural data evaluating the longevity of AAV2 infection in multiple brain areas of macaques in the context of DREADD experiments. The central aim is to provide unprecedented information about how long the expression of HM4di or HM3dq receptors are expressed and efficient in modulating brain functions after vector injections. The data show peak expression after 40 to 60 days of vector injection, and stable expressions for up to 1.5 years for hM4di, and that hM3dq remained mostly at 75% of peak after a year, declining to 50% after 2 years. DREADDs effectively modulated neuronal activity and behaviour for approximately two years, evaluated with behavioural testings, neural recordings or FDG-PET. A statistical evaluation revealed that vector titers, DREADD type and tags contribute to the measured peak level of DREADD expression.

The article present a thorough discussion of the limitations and specificities of chemogenetic approaches in monkeys.

Strength:

These are unique data, in non-human primate (NHP), an animal model that not only features physiological and immunological characteristics similar to humans, but also contributes to neurobiological functional studies over long timescales with experiments spanning months or years. This evaluation of long-term efficacy of DREADDs will be very important for all laboratories using chemogenetics in NHP but also for future use of such approach in experimental therapies. The longevity estimates are based on multiple approaches including behavioural and neurophysiological, thus providing information on functional efficacy of DREADD expression.

Performing such evaluation requires specific tools like PET imaging that very few monkey labs have access to. This study was done by the laboratory that has developed the radiotracer c11-DCZ, used here, a radiotracer binding selectively to DREADDs and providing, using PET, quantitative in vivo measures of DREADD expression. This study and its data should thus be a reference in the field, providing estimates to plan future chemogenetic experiments.

Publishing databases of experimental outcomes in NHP DREADD experiments is crucial for the community because such experiments are rare, expensive and long. It contributes to refining experiments and reducing the number of animals overall used in the domain.

Weaknesses:

This study is a meta-analysis of several experiments performed in one lab. The good side is that it combined a large amount of data that might not have been published individually; the down side is that all things where not planned and equated, creating a lot of unexplained variances in the data. However, this was judiciously used by the authors to provide very relevant information. One might think that organized multi-centric experiments planned using the knowledge acquired here, will provide help testing more parameters, including some related to inter-individual variability, and particular genetic constructs.

Reviewer #3 (Public review):

Summary

This manuscript, from the developers of the novel DREADD-selective agonist DCZ (Nagai et al., 2020), utilizes a unique dataset where multiple PET scans in a large number of monkeys, including baseline scans before AAV injection, 30-120 days post-injection, and then periodically over the course of the prolonged experiments, were performed to access short- and long-term dynamics of DREADD expression in vivo, and to associate DREADD expression with the efficacy of manipulating the neuronal activity or behavior. The goal was to provide critical insights into practicality and design of multi-year studies using chemogenetics, and to elucidate factors affecting expression stability.

Strengths are systematic quantitative assessment of the effects of both excitatory and inhibitory DREADDs, quantification of both the short-term and longer-term dynamics, a wide range of functional assessment approaches (behavior, electrophysiology, imaging), and assessment of factors affecting DREADD expression levels, such as serotype, promoter, titer (concentration), tag, and DREADD type.

These finding will undoubtedly have a very significant impact on the rapidly growing, but still highly challenging field of primate chemogenetic manipulations. As such, the work represents an invaluable resource for the community.

Reviewer #1 (Public review):

Summary:

This manuscript assesses the differences between young and aged chondrocytes. Through transcriptomic analysis and further assessments in chondrocytes, GATA4 was found to be increased in aged chondrocyte donors compared to young. Subsequent mechanistic analysis with lentiviral vectors, siRNAs, and a small molecule were used to study the role of GATA4 in young and old chondrocytes. Lastly, an in vivo study was used to assess the effect of GATA4 expression on osteoarthritis progression in a DMM mouse model.

Strengths:

This work linked the over expression of GATA4 to NF-kB signaling pathway activation, alterations to the TGF-b signaling pathway, and found that GATA4 increased the progression of OA compared to the DMM control group. Indicating that GATA4 contributes to the onset and progression of OA in aged individuals.

Comments on revised version:

Great work! All my concerns have been well addressed.

Reviewer #2 (Public review):

Summary:

This study elucidated the impact of GATA4 on aging- and injury-induced cartilage degradation and osteoarthritis (OA) progression, based on the team's finding that GATA expression is positively correlated with aging in human chondrocytes. By integrating cell culture of human chondrocytes, gene manipulation tools (siRNA, lentivirus), biological/biochemical analyses and murine models of post-traumatic OA, the team found that increasing GATA4 levels reduced anabolism and increased catabolism of chondrocytes from young donors, likely through upregulation of the BMP pathway, and that this impact is not correlated with TGF-β stimulation. Conversely, silencing GATA4 by siRNA attenuated catabolism and elevated aggrecan/collagen II biosynthesis of chondrocytes from old donors. The physiological relevance of GATA4 was further validated by the accelerated OA progression observed in lentivirus-infected mice in the DMM model.

Strengths:

This is a highly significant and innovative study that provides new molecular insights into cartilage homeostasis and pathology in the context of aging and disease. The experiments were performed in a comprehensive and rigorous manner. The data were interpreted thoroughly in the context of the current literature.

Weaknesses:

The only aspect that would benefit from further clarification is a more detailed discussion of aging-associated ECM changes in the context of prior literature.

Reviewer #3 (Public review):

Summary:

This is an exciting, comprehensive paper that demonstrates the role of GATA4 on OA-like changes in chondrocytes. The authors present elegant reverse translational experiments that justify this mechanism and demonstrate the sufficiency of GATA4 in a mouse model of osteoarthritis (DMM), where GATA4 drove cartilage degeneration and pain in a manner that was significantly worse than DMM alone. This could pave the way for new therapies for OA that account for both structural changes and pain.

Strengths:

(1) GATA4 was identified from human chondrocytes.

(2) IHC and sequencing confirmed GATA4 presence.

(3) Activation of SMADs is clearly shown in vitro with GATA4 overexpression.

(4) The role of GATA4 was functionally assessed in vivo using the mouse DMM model, where the authors uncovered that GATA4 worsens OA structure and hyperalgesia in male mice.

(5) It is interesting that GATA4 is largely known to be found in cardiac cells and to have a role in cardiac repair, metabolism, and inflammation, among other things listed by the authors in the discussion (in liver, lung, pancreas). What could this new knowledge of GATA4 mean for OA as a potentially systemically mediated disease, where cardiac disease and metabolic syndrome are often co-morbid?

Weaknesses:

I do not have further comments. Thank you for addressing the previously mentioned concerns.

Reviewer #1 (Public review):

In this work, Rios-Jimenez and Zomer et al have developed a 'zero-code' accessible computational framework (BEHAV3D-Tumour Profiler) designed to facilitate unbiased analysis of Intravital imaging (IVM) data to investigate tumour cell dynamics (via the tool's central 'heterogeneity module' ) and their interactions with the tumour microenvironment (via the 'large-scale phenotyping' and 'small-scale phenotyping' modules). A key strength is that it is designed as an open-source modular Jupyter Notebook with a user-friendly graphical user interface and can be implemented with Google Colab, facilitating efficient, cloud-based computational analysis at no cost. In addition, demo datasets are available on the authors GitHub repository to aid user training and enhance the usability of the developed pipeline.

To demonstrate the utility of BEHAV3D-TP, they apply the pipeline to timelapse IVM imaging datasets to investigate the in vivo migratory behaviour of fluorescently labelled DMG cells in tumour bearing mice. Using the tool's 'heterogeneity module' they were able to identify distinct single-cell behavioural patterns (based on multiple parameters such as directionality, speed, displacement, distance from tumour edge) which was used to group cells into distinct categories (e.g. retreating, invasive, static, erratic). They next applied the framework's 'large-scale phenotyping' and 'small-scale phenotyping' modules to investigate whether the tumour microenvironment (TME) may influence the distinct migratory behaviours identified. To achieve this, they combine TME visualisation in vivo during IVM (using fluorescent probes to label distinct TME components) or ex vivo after IVM (by large-scale imaging of harvested, immunostained tumours) to correlate different tumour behavioural patterns with the composition of the TME. They conclude that this tool has helped reveal links between TME composition (e.g. degree of vascularisation, presence of tumour-associated macrophages) and the invasiveness and directionality of tumour cells, which would have been challenging to identify when analysing single kinetic parameters in isolation.<br /> While the analysis provides only preliminary evidence in support of the authors conclusions on DMG cell migratory behaviours and their relationship with components of the tumour microenvironment, conclusions are appropriately tempered in the absence of additional experiments and controls.

The authors also evaluated the BEHAV3D TP heterogeneity module using available IVM datasets of distinct breast cancer cell lines transplanted in vivo, as well as healthy mammary epithelial cells to test its usability in non-tumour contexts where the migratory phenotypes of cells may be more subtle. This generated data is consistent with that produced during the original studies, as well as providing some additional (albeit preliminary) insights above that previously reported. Collectively, this provides some confidence in BEHAV3D TP's ability to uncover complex, multi-parametric cellular behaviours that may be missed using traditional approaches.

While the tool does not facilitate the extraction of quantitative kinetic cellular parameters (e.g. speed, directionality, persistence and displacement) from intravital images, the authors have developed their tool to facilitate the integration of other data formats generated by open-source Fiji plugins (e.g. TrackMate, MTrackJ, ManualTracking) which will help ensure its accessibility to a broader range of researchers. Overall, this computational framework appears to represent a useful and comparatively user-friendly tool to analyse dynamic multi-parametric data to help identify patterns in cell migratory behaviours, and to assess whether these behaviours might be influenced by neighbouring cells and structures in their microenvironment.

When combined with other methods, it therefore has the potential to be a valuable addition to a researcher's IVM analysis 'tool-box'.

Reviewer #2 (Public review):

Summary:

The authors produce a new tool, BEHAV3D to analyse tracking data and to integrate these analyses with large and small scale architectural features of the tissue. This is similar to several other published methods to analyse spatio-temporal data, however, the connection to tissue features is a nice addition, as is the lack of requirement for coding. The tool is then used to analyse tracking data of tumour cells in diffuse midline glioma. They suggest 7 clusters exist within these tracks and that they differ spatially. They ultimately suggest that these behaviours occur in distinct spatial areas as determined by CytoMAP.

Strengths:

The tool appears relatively user-friendly and is open source. The combination with CytoMAP represents a nice option for researchers.

The identification of associations between cell track phenotype and spatial features is exciting and the diffuse midline glioma data nicely demonstrates how this could be used.

Reviewer #3 (Public review):

The manuscript by Rios-Jimenez developed a software tool, BEHAV3D Tumor Profiler, to analyze 3D intravital imaging data and identify distinctive tumor cell migratory phenotypes based on the quantified 3D image data. Moreover, the heterogeneity module in this software tool can correlate the different cell migration phenotypes with variable features of the tumor microenvironment. Overall, this is a useful tool for intravital imaging data analysis and its open-source nature makes it accessible to all interested users.

Strengths:

An open-source software tool that can quantify cell migratory dynamics from intravital imaging data and identify distinctive migratory phenotypes that correlate with variable features of the tumor microenvironment.

Weaknesses:

Motility is the main tumor cell feature analyzed in the study together with some other tumor-intrinsic features, such as morphology. However, these features are insufficient to characterize and identify the heterogeneity of the tumor cell population that impacts their behaviors in the complex tumor microenvironment (TME). For instance, there are important non-tumor cell types in the TME, and the interaction dynamics of tumor cells with other cell types, e.g., fibroblasts and distinct immune cells, play a crucial role in regulating tumor behaviors. BEHAV3D-TP focuses on analysis of tumor-alone features, and cannot be applied to analyze important cell-cell interaction dynamics in 3D.

Reviewer #1 (Public review):

Summary:

This manuscript uses molecular dynamics simulations to understand how forces felt by the intracellular domain are coupled to opening of the mechanosensitive ion channel NOMPC. The concept is interesting - as the only clearly defined example of an ion channel that opens due to forces on a tethered domain, the mechanism by which this occur are yet to be fully elucidated. The main finding is that twisting of the transmembrane portion of the protein - specifically via the TRP domain that is conserved within the broad family of channels- is required to open the pore. That this could be a common mechanism utilised by a wide range of channels in the family, not just mechanically gated ones, makes the result significant. It is intriguing to consider how different activating stimuli can produce a similar activating motion within this family. While the authors do not see full opening of the channel, only an initial dilation, this motion is consistent with partial opening of structurally characterized members of this family.

Strengths:

Demonstrating that rotation of the TRP domain is the essential requirement for channel opening would have significant implcaitions for other members of this channel family.

Weaknesses:

The manuscript centres around 3 main computational experiments. In the first, a compression force is applied on a truncated intracellular domain and it is shown that this creates both a membrane normal (compression) and membrane parallel (twisting) force on the TRP domain. This is a point that was demonstrated in the authors prior eLife paper - so the point here is to quantify these forces for the second experiment.

The second experiment is the most important in the manuscript. In this, forces are applied directly to two residues on the TRP domain with either a membrane normal (compression) or membrane parallel (twisting) direction, with the magnitude and directions chosen to match that found in the first experiment. Only the twisting force is seen to widen the pore in the triplicate simulations, suggesting that twisting, but not compression can open the pore. This result is intriguing and there appears to be a significant difference between the dilation of pore with the two force directions. When the forces are made of similar magnitude, twisting still has a larger effect than forces along the membrane normal.

The second important consideration is that the study never sees full pore opening, rather a widening that is less than that seen in open state structures of other TRP channels and insufficient for rapid ion currents. This is something the authors acknowledge in their prior manuscript Twist may be the key to get this dilation, but we don't know if it is the key to full pore opening. Structural comparison to open state TRP channels supports that this represents partial opening along the expected pathway of channel gating.

Experiment three considers the intracellular domain and determines the link between compression and twisting of the intracellular AR domain. In this case, the end of the domain is twisted and it is shown that the domain compresses, the converse to the similar study previously done by the authors in which compression of the domain was shown to generate torque.

Reviewer #2 (Public review):

This study uses all atom MD simulation to explore the mechanics of channel opening for the NOMPC mechanosensitive channel. Previously the authors used MD to show that external forces directed along the long-axis of the protein (normal to the membrane) results in AR domain compression and channel opening. This force causes two changes to the key TRP domains adjacent to the channel gate: 1) a compressive force pushes the TRP domain along the membrane normal, while 2) a twisting torque induces a clock-wise rotation on the TRP domain helix when viewing the bottom of the channel from the cytoplasm. Here, the authors wanted to understand which of those two changes are responsible for increasing the inner pore radius, and they show that it is the torque. The simulations in Figure 2 probe this question with different forces, and we can see the pore open with parallel forces in the membrane, but not with the membrane-normal forces. I believe this result as it is reproducible, the timescales are reaching 1 microsecond, and the gate is clearly increasing diameter to about 4 Å. This seems to be the most important finding in the paper, but the impact is limited since the authors already shows how forces lead to channel opening, and this is further teasing apart the forces and motions that are actually the ones that cause the opening.

Reviewer #3 (Public review):

Summary:

This manuscript by Duan and Song interrogates the gating mechanisms and specifically force transmission in mechanosensitive NOMPC channels using steered molecular dynamics simulations. They propose that the ankyrin spring can transmit force to the gate through torsional forces adding molecular detail to the force transduction pathways in this channel.

Strengths:

Detailed, rigorous simulations coupled with a novel model for force transduction.

Weaknesses:

Experimental validation of reduced mechanosensitivity through mutagenesis of proposed ankyrin/TRP domain coupling interactions would greatly enhance the manuscript.

Reviewer #1 (Public review):

Summary:

This paper attempts to measure the complex changes of consciousness in the human brain as a whole. Inspired by the perturbational complexity index (PCI) from classic research, authors introduce simulation PCI (𝑠𝑃𝐶𝐼) of a time series of brain activity as a measure of consciousness. They first use large-scale brain network modeling to explore its relationship with the network coupling and input noise. Then the authors verify the measure with empirical data collected in previous research.

Strengths:

The conceptual idea of the work is novel. The authors measure the complexity of brain activity from the perspective of dynamical systems. They provide a comparison of the proposed measure with four other indexes. The text of this paper is very concise, supported by experimental data and theoretical model analysis.

Comments on revisions:

The manuscript is in good shape after revision. I would suggest that the author open-source the code and data in this study.

Reviewer #2 (Public review):

Summary:

Breyton and colleagues analysed the emergent dynamics from a neural mass model, characterised the resultant complexity of the dynamics, and then related these signatures of complexity to datasets in which individuals had been anaesthetised with different pharmacological agents. The results provide a coherent explanation for observations associated with different time series metrics, and further help to reinforce the importance of modelling when integrating across scientific studies.

Strengths:

* The modelling approach was clear, well-reasoned and explicit, allowing for direct comparison to other work and potential elaboration in future studies through the augmentation with richer neurobiological detail.

* The results serve to provide a potential mechanistic basis for the observation that Perturbational Complexity Index changes as a function of consciousness state.

Weaknesses:

* Coactivation cascades were visually identified, rather than observed through an algorithmic lens. Given that there are numerous tools for quantifying the presence/absence of cascades from neuroimaging data, the authors may benefit from formalising this notion.

* It was difficult to tell, graphically, where the model's operating regime lay. Visual clarity here will greatly benefit the reader.

Comments on revisions:

The authors have addressed my concerns.

Reviewer #1 (Public review):

Summary:

The manuscript "Synaptotagmin 1 and Synaptotagmin 7 promote MR1-mediated presentation of Mycobacterium tuberculosis antigens", authored by Kim et al., showed that the calcium-sensing trafficking proteins Synaptotagmin (Syt) 1 and Syt7 specifically promote (are critical for) MAIT cell activation in response to Mtb-infected bronchial epithelial cell line BEAS-2B (Fig. 1) and monocyte-like cell line THP-1 (Figure 3) . This work also showed co-localization of Syt1 and Syt7 with Rab7a and Lamp1, but not with Rab5a (Figure 5). Loss of Syt1 and Syt7 resulted in a larger area of MR1 vesicles (Figure 6f) and an increased number of MR1 vesicles in close proximity to an Auxotrophic Mtb-containing vacuoles during infection (Figure 7ab). Moreover, flow organellometry was used to separate phagosomes from other subcellular fractions and identify enrichment of auxotrophic Mtb-containing vacuoles in fractions 42-50, which were enriched with Lamp1+ vacuoles or phagosomes (Figures 7e-f).

Strengths:

This work nicely associated Syt1 and Syt7 with late endocytic compartments and Mtb+ vacuoles. Gene editing of Syt1 and Syt7 loci of bronchial epithelial and monocyte-like cells supported Syt1 and Syt7 facilitated maintaining a normal level of antigen presentation for MAIT cell activation in Mtb infection. Imaging analyses further supported that Syt1 and Syt7 mutants enhanced the overlaps of MR1 with Mtb fluorescence, and the MR1 proximity with Mtb-infected vacuoles, suggesting that Syt1 and Syt7 proteins help antigen presentation in Mtb infection for MAIT activation.

Weaknesses:

Additional data are needed to support the conclusion, "identify a novel pathway in which Syt1 and Syt7 facilitate the translocation of MR1 from Mtb-containing vacuoles" and some pieces of other evidence may be seen by some to contradict this conclusion.

Reviewer #2 (Public review):

Summary:

The study demonstrates that calcium-sensing trafficking proteins Synaptotagmin (Syt) 1 and Syt7 are involved in the efficient presentation of mycobacterial antigens by MR1 during M. tuberculosis infection.

This is achieved by creating antigen-presenting cells in which the Syt1 and Syt7 genes are knocked out. These mutated cell lines show significantly reduced stimulation of MAIT cells, while their stimulation of HLA class I-restricted T cells remains unchanged. Syt1 and Syt7 co-localize in a late endo-lysosomal compartment where MR1 molecules are also located, near M. tuberculosis-containing vacuoles.

Strengths:

This work uncovers a new aspect of how mycobacterial antigens generated during infection are presented. The finding that Syt1 and Syt7 are relevant for final MR1 surface expression and presentation to MR1-restricted T cells is novel and adds valuable information to this process.

The experiments include all necessary controls and convincingly validate the role of Syt1 and Syt7.

Another key point is that these proteins are essential during infection, but they are not significant when an exogenous synthetic antigen is used in the experiments. This emphasizes the importance of studying infection as a physiological context for antigen presentation to MAIT cells.

An additional relevant aspect is that the study reveals the existence of different MR1 antigen presentation pathways, which differ from the endoplasmic reticulum or endosomal pathways that are typical for MHC-presented peptides.

Weaknesses:

The reduced MAIT cell response observed with Syt1 and Syt7-deficient cell lines is statistically significant but not completely abolished. This may suggest that only some MR1-loaded molecules depend on these two Syt proteins. Further research is needed to determine whether, during persistent M. tuberculosis infection, enough MR1-loaded molecules are produced and transported to the plasma membrane to sufficiently stimulate MAIT cells.

The study proposes that other Syt proteins might also play a role, as outlined by the authors. However, exploring potential redundant mechanisms that facilitate MR1 loading with antigens remains a challenging task.

Reviewer #3 (Public review):

Summary:

In the submitted manuscript, the authors investigate the role of Synaptotagmins (Syt1) and (Syt7) in MR1 presentation of MtB.

Strengths:

In the first series of experiments, the authors determined that knocking down Syt1 and Sy7 in antigen-presenting cells decreases IFN-γ production following cellular infection with Mtb. These experiments are well performed and controlled.

Weaknesses:

Next, they aim to mechanistically investigate how Syt1 and Syt7 affect MtB presentation. In particular, they focus on MR1, a non-classical MHC-I molecule known to present endogenous and exogenous metabolites, including MtB metabolites.

Results from these next series of experiments are less clear. Firstly, they show that knocking down Syt1 and Sy7 does not change MtB phagocytosis as well as MR1 ER-plasma membrane translocation. Based on this, they suggest that Syt1 and Syt7 may affect MR1 trafficking in endosomal compartments. However, neither subcellular compartment analysis nor flow organelleometry clearly establishes the role of Syt1 and Syt7 in MtB trafficking.

Altogether, the notion that Synaptotagmins facilitate MR1 interaction with Mtb-containing compartments and its vesicular transport was already known. As such, the manuscript should add additional insight on where/how the interaction occurs. The reviewer is left with the notion that Syt1 and Sy7 may affect MR1 presentation, facilitating the trafficking of MR1 vesicles from endosomal compartments to either the cell surface or other endosomal compartments. The analysis is observational and additional data or discussion could address what the insight gained beyond what is already known from the literature.

Reviewer #1 (Public review):

This study by Thapliyal and Glauser investigates the neural mechanisms that contribute to the progressive suppression of thermonociceptive behavior that is induced under conditions of starvation. Several previous studies have demonstrated that when starved, C. elegans alters its preferences for a variety of sensory cues, including CO2, temperature, and odors, in order to prioritize food seeking over other behavioral drives. The varied mechanisms that underlie the ability of internal states to alter behavioral responses are not fully understood, however there is growing evidence for a role by neuropeptidergic signaling as well as capacity for functionally distinct microcircuits, formed by distinct internal states, to trigger similar behavior outcomes.

Within the physiological range of C. elegans (~15-25C), starvation triggers a profound reduction in temperature-driven thermotaxis behaviors. This reduction involves the recruitment of the amphid sensory neuron pair AWC. The AWC neurons primarily act to sense appetitive chemosensory cues, however under starvation conditions begin to display temperature responses that previous studies have linked to the reduction in thermotaxis navigation. Here, Thapliyal and Glauser investigate the impact of starvation on thermonociceptive responses, innate escape behaviors that are triggered by exposure to noxious temperatures above 26C or rapid thermal stimuli below 26C. They compare the strength of thermonociceptive behaviors, specifically heat-triggered reversals, in worms experiencing either early food deprivation (1 hour off food) or prolonged starvation (6 hours off food). Their experiments demonstrate a progressive loss of heat-triggered reversals that is mediated by AWC and ASI neurons, as well as both glutamateric and neuropeptidergic signaling.

At the level of neural activity, this study reports that the transition from early food deprivation to prolonged starvation reconfigures the temperature-driven activity of AWC neurons from largely deterministic to stochastic. This finding is interesting in light of previous work that reported the opposite transition (from stochastic to deterministic) in temperature-driven AWC responses when comparing well-fed worms to those kept from food for 3 hours. This study also identifies neural and genetic mechanisms that contribute to differences in thermonociceptive responses at +1 versus +6 hours starvation; confusingly, these mechanisms are partially distinct from those that contribute to differences in negative thermotaxis behaviors in well-fed and +3 hours starvation worms (Takeishi et al 2020). A limitation of this manuscript is that these differences are not particularly acknowledged or addressed, other than the hypothesis that independent mechanisms underlie negative thermotaxis versus thermonociceptive stimuli. However, this suggestion is not experimentally verified. Multiple additional aspects of this study make the results difficult to synthesize with existing knowledge, including 1) differences in - and insufficient discussion of - the magnitude and kinetics of thermal stimuli; 2) this study's use of "heating power" rather than temperature values when presenting behavioral results; 3) the use of +1 hours starvation as a baseline instead of well-fed worms. Indeed, this last point reflects a noticeable experimental result that differs from previous studies, namely that at room temperature the basal movements of well-fed and starved worms are not different. Such a surprisingly result warrants further quantification of worm mobility in general and could have prompted a set of experiments directly testing previously published thermal conditions, to demonstrate that the new effects reported arise specifically from the use of thermonociceptive stimuli, as hypothesized. Finally, a previous report (Yeon et al 2021) demonstrated differences in the impact of chronic versus acute neural silencing on starvation-dependent plasticity in the context of negative thermotaxis. We therefore wonder whether similar developmental compensation impacts the neural circuits that contribute to starvation-dependent plasticity in the thermonociceptive responses.

A weakness of this manuscript is that the introduction is insufficiently scholarly in terms of citations and the description of current knowledge surrounding the impact of internal state on sensory behavior, particularly given previous work on the impact of feeding state on thermosensory behavioral plasticity (Takeshi et al 2020, Yeon et al 2021) and chemosensory valence (Banerjee et al 2023, Rengarajan et al 2019, etc). Similarly, the authors commanding knowledge of the distinction between thermotaxis navigation (especially negative thermotaxis) and thermonociceptive behaviors could be communicated in more depth and clarity to the readers, in order to contextualize this study's new findings within the previous literature.

Nevertheless, this study represents a solid addition to the growing evidence that C. elegans sensory behaviors are strongly impacted by internal states, and that neuropeptigergic signaling plays a key role in mediating behavioral plasticity. To that end, the authors have provided solid evidence of their claims.

Reviewer #2 (Public review):

In this work Thapliyal and Glauser tried to provide mechanistic understanding by which animals modulate their neural circuit responses to control nociceptive behavior on the basis of the dynamic internal feeding state. It is an important study that adds to growing body of evidences coming from multiple model systems. They have used elegant genetics, behavioral and Ca-imaging experiments to demonstrate how the auxiliary thermosensory neuron pair, AWC and one of the internal state sensing interneuron pair, ASI, respond to dynamic internal starvation-state to modulate behavioral response to noxious heat. Interestingly, these neuron pairs use distinct molecular mechanisms along with some other unidentified neurons to suppress heat-indued reversal response under short-term and prolonged starvations. The experiments are well performed that support most of the claims and provide important framework for future studies.

I have some queries that if answered, will certainly enhance the study,

(1) The results suggests that ASI is one of the primary drivers for the starvation-evoked behavioral plasticity, which regulates AWC activity under prolonged starvation. It raises many important questions including, a) how starvation modulates ASI response to heat? b) under prolonged starvation, whether ASI also promotes other, non-AWC, glutamatergic inhibitory neurons to suppress heat-induced reversal and how?

(2) How does ASI regulate AWC activity? In the proposed model (figure 8) authors suggested an independent, unknown signal, other than INS-32 and NLP-18, from ASI to regulate AWC activity. However, from the results the existence of another signal is not very clear.

(3) Previously, Takeishi et. al., showed that ins-1 dynamically modulates AWC-AIA mediated thermotaxis behavior based on the feeding state of the animal. It raises questions whether ins-1 also contributes to noxious heat-induced reversal behavior.

(4) Experiments with AWC fate conversion mutants (nsy-1 and nsy-7) were very good ideas, however the results obtained were confusing. flp-6 mutant data suggests AWCoff would be essential for heat induced reversal, especially at the low intensity stimulus level. However, nsy-1 mutant forming two AWCon neurons showed complete rescue at the low heat level, which is quite opposite. Similarly, although less prominent, eat-4 rescue experiments suggested both nsy-1 and nsy-7 should behave normally at high heat condition, which was not the result observed.

Reviewer #3 (Public review):

Summary:

Thapliyal and Glauser show that hunger alters how C. elegans respond to noxious thermal stimuli. Using targeted neural ablation, mutant analysis, and live-cell functional imaging the authors demonstrate that hunger changes the properties of AWC sensory neurons, which sense noxious heat. The authors further show that effects of hunger on nociception require ASI neurons, which are known to respond to hunger and mediate effects of food deprivation on behavior. Finally, the study uses mutant analysis to implicate glutamate and specific neuropeptides in thermal nociception and in modulation of nociceptors by hunger-responsive neurons.

Strengths:

The study clearly shows a strong effect of hunger on nociception and documents a striking effect of hunger on the intrinsic properties of AWC sensory neurons, which respond to noxious heat. The study also clearly and compellingly demonstrates that ablation of hunger-responsive ASI neurons blocks effects of hunger on nociceptive AWCs. These data, which constitute the kernel of the manuscript, are striking and exciting.

Weaknesses:

The study has some weaknesses that the authors should address.

(1) Ablation of AWC neurons alters the basal sensitivity to noxious heat stimuli. This should be clearly noted in the description of the result and warrants some discussion.

(2) Throughout the study it seems that data are replotted in multiple figure panels. The authors should clearly indicate in figure legends when this occurs. Also, the authors should ensure that statistical tests requiring multiple comparisons are correctly implemented and reflect the number of times experimental data are compared to a single set of control data.

(3) How ASIs modulate AWCs remains unclear. The authors find that loss of INS-6, an insulin-like peptide provided by ASIs, partially recapitulates the effect of ASI ablation. This is observation is not further developed and instead the authors characterize other secreted factors that seem to mediate sensitization of animals to noxious heat stimuli. While it is interesting that there are multiple opposing inputs into the nociceptor circuit, the essential connection between ASIs and AWCs that underlies the foundational observations in figures 1 and 2 is not sufficiently characterized.

(4) The assertion that 'starvation reshapes AWC responses from deterministic to stochastic' is not clearly supported by the data. AWC neurons seem capable of showing different responses to thermal stimuli, and the probabilities associated with these responses change after fasting. The different kinds of responses are seen under basal and fasted conditions.

Reviewer #1 (Public review):

Summary:

In this article, the authors develop a method to re-analyze published data measuring the transcription dynamics of developmental genes within Drosophila embryos. Using a simple framework, they identify periods of transcriptional activity from traces of MS2 signal and analyze several parameters of these traces. In the five data sets they analyzed, the authors find that each transcriptional "burst" has a largely invariant duration, both across spatial positions in the embryo and across different enhancers and genes, while the time between transcriptional bursts varies more. However, they find that the best predictor of the mean transcription levels at different spatial positions in the embryo is the "activity time" -- the total time from the first to the last transcriptional burst in the observed cell cycle.

Strengths:

(1) The algorithm for analyzing the MS2 transcriptional traces is clearly described and appropriate for the data.

(2) The analysis of the four transcriptional parameters -- the transcriptional burst duration, the time between bursts, the activity time, and the polymerase loading rate is clearly done and logically explained, allowing the reader to observe the different distributions of these values and the relationship between each of these parameters and the overall expression output in each cell. The authors make a convincing case that the activity time is the best predictor of a cell's expression output.

(3) The figures are clearly presented and easy to follow.

Weaknesses:

(1) The strength of the relationship between the different transcriptional parameters and the mean expression output is displayed visually in Figures 5 and 7, but is not formally quantified. Given that the tau_off times seem more correlated to mean activity for some enhancers (e.g., rho) than others (e.g., sna SE), the quantification might be useful.

(2) There are some mechanistic details that are not discussed in depth. For example, the authors observe that the accumulation and degradation of the MS2 signal have similar slopes. However, given that the accumulation represents the transcription of MS2 loops, while the degradation represents diffusion of nascent transcripts away from the site of transcription, there is no mechanistic expectation for this. The degradation of signal seems likely to be a property of the mRNA itself, which shouldn't vary between cells or enhancer reporters, but the accumulation rate may be cell- or enhancer-specific. Similarly, the activity time depends both on the time of transcription onset and the time of transcription cessation. These two processes may be controlled by different transcription factor properties or levels and may be interesting to disentangle.

(3) There are previous analyses of the eve stripe dynamics, which the authors cite, but do not compare the results of their work to the previous work in depth.

Reviewer #2 (Public review):

Summary:

In this work, Nieto et al. investigate how spatial gene expression patterns in the early Drosophila embryo are regulated at the level of transcriptional bursting. Using live-cell MS2 imaging data of four reporter constructs and the endogenous eve gene, the authors extract temporal dynamics of nascent transcription at single-cell resolution. They implement a novel, simplified algorithm to infer promoter ON/OFF states based on fluorescence slope dynamics and use this to quantify burst duration (Ton), inter-burst duration (Toff), and total activity time across space.

The key finding is that while Ton and Toff remain relatively constant across space, the activity time-the window between first and last burst-is spatially modulated and best explains mean expression differences across the embryo. This uncovers a general strategy where early embryonic patterning genes modulate the duration of their transcriptionally permissive states, rather than the frequency or strength of bursting itself. The manuscript also shows that different enhancers of the same gene (e.g., sna proximal vs. shadow) can differentially modulate Toff and activity time, providing mechanistic insight into enhancer function.

Strengths:

The manuscript introduces activity time as a major, previously underappreciated determinant of spatial gene expression, distinct from Ton and Toff, providing an intuitive mechanistic link between temporal bursting and spatial patterning.

The authors develop a tractable inference algorithm based on linear accumulation/decay rates of MS2 fluorescence, allowing efficient burst state segmentation across thousands of trajectories.

Analysis across multiple biological replicates and different genes/enhancers lends confidence to the reproducibility and generalizability of the findings.

By analyzing both synthetic reporter constructs and an endogenous gene (eve), the work provides a coherent view of how enhancer architecture and spatial regulation are intertwined with transcriptional kinetics.

The supplementary information extends the biological findings with a gene expression noise model that accounts for non-exponential dwell times and illustrates how low-variability Ton buffers stochasticity in transcript levels.

Weaknesses:

The manuscript does not clearly delineate how this analysis extends beyond the prior landmark study (citation #40: Fukaya et al., 2016). While the current manuscript offers new modeling and statistics, more explicit clarification of what is novel in terms of biological conclusions and methodological advancement would help position the work.

While the methods are explained in detail in the Supplementary Information, the manuscript would benefit from including a diagrammatic model and explicitly clarifying whether the model is descriptive or predictive in scope.

The interpretation that fluorescence decay reflects RNA degradation could be confounded by polymerase runoff or transcript diffusion from the transcription site. These potential limitations are not thoroughly discussed.

The so-called loading rate is used as an empirical parameter in fitting fluorescence traces, but is not convincingly linked to distinct biological processes. The manuscript would benefit from a more precise definition or reframing of this term.

Impact and Utility:

The study provides a general and scalable framework for dissecting transcriptional kinetics in developing embryos, with implications for understanding enhancer logic and developmental robustness. The algorithm is suitable for adaptation to other live-imaging datasets and could be useful across systems where temporal transcriptional variability is being quantified. By highlighting activity time as a key regulatory axis, the work shifts attention to transcriptionally permissive windows as a primary developmental control layer.

This work will be of interest to: developmental biologists investigating spatial gene expression, researchers studying transcriptional regulation and noise, quantitative biologists developing models for transcriptional dynamics, and imaging and computational biologists working with live single-cell data.

Reviewer #3 (Public review):

Summary:

In this paper, the authors developed a simple algorithm to analyse live imaging transcription data (MS2) and infer various kinetic parameters. They then applied it to analyse data from previous publications on Drosophila that measured the dynamics of reporter genes driven by various enhancers alone (sna, Kr, rho), or in an endogenous context (eve).

The authors find that the main correlate with mean gene expression levels is the activity time, that is, the time during which the gene is bursting. They also find a correlation with the variation of the off time.

Strengths:

(1) The findings are very clearly presented.

(2) The simplicity of the algorithm is nice, and the comparative analysis among the various enhancers can be helpful for the field.

Weaknesses:

(1) The algorithm is not benchmarked against previously used algorithms in the field to infer ON and OFF times, for example, those based on Hidden Markov models. A comparison would help strengthen the support for this algorithm (if it really works well) or show at which point one must be careful when interpreting this data.

(2) More broadly, the novelty of the findings and how those fit within the knowledge of the field is not super clear. A better account of previous findings that have already quantified ON, OFF times and so on, and how the current findings fit within those, would help better appreciate the significance of the work.

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 inter-individual variability, and presents intriguing data that speaks to those ideas, albeit with the issues outlined above.

While the current work does not present any mechanistic analysis of inter-individual variability, the implementation of high-throughput assays sets up the field to more systematically investigate fly visual behaviors, their variability, and their underlying mechanisms.

Comments on revisions:

While the incorporation of a hierarchical mixed model (HMM) appears to represent an improvement over their prior single-parameter correlation approach, it's not clear to me that this is a multivariate analysis. They write that "For each trait, we fitted a hierarchical linear mixed-effects model in Matlab (using the fit lme function) with environmental context as a fixed effect and fly identity (ID) as a random intercept... We computed the intraclass correlation coefficient (ICC) from each model as the between-fly variance divided by total variance. ICC, therefore, quantified repeatability across environmental contexts."

Does this indicate that HMM was used in a univariate approach? Can an analysis of only five metrics of several dozen total metrics be characterized as 'holistic'?

Within Figure 10a, some of the metrics show high ICC scores, but others do not. This suggests that the authors are overstating the overall persistence and/or consistency of behavioral individuality. It is clear from Figure S8 that a large number of metrics were calculated for each fly, but it remains unclear, at least to me, why the five metrics in Figure 10a are justified for selection. One is left wondering how rare or common is the 0.6 repeatability of % time walked among all the other behavioral metrics. It appears that a holistic analysis of this large data set remains impossible.

The authors write: "...fly individuality persists across different contexts, and individual differences shape behavior across variable environments, thereby making the underlying developmental and functional mechanisms amenable to genetic dissection." However, presumably the various behavioral features (and their variability) are governed by different brain regions, so some metrics (high ICC) would be amenable to the genetic dissection of individuality/variability, while others (low ICC) would not. It would be useful to know which are which, to define which behavioral domains express individuality, and could be targets for genetic analysis, and which do not. At the very least, the Abstract might like to acknowledge that inter-context consistency is not a major property of all or most behavioral metrics.

I hold that inter-trial repeatability should rightly be called "stability" while inter-context repeatability should be called "consistency". In the current manuscript, "consistency" is used throughout the manuscript, except for the new edits, which use "stability". If the authors are going to use both terms, it would be preferable if they could explain precisely how they define and use these terms.

Reviewer #2 (Public review):

Summary:

The authors repeated measured the behavior of individual flies across several environmental situations in custom-made behavioral phenotyping rigs.

Strengths:

The study uses several different behavioral phenotyping devices to quantify individual behavior in a number of different situations and over time. It seems to be a very impressive amount of data. The authors also make all their behavioral phenotyping rig design and tracking software available, which I think is great and I'm sure other folks will be interested in using and adapting to their own needs.

Weaknesses/Limitations:

I think an important limitation is that while the authors measured the flies under different environmental scenarios (i.e. with different lighting, temperature) they didn't really alter the "context" of the environment. At least within behavioral ecology, context would refer to the potential functionality of the expressed behaviors so for example, an anti-predator context, or a mating context, or foraging. Here, the authors seem to really just be measuring aspects of locomotion under benign (relatively low risk perception) contexts. This is not a flaw of the study, but rather a limitation to how strongly the authors can really say that this demonstrates that individuality is generalized across many different contexts. It's quite possible that rank-order of locomotor (or other) behaviors may shift when the flies are in a mating or risky context.

I think the authors are missing an opportunity to use much more robust statistical methods. It appears as though the authors used pearson correlations across time/situations to estimate individual variation; however far more sophisticated and elegant methods exist. The problem is that pearson correlation coefficients can be 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 change, 1 if it was) and the resulting individual rank differences as the response"). So were different models run for each scenario? for different behaviors? Across scenarios? what exactly? I just harp on this because I'm actually really interested in these data and think that updating these methods can really help clarify the results and make the main messages much clearer!

I appreciate that the authors now included their sample sizes in the main body of text (as opposed to the supplement) but I think that it would still help if the authors included a brief overview of their design at the start of the methods. It is still unclear to me how many rigs each individual fly was run through? Were the same individuals measured in multiple different rigs/scenarios? Or just one?

I really think a variance partitioning modeling framework could certainly improve their statistical inference and likely highlight some other cool patterns as these methods could better estimate stability and covariance in individual intercepts (and potentially slopes) across time and situation. I also genuinely think that this will improve the impact and reach of this paper as they'll be using methods that are standard in the study of individual behavioral variation

Reviewer #1 (Public review):

Summary:

In this manuscript, Mahajan et.al introduce two innovative macroscopic measures-intrachromosomal gene correlation length (𝓁∗) and transition energy barrier-to investigate chromatin structural dynamics associated with aging and age-related syndromes such as Hutchinson-Gilford Progeria Syndrome (HGPS) and Werner Syndrome (WRN). The authors propose a compelling systems-level approach that complements traditional biomarker-driven analyses, offering a more holistic and quantitative framework to assess genome-wide dysregulation. The concept of 𝓁∗ as a spatial correlation metric to capture chromatin disorganization is novel and well-motivated. The use of autocorrelation on distance-binned gene expression adds depth to the interpretation of chromatin state shifts. The energy landscape framework for gene state transitions is an elegant abstraction, with the notion of "irreversibility" providing a thermodynamic interpretation of transcriptional dysregulation. The application to multiple datasets (Fleischer, Line-1) and pathological states adds robustness to the analysis. The consistency of chromosome 6 (and to some extent chromosomes 16 and X) emerging as hotspots aligns well with known histone cluster localization and disease-relevant pathways. The manuscript does an excellent job of integrating transcriptomic trends with known epigenetic hallmarks of aging, and the proposed metrics can be used in place of traditional techniques like PCA in capturing structural transcriptome features. However, a direct correlation with ATACseq/ HiC data with the present analysis will be more informative.

Strengths:

Novel inclusion of statistical metrics that can help in systems-level studies in aging and chromatin biology.

Weaknesses:

(1) In the manuscript, the authors mention "While it may be intuitive to assume that highly expressed genes originate from euchromatin, this cannot be conclusively stated as a complete representation of euchromatin genes, nor can LAT be definitively linked to heterochromatin". What percentage of LAT can be linked to heterochromatin? What is the distribution of LAT and HAT in the euchromatin?

(2) In Figure 2, the authors observe "that the signal from the HAT class is the stronger between two and the signal from the LAT class, being mostly uniform, can be constituted as background noise." Is this biologically relevant? Are low-abundance transcripts constitutively expressed? The authors should discuss this in the Results section.

(3) The authors make a very interesting observation from Figure 3: that ASO-treated LINE-1 appears to be more effective in restoring HGPS cell lines closer to wild-type compared to WRN.. This can be explained by the difference in the basal activity of L1 elements in the HGPS vs WRN cell types. The authors should comment on this.

(4) The authors report that "from the results on Fleicher dataset is the magnitude of the difference in similarity distance is more pronounced in 𝓁∗ than in gene expression." Does this mean that the alterations in gene distance and chromatin organization do not result in gene expression change during aging?

(5) "In Fleischer dataset, as evident in Figure 4a, although changes in the heterochromatin are not identical for all chromosomes shown by the different degrees of variation of 𝓁∗ in each age group." The authors should present a comprehensive map of each chromosome change in gene distance to better explain the above statement.

(6) While trends in 𝓁∗ are discussed at both global and chromosome-specific levels, stronger statistical testing (e.g., permutation tests, bootstrapping) would lend greater confidence, especially when differences between age groups or treatment states are modest.

(7) While the transition energy barrier is an insightful conceptual addition, further clarification on the mathematical formulation and its physical assumptions (e.g., energy normalization, symmetry conditions) would improve interpretability. Also, in between Figures 7 and 8, the authors first compare the energy barrier of Chromosome 1 and then for all other chromosomes. What is the rationale for only analyzing chromosome 1? How many HAT or LAT are present there?

Reviewer #2 (Public review):

The authors report that intra-chromosomal gene correlation length (spatial correlations in gene expressions along the chromosome) serves as a proxy of chromatin structure and hence gene expression. They further explore changes in these metrics with aging. These are interesting and important findings. However, there are fundamental problems at this time.

(1) The basic method lacks validation. There is no validation of the method by approaches that directly measure chromatin structure, for example ATAC-seq, ChIP-seq, or CUT n RUN.

(2) There is no validation by interventions that directly probe chromatin structure, such as HDAC inhibitors. The authors employ datasets with knockdown of LINE-1 for validation. However, this is not a specific chromatin intervention.

(3) There is no statistical analysis, e.g., in Figures 4 and 5.

(4) The authors state, "in Figure 4a changes in the heterochromatin are not identical for all chromosomes shown...." I do not see the data for individual chromosomes.

(5) In comparisons of WT vs HGPS NT or HGPS SCR (Figure S6), is this a fair comparison? The WT and HGPS are presumably from different human donors, so they have genetic and epigenetic differences unrelated to HGPS.

Reviewer #1 (Public review):

Summary

This manuscript presents an updated version of rsatoolbox, a Python package for performing Representational Similarity Analysis (RSA) on neural data. The authors provide a comprehensive and well-integrated framework that incorporates a range of state-of-the-art methodological advances. The updated version extends the toolbox's capabilities.

The paper outlines a typical RSA workflow in five steps:

(1) Importing data and estimating activity patterns.

(2) Estimating representational geometries (computing RDMs).

(3) Comparing RDMs.

(4) Performing inferential model comparisons.

(5) Handling multiple testing across space and time.

For each step, the authors describe methodological advances and best practices implemented in the toolbox, including improved measures of representational distances, evaluators for representational models, and statistical inference methods.

While the relative impact of the manuscript is somewhat limited to the new contributions in this update (which are nonetheless very useful), the general toolbox - here thoroughly described and discussed - remains an invaluable contribution to the field and is well-received by the cognitive and computational neuroscience communities.

Strengths:

A key strength of the work is the breadth and integration of the implemented methods. The updated version introduces several new features, such as additional comparators and dissimilarity estimators, that closely follow recent methodological developments in the field. These enhancements build on an already extensive set of functionalities, offering seamless support for RSA analyses across a wide variety of data sources, including deep neural networks, fMRI, EEG, and electrophysiological recordings.

The toolbox also integrates effectively with the broader open-source ecosystem, providing compatibility with BIDS formats and outputs from widely used neuroscience software. This integration will make it easier for researchers to incorporate rsatoolbox into existing workflows. The documentation is extensive, and the scope of functionality - from dissimilarity estimation to statistical inference - is impressive.

For researchers already familiar with RSA, rsatoolbox offers a coherent environment that can streamline analyses, promote methodological consistency, and encourage best practices.

Weaknesses:

While I enjoyed reading the manuscript - and even more so exploring the toolbox - I have some comments for the authors. None of these points is strictly major, and I leave it to the authors' discretion whether to act on them, but addressing them could make the manuscript an even more valuable resource for those approaching RSA.

(1) While several estimators and comparators are implemented, Figure 4 appears to suggest that only a subset should be used in practice. This raises the question of whether the remaining options are necessary, and under what circumstances they might be preferable. Although it is likely that different measures are suited to different scenarios, this is not clearly explained in the manuscript. As presented, a reader following the manuscript's guidance might rely on only a few of the available comparators and estimators without understanding the rationale. It would be helpful if the authors could provide practical examples illustrating when one measure might be preferred over another, and how different measures behave under varying conditions-for instance, in what situations the user should choose manifold similarity versus Bures similarity?

(2) The comparison to other RSA tools is minimal, making it challenging to place rsatoolbox in the broader landscape of available resources. Although the authors mention some existing RSA implementations, they do not provide a detailed comparison of features or performance between their toolbox and alternatives.

(3) Finally, given the growing interest in comparing neural network models with brain data, a more detailed discussion of how the toolbox can be applied to common questions in this area would be a valuable addition.

Reviewer #2 (Public review):

Summary:

The manuscript, "A Python Toolbox for Representational Similarity Analysis", presents an overview of the RSAToolbox, including a review of the methods it implements (some of which are more recently developed) and recommendations for constructing RSA analysis pipelines. It is encouraging to see that this toolbox, which has existed in both Python and other forms, continues to be actively developed and maintained.

Strengths:

The authors do a nice job reviewing the history of RSA analysis while introducing the methods within the toolbox. It is helpful that the authors discuss when and how to apply specific measures to different data types (e.g., why Euclidean or Mahalanobis distances are suboptimal for spike data). The manuscript strikes a valuable balance between theoretical background and hands-on instruction. The inclusion of decision-making aids, such as the Euler diagram for selecting similarity measures, and well-maintained demo scripts (available on GitHub), enhance the manuscript's utility as a practical guide.

Overall, this paper will be particularly useful to researchers new to RSA and those interested in performing a rigorous analysis using this framework. The manuscript and accompanying toolbox provide everything a researcher needs to get started, provided they take the time to engage with the methodological details and references offered

Weaknesses:

While the links to the demos in the figure legend did not work for me, it was easy to locate the current demos online, and it's encouraging to see that they are actively maintained. One small issue is that a placeholder ("XXX") remains in the description of Figure 3b and should be corrected.

Reviewer #1 (Public review):

This is an interesting and timely computational study using molecular dynamics simulation as well as quantum mechanical calculation to address why tyrosine (Y), as part of an intrinsically disordered protein (IDP) sequence, has been observed experimentally to be stronger than phenylalanine (F) as a promoter for biomolecular phase separation. Notably, the authors identified the aqueous nature of the condensate environment and the corresponding dielectric and hydrogen bonding effects as a key to understand the experimentally observed difference. This principle is illustrated by the difference in computed transfer free energy of Y- and F-containing pentapeptides into solvent with various degrees of polarity. The elucidation offered by this work is important. The computation appears to be carefully executed, the results are valuable, and the discussion is generally insightful. However, there is room for improvement in some parts of the presentation in terms of accuracy and clarity, including, e.g., the logic of the narrative should be clarified with additional information (and possibly additional computation), and the current effort should be better placed in the context of prior relevant theoretical and experimental works on cation-π interactions in biomolecules and dielectric properties of biomolecular condensates. Accordingly, this manuscript should be revised to address the following, with added discussion as well as inclusion of references mentioned below.

(1) Page 2, line 61: "Coarse-grained simulation models have failed to account for the greater propensity of arginine to promote phase separation in Ddx4 variants with Arg to Lys mutations (Das et al., 2020)". As it stands, this statement is not accurate, because the cited reference to Das et al. showed that although some coarse-grained model, namely the HPS model of Dignon et al., 2018 PLoS Comput did not capture the Arg to Lys trend, the KH model described in the same Dignon et al. paper was demonstrated by Das et al. (2020) to be capable of mimicking the greater propensity of Arg to promote phase separation than Lys. Accordingly, a possible minimal change that would correct the inaccuracy of this statement in the manuscript would be to add the word "Some" in front of "coarse-grained simulation models ...", i.e., it should read "Some coarse-grained simulation models have failed ...". In fact, a subsequent work [Wessén et al., J Phys Chem B 126: 9222-9245 (2022)] that applied the Mpipi interaction parameters (Joseph et al., 2021, already cited in the manuscript) showed that Mpipi is capable of capturing the rank ordering of phase separation propensity of Ddx4 variants, including a charge scrambled variant as well as both the Arg to Lys and the Phe to Ala variants (see Fig.11a of the above-cited Wessén et al. 2022 reference). The authors may wish to qualify their statements in the introduction to take note of these prior results. For example, they may consider adding a note immediately after the next sentence in the manuscript "However, by replacing the hydrophobicity scales ... (Das et al., 2020)" to refer to these subsequent findings in 2021-2022.

(2) Page 8, lines 285-290 (as well as the preceding discussion under the same subheading & Fig.4): "These findings suggest that ... is not primarily driven by differences in protein-protein interaction patterns ..." The authors' logic in terms of physical explanation is somewhat problematic here. In this regard, "Protein-protein interaction patterns" appears to be a straw man, so to speak. Indeed, who (reference?) has argued that the difference in the capability of Y and F in promoting phase separation should be reflected in the pairwise amino acid interaction pattern in a condensate that contains either only Y (and G, S) and only F (and G, S) but not both Y and F? Also, this paragraph in the manuscript seems to suggest that the authors' observation of similar contact patterns in the GSY and GSF condensates is "counterintuitive" given the difference in Y-Y and F-F potentials of mean force (Joseph et al., 2021); but there is nothing particularly counterintuitive about that. The two sets of observations are not mutually exclusive. For instance, consider two different homopolymers, one with a significantly stronger monomer-monomer attraction than the other. The condensates for the two different homopolymers will have essentially the same contact pattern but very different stabilities (different critical temperatures), and there is nothing surprising about it. In other words, phase separation propensity is not "driven" by contact pattern in general, it's driven by interaction (free) energy. The relevant issue here is total interaction energy or critical point of the phase separation. If it is computationally feasible, the authors should attempt to determine the critical temperatures for the GSY condensate versus the GSF condensate to verify that the GSY condensate has a higher critical temperature than the GSF condensate. That would be the most relevant piece of information for the question at hand.

(3) Page 9, lines 315-316: "...Our ε [relative permittivity] values ... are surprisingly close to that derived from experiment on Ddx4 condensates (45{plus minus}13) (Nott et al., 2015)". For accuracy, it should be noted here that the relative permittivity provided in the supplementary information of Nott et al. was not a direct experimental measurement but based on a fit using Flory-Huggins (FH), but FH is not the most appropriate theory for polymer with long-spatial-range Coulomb interactions. To this reviewer's knowledge, no direct measurement of relative permittivity in biomolecular condensates has been made to date. Explicit-water simulation suggests that relative permittivity of Ddx4 condensate with protein volume fraction ≈ 0.4 can have relative permittivity ≈ 35-50 (Das et al., PNAS 2020, Fig.7A), which happens to agree with the ε = 45{plus minus}13 estimate. This information should be useful to include in the authors' manuscript.

(4) As for the dielectric environment within biomolecular condensates, coarse-grained simulation has suggested that whereas condensates formed by essentially electric neutral polymers (as in the authors' model systems) have relative permittivities intermediate between that of bulk water and that of pure protein (ε = 2-4, or at most 15), condensates formed by highly charge polymers can have relative permittivity higher than that of bulk water [Wessén et al., J Phys Chem B 125:4337-4358 (2021), Fig.14 of this reference]. In view of the role of aromatic residues (mainly Y and F) in the phase separation of IDPs such as A1-LCD and LAF-1 that contain positively and negatively charged residues (Martin et al., 2020; Schuster et al., 2020, already cited in the manuscript), it should be useful to address briefly how the relationship between the relative phase-separation promotion strength of Y vs F and dielectric environment of the condensate may or may not be change with higher relative permittivities.

(5) The authors applied the dipole moment fluctuation formula (Eq.2 in the manuscript) to calculate relative permittivity in their model condensates. Does this formula apply only to an isotropic environment? The authors' model condensates were obtained from a "slab" approach (p.4) and thus the simulation box has a rectangular geometry. Did the authors apply their Eq.2 to the entire simulation box or only to the central part of the box with the condensate (see, e.g., Fig.3C in the manuscript). If the latter is the case, is it necessary to use a different dipole moment formula that distinguishes between the "parallel" and "perpendicular" components of the dipole moment (see, e.g., Eq.16 in the above-cited Wessén et al. 2021 paper). A brief added comments will be useful.

(6) With regard to the general role of Y and F in the phase separation of biomolecules containing positively charged Arg and Lys residues, the relative strength of cation-π interactions (cation-Y vs cation-F) should be addressed (in view of the generality implied by the title of the manuscript), or at least discussed briefly in the authors' manuscript if a detailed study is beyond the scope of their current effort. It has long been known that in the biomolecular context, cation-Y is slightly stronger than cation-F, whereas cation-tryptophan (W) is significantly stronger than either cation-Y and cation-F [Wu & McMahon, JACS 130:12554-12555 (2008)]. Experimental data from a study of EWS (Ewing sarcoma) transactivation domains indicated that Y is a slightly stronger promoter than F for transcription, whereas W is significantly stronger than either Y or F [Song et al., PLoS Comput Biol 9:e1003239 (2013)]. In view of the subsequent general recognition that "transcription factors activate genes through the phase-separation capacity of their activation domain" [Boija et al., Cell 175:1842-1855.e16 (2018)] which is applicable to EWS in particular [Johnson et al., JACS 146:8071-8085 (2024)], the experimental data in Song et al. 2013 (see Fig.3A of this reference) suggests that cation-Y interactions are stronger than cation-F interactions in promoting phase separation, thus generalizing the authors' observations (which focus primarily on Y-Y, Y-F and F-F interactions) to most situations in which cation-Y and cation-F interactions are relevant to biomolecular condensation.

(7) Page 9: The observation of a weaker effective F-F (and a few other nonpolar-nonpolar) interaction in a largely aqueous environment (as in an IDP condensate) than in a nonpolar environment (as in the core of a folded protein) is intimately related to (and expected from) the long-recognized distinction between "bulk" and "pair" as well as size dependence of hydrophobic effects that have been addressed in the context of protein folding [Wood & Thompson, PNAS 87:8921-8927 (1990); Shimizu & Chan, JACS 123:2083-2084 (2001); Proteins 49:560-566 (2002)]. It will be useful to add a brief pointer in the current manuscript to this body of relevant resource in protein science.

Comments on revisions:

The authors have largely addressed my previous concerns and the manuscript has been substantially improved. Nonetheless, it will benefit the readers more if the authors had included more of the relevant references provided in my previous review so as to afford a broader and more accurate context to the authors' effort. This deficiency is particularly pertinent for point number 6 in my previous report about cation-pi interactions. The authors have now added a brief discussion but with no references on the rank ordering of Y, F, and W interactions. I cannot see how providing additional information about a few related works could hurt. Quite the contrary, having the references will help readers establish scientific connections and contribute to conceptual advance.

Reviewer #2 (Public review):

Summary:

In this preprint, De Sancho and López use alchemical molecular dynamics simulations and quantum mechanical calculations to elucidate the origin of the observed preference of Tyr over Phe in phase separation. The paper is well written, and the simulations conducted are rigorous and provide good insight into the origin of the differences between the two aromatic amino acids considered.

Strengths:

The study addresses a fundamental discrepancy in the field of phase separation where the predicted ranking of aromatic amino acids observed experimentally is different from their anticipated rankings when considering contact statistics of folded proteins. While the hypothesis that the difference in the microenvironment of the condensed phase and hydrophobic core of folded proteins underlies the different observations, this study provides a quantification of this effect. Further, the demonstration of the crossover between Phe and Tyr as a function of the dielectric is interesting and provides further support for the hypothesis that the differing microenvironments within the condensed phase and the core of folded proteins is the origin of the difference between contact statistics and experimental observations in phase separation literature. The simulations performed in this work systematically investigate several possible explanations and therefore provide depth to the paper.