Reviewer #2 (Public Review):

Summary:

Turning behavior plays a crucial role in animal exploration and escape responses, regardless of the presence or absence of environmental cues. These turns can be broadly categorized into two categories: strong reorientations, characterized by sudden changes in path directionality, and smooth turns, which involve gradual changes in the direction of motion, leading to sinuosity and looping patterns. One of the key model animals to study these behaviors is the nematode Caenorhabditis elegans, in which the role of strong reorientations has been thoroughly studied. Despite their impact on trajectories, smooth turns have received less attention and remain poorly understood. This study addresses this gap in the literature, by studying the interplay between smooth turns and strong reorientations in nematodes moving in a uniform environment, surrounded by an aversive barrier. The authors use this set-up to study both exploration behavior (when the worm is far from the aversive barrier) and avoidance behavior (when the worm senses the aversive barrier). The main claims of the paper are that (1) during exploratory behavior, the parameters governing strong reorientations are optimized to compensate for the effect of smooth turns, increasing exploration efficiency, and (2) during avoidance, strong reorientations are biased towards the side that maximizes escape success. To support these two claims, the paper presents a detailed quantitative characterization of the statistics of smooth turns and strong reorientations. These results offer insights that may interest a diverse audience, including those in movement ecology, animal search behavior, and the study of Caenorhabditis elegans. In our opinion, the experimental work and data analysis are of the highest quality, resulting in a very clean characterization of C. elegans' turning behavior. However, the experimental design and data analyses presented are not fully aligned with some of the central conclusions drawn, and in particular, we believe that further work is needed to fully support the claim that strong reorientations are optimized to increase exploration efficiency.

Strengths:

The authors have addressed important questions in movement ecology through hypothesis-driven experiments. The choice of C. elegans as a model organism to investigate the impact of turning dynamics on escape and exploration is well-justified by its limited repertoire of strong reorientation behaviors and consistent turning bias across strains and individuals. The quality of the experimental data is very high, using state-of-the-art techniques, and a set-up where a robust and reproducible avoidance response can be studied. The data analysis benefits from state-of-the-art techniques and a deep understanding of C. elegans' behavior, resulting in a very clean and very clear set of results. We particularly appreciated the use of a ventral/dorsal reference system (rather than a left/right one), which is more natural and insightful. As a result, the paper presents one of the best characterizations of C. elegans sharp turning behavior published to date. We find that the claim that strong reorientations are chosen in a way that optimizes avoidance behavior is solid and well-supported. The manuscript is well-written and maintains a coherent line of reasoning throughout.

Weaknesses:

Our primary concerns revolve around the significance and rigor of the research on exploratory behavior. First, we believe that the experimental arena was too small for accurately observing the unfolding of exploration. The movement of assayed animals was clearly impaired by boundary effects, which obscured key elements of C. elegans exploratory behavior such as the mean square displacement or large-scale trajectory structures emerging from curvature bias. Second, we think that the proof that strong reorientations are optimized to maximize exploration performance is too indirect: it relies on a particular model with some unrealistic assumptions and lacks a quantification of the gains provided by the optimization to the individuals. We believe that a more thorough and direct analysis would be needed to fully support the claim.

Public Review:

The study addresses the role of enkephalins, which are specifically expressed by regulatory T cells (Treg), in sensory perception in mice. The authors used a combination of transcriptomic databases available online to characterize the molecular signature of Treg. The proenkephalin gene Penk is among the most enriched transcripts, suggesting that Treg plays an analgesic role through the release of endogenous opioids. In addition, in silico analysis suggests that Penk is regulated by the TNFR superfamily; this being experimentally confirmed. Using flow cytometry analysis, the authors then show that Penk is mostly expressed in Treg of the skin and colon, compared to other immune cells. Finally, genetic conditional excision of Penk, selectively in Treg, results in heat hypersensitivity, as assessed by behavior analysis.

Editors' note: The authors accepted most if not all the suggestions given by the reviewers and the revised version of the manuscript is substantially improved.

Reviewer #2 (Public Review):

Summary:

Several publications during the past years provided evidence that NMD protects tumor cells from being recognized by the immune system by suppressing the display of neoantigens, and hence NMD inhibition is emerging as a promising anti-cancer approach. However, the lack of an efficacious and specific small molecule NMD inhibitor with suitable pharmacological properties is currently a major bottleneck in the development of therapies that rely on NMD inhibition. In this manuscript, the authors describe their screen for identifying NMD inhibitors, which is based on isogenic cell lines that either express wild-type or NMD-sensitive transcript isoforms of p53 and STAG2. Using this setup, they screened a library of 2658 FDA-approved or late-phase clinical trial drugs and had 8 hits. Among them they further characterized LY3023414, showing that it inhibits NMD in cultured cells and in a mouse xenograft model, where it, however, was very toxic. Because LY3023414 was originally developed as a PI3K inhibitor, the authors claim that it inhibits NMD by inhibiting SMG1. While this is most likely true, the authors do not provide experimental evidence for this claim. Instead, they use this statement to switch their attention to another previously developed SMG1 inhibitor (SMG1i-11), of which they design and test several derivatives. Of these derivatives, KVS0001 showed the best pharmacological behavior. It upregulated NMD-sensitive transcripts in cultured cells and the xenograft mouse model, and two predicted neoantigens could indeed be detected by mass spectrometry when the respective cells were treated with KVS0001. A bispecific antibody targeting T cells to a specific antigen-HLA complex led to increased IFN-gamma release and killing of cancer cells expressing this antigen-HLA complex when they were treated with KVS0001. Finally, the authors show that renal (RENCA) or lung cancer cells (LLC) were significantly inhibited in tumor growth in immunocompetent mice treated with KVS0001. Overall, this establishes KVS0001 as a novel and promising ant-cancer drug that by inhibiting SMG1 (and therewith NMD) increases the neoantigen production in the cancer cells and reveals them to the body's immune system as "foreign".

Strengths:

The novelty and significance of this work consist in the development of a novel and - judging from the presented data - very promising NMD inhibiting drug that is suitable for applications in animals. This is an important advance for the field, as previous NMD inhibitors were not specific, lacked efficacy, or were very toxic and hence not suitable for animal application. It will be still a long way with many challenges ahead towards an efficacious NMD inhibitor that is safe for use in humans, but KVS0001 appears to be a molecule that bears promise for follow-up studies. In addition, while the idea of inhibiting NMD to trigger neoantigen production in cancer cells and so reveal them to the immune system has been around for quite some time, this work provides ample and compelling support for the feasibility of this approach, at least for tumors with a high mutational burden.

Main weaknesses:

There is a disconnect between the screen and the KVS0001 compound, that they describe and test in the second part of the manuscript since KVS0001 is a derivative of the SMG1 inhibitors developed by Gopalsamy et al. in 2012 and not of the lead compound identified in the screen (LY3023414). Because of high toxicity in the mouse xenograft experiments, the authors did not follow up LY3023414 but instead switched to the published SMG1i-11 drug of Gopalsamy and colleagues, a molecule that is widely used among NMD researchers for NMD inhibition in cultured cells. Therefore, in my view, the description of the screen is obsolete, and the paper could just start with the optimization of the pharmacological properties of SMG1i-11 and the characterization of KVS0001. Even though the screen is based on an elegant setup and was executed successfully, it was ultimately a failure as it didn't reveal a useful lead compound that could be further optimized.

Additional points:

- Compared to SMG1i-11, KVS0001 seems less potent in inhibiting SMG1 (higher IC50). It would therefore be important to also compare the specificity of both drugs for SMG1 over other kinases at the actually applied concentrations (1 uM for SMG1i-11, 5 uM for KVS0001). The Kinativ Assay (Fig. S13) was performed with 100 nM KVS0001, which is 50-fold less than the concentration used for functional assays and hence not really meaningful. In addition, more information on the pharmacokinetic properties and toxicology of KVS0001 would allow a better judgment of the potential of this molecule as a future therapeutic agent.<br /> - On many figures, the concentrations of the used drugs are missing. Please ensure that for every experiment that includes drugs, the drug concentration is indicated.<br /> - Do the authors have an explanation for why LY3023414 has a much stronger effect on the p53 than on the STAG2 nonsense allele (Fig. 1B, S8), whereas emetine upregulates the STAG2 nonsense alleles more than the p53 nonsense allele (Fig. S5). I find this curious, but the authors do not comment on it.<br /> - While it is a strength of the study that the NMD inhibitors were validated on many different truncation mutations in different cell lines, it would help readers if a table or graphic illustration was included that gives an overview of all mutant alleles tested in this study (which gene, type of mutation, in which cell type). In the current version, this information is scattered throughout the manuscript.<br /> - Lines 194 and 302: That SMG1i-11 was highly insoluble in the hands of the authors is surprising. It is unclear why they used variant 11j, since variant 11e of this inhibitor is widely used among NMD researchers and readily dissolves in DMSO.<br /> - Line 296: The authors claim that they were able to show that LY3023414 inhibited the SMG1 kinase, which is not true. To show this, they would have for example to show that LY3023414 prevents SMG1-mediated UPF1 phosphorylation, as they did for KVS0001 and SMG1i-11 in Fig. 3F. Unless the authors provide this data, the statement should be deleted or modified.

Comments on the revised version:

- The authors have satisfactorily addressed all my "Additional points" listed above.

- With the new publishing model of Life, the authors ultimately decide on whether or not to follow reviewers suggestions, and in this case, the authors decided (against my suggestion) to leave the screening part in the manuscript, although it did not result in a useful lead compound. They argue it helped them define in an unbiased way SMG1 as the ideal target for NMD disruption. I would counterargue that this has been known in the field for quite a while.

- One last suggestion I have to the authors would be to modify the statement in the abstract "This led to the design of a novel SMG1 inhibitor", because what they call "novel" is, in reality, a chemical improvement of the pharmacological properties of a previously reported SMG1 inhibitor (Gopalsamy et al., 2012).

Reviewer #2 (Public Review):

Main comment from 1st review:

Weaknesses:<br /> The modeling is interesting, with the integration of tension through tension triangulation around vertices and thus integrating force inference directly in the vertex model. However, the authors are not using it to test their hypothesis and support their analysis at the tissue level. Thus, although interesting, the analysis at the tissue level stays mainly descriptive.

Comments on the revised version:

My main concern was that the author did not use the analysis of mutant contexts such as Snail and Twist to confirm their predictions. They made a series of modifications, clarifying their conclusions. In particular, they now included an analysis of Snail mutant and show that isogonal deformations in the ventro-lateral regions are absent when the external pulling force of the VF is abolished, supporting the idea that isogonal strain could be used as an indicator of external forces (Fig7 and S6).

They further discuss their results in the context of what was published regarding the mutant backgrounds (fog, torso-like, scab, corkscrew, ksr) where midgut invagination is disrupted, and where germ band buckles, and propose that this supports the importance of internal versus external forces driving GBE.<br /> Overall, these modifications, in addition to clarifications in the text, clearly strengthen the manuscript.

Reviewer #1 (Public Review):

Summary and strength:<br /> The authors undertook to assemble and annotate the genome sequence of the Malabar grouper fish, with the aim to provide molecular resources for fundamental and applied research. Even though this is more mainstream, the task is still daunting and labor intensive. Currently, high quality and fully annotated genome sequences are of strategic importance in modern biology. The authors make use of the resource to address the endocrine control of an ecologically and developmentally relevant life cycle transition, metamorphosis. As opposed to amphibian and flat fish where body plan changes, fish metamorphosis is anatomically more subtle and much less known, although it is clear that thyroid hormone (TH) signaling is a key player. The authors thus provide a repertoire of TH-relevant gene expression changes during development and across post-embryonic transitions and correlate developmental stages with changes of gene expression. Overall, this work represents a significant advance in the field.

Fish 'metamorphosis' is well known because it is not as spectacular as amphibians. This work clearly provides technical and theoretical resources to address in a more systematic manner the molecular changes occurring during development and post-embryonic transitions. Heterochrony is a major source of functional and life cycle diversity in fish, which blurs our anatomy-based understanding of fish biology, and has a direct impact on the protocols and rearing procedures used to produce live stocks. This work illustrates how, by using genomics coupled to simple experimental endocrinology, one directly addresses these challenges.

Reviewer #1 (Public Review):

The authors present data on outer membrane vesicle (OMV) production in different mutants, but they state that this is beyond the scope of the current manuscript, which I disagree with. This data could provide valuable physiological context that is otherwise lacking. The preliminary blots suggest that YafK does not alter OMV biogenesis. I recommend repeating these blots with appropriate controls, such as blotting for proteins in the culture media, an IM protein, periplasmic protein and an OM protein to strengthen the reliability of these findings. Including this data in the manuscript, even if it does not directly support the initial hypothesis, would enhance the physiological relevance of the study. Currently, the manuscript relies completely on the experimental setup (labeling-mass spec) previously developed by the authors, which limits the broader scope and interpretability of this study.

Additionally susceptibility of strains to detergents like SDS can be tested to provide a much needed physisological context to the study.

In summary, the authors should consider revising the manuscript to improve clarity, substantiate their claims with more detailed evidence, and include additional experimental results that provide necessary physiological context to their study.

Reviewer #2 (Public Review):

Summary:<br /> The authors of this study have sought to better understand the timing and location of the attachment of the lpp lipoprotein to the peptidoglycan in E. coli, and to determine whether YafK is the hydrolase that cleaves lpp from the peptidoglycan.

Strengths:<br /> The method is relatively straightforward. The authors are able to draw some clear conclusions from their results, that lpp molecules get cleaved from the peptidoglycan and then re-attached, and that YafK is important for that cleavage.

Weaknesses:<br /> Figure 3 and 4 - why are the data shown here only two biological replicates, when there are 3-5 replicates shown in table S1 and S2? This makes it seem like you are cherry picking your favorite replicates. Please present the data as the mean of all the replicates performed, with error shown on the graph.

This work will have a moderate impact on the field of research in which the connections between the OM and peptidoglycan are being studied in E. coli. Since lpp is not widely conserved in gram negatives, the impact across species is not clear. The authors do not discuss the impact of their work in depth.

Reviewer #1 (Public Review):

Koren et al. derive and analyse a spiking network model optimised to represent external signals using the minimum number of spikes. Unlike most prior work using a similar setup, the network includes separate populations of excitatory and inhibitory neurons. The authors show that the optimised connectivity has a like-to-like structure, leading to the experimentally observed phenomenon of feature competition. They also characterise the impact of various (hyper)parameters, such as adaptation timescale, ratio of excitatory to inhibitory cells, regularisation strength, and background current. These results add useful biological realism to a particular model of efficient coding. However, not all claims seem fully supported by the evidence. Specifically, several biological features, such as the ratio of excitatory to inhibitory neurons, which the authors claim to explain through efficient coding, might be contingent on arbitrary modelling choices. In addition, earlier work has already established the importance of structured connectivity for feature competition. A clearer presentation of modelling choices, limitations, and prior work could improve the manuscript.

Major comments:

(1) Much is made of the 4:1 ratio between excitatory and inhibitory neurons, which the authors claim to explain through efficient coding. I see two issues with this conclusion: (i) The 4:1 ratio is specific to rodents; humans have an approximate 2:1 ratio (see Fang & Xia et al., Science 2022 and references therein); (ii) the optimal ratio in the model depends on a seemingly arbitrary choice of hyperparameters, particularly the weighting of encoding error versus metabolic cost. This second concern applies to several other results, including the strength of inhibitory versus excitatory synapses. While the model can, therefore, be made consistent with biological data, this requires auxiliary assumptions.

(2) A growing body of evidence supports the importance of structured E-I and I-E connectivity for feature selectivity and response to perturbations. For example, this is a major conclusion from the Oldenburg paper (reference 62 in the manuscript), which includes extensive modelling work. Similar conclusions can be found in work from Znamenskiy and colleagues (experiments and spiking network model; bioRxiv 2018, Neuron 2023 (ref. 82)), Sadeh & Clopath (rate network; eLife, 2020), and Mackwood et al. (rate network with plasticity; eLife, 2021). The current manuscript adds to this evidence by showing that (a particular implementation of) efficient coding in spiking networks leads to structured connectivity. The fact that this structured connectivity then explains perturbation responses is, in the light of earlier findings, not new.

(3) The model's limitations are hard to discern, being relegated to the manuscript's last and rather equivocal paragraph. For instance, the lack of recurrent excitation, crucial in neural dynamics and computation, likely influences the results: neuronal time constants must be as large as the target readout (Figure 4), presumably because the network cannot integrate the signal without recurrent excitation. However, this and other results are not presented in tandem with relevant caveats.

(4) On repeated occasions, results from the model are referred to as predictions claimed to match the data. A prediction is a statement about what will happen in the future - but most of the "predictions" from the model are actually findings that broadly match earlier experimental results, making them "postdictions". This distinction is important: compared to postdictions, predictions are a much stronger test because they are falsifiable. This is especially relevant given (my impression) that key parameters of the model were tweaked to match the data.

Reviewer #2 (Public Review):

Summary:

In this work, the authors present a biologically plausible, efficient E-I spiking network model and study various aspects of the model and its relation to experimental observations. This includes a derivation of the network into two (E-I) populations, the study of single-neuron perturbations and lateral-inhibition, the study of the effects of adaptation and metabolic cost, and considerations of optimal parameters. From this, they conclude that their work puts forth a plausible implementation of efficient coding that matches several experimental findings, including feature-specific inhibition, tight instantaneous balance, a 4 to 1 ratio of excitatory to inhibitory neurons, and a 3 to 1 ratio of I-I to E-I connectivity strength. It thus argues that some of these observations may come as a direct consequence of efficient coding.

Strengths:

While many network implementations of efficient coding have been developed, such normative models are often abstract and lacking sufficient detail to compare directly to experiments. The intention of this work to produce a more plausible and efficient spiking model and compare it with experimental data is important and necessary in order to test these models.

In rigorously deriving the model with real physical units, this work maps efficient spiking networks onto other more classical biophysical spiking neuron models. It also attempts to compare the model to recent single-neuron perturbation experiments, as well as some long-standing puzzles about neural circuits, such as the presence of separate excitatory and inhibitory neurons, the ratio of excitatory to inhibitory neurons, and E/I balance. One of the primary goals of this paper, to determine if these are merely biological constraints or come from some normative efficient coding objective, is also important.

Though several of the observations have been reported and studied before (see below), this work arguably studies them in more depth, which could be useful for comparing more directly to experiments.

Weaknesses:

Though the text of the paper may suggest otherwise, many of the modeling choices and observations found in the paper have been introduced in previous work on efficient spiking models, thereby making this work somewhat repetitive and incremental at times. This includes the derivation of the network into separate excitatory and inhibitory populations, discussion of physical units, comparison of voltage versus spike-timing correlations, and instantaneous E/I balance, all of which can be found in one of the first efficient spiking network papers (Boerlin et al. 2013), as well as in subsequent papers. Metabolic cost and slow adaptation currents were also presented in a previous study (Gutierrez & Deneve 2019). Though it is perfectly fine and reasonable to build upon these previous studies, the language of the text gives them insufficient credit.

Furthermore, the paper makes several claims of optimality that are not convincing enough, as they are only verified by a limited parameter sweep of single parameters at a time, are unintuitive and may be in conflict with previous findings of efficient spiking networks. This includes the following. Coding error (RMSE) has a minimum at intermediate metabolic cost (Figure 5B), despite the fact that intuitively, zero metabolic cost would indicate that the network is solely minimizing coding error and that previous work has suggested that additional costs bias the output. Coding error also appears to have a minimum at intermediate values of the ratio of E to I neurons (effectively the number of I neurons) and the number of encoded variables (Figures 6D, 7B). These both have to do with the redundancy in the network (number of neurons for each encoded variable), and previous work suggests that networks can code for arbitrary numbers of variables provided the redundancy is high enough (e.g., Calaim et al. 2022). Lastly, the performance of the E-I variant of the network is shown to be better than that of a single cell type (1CT: Figure 7C, D). Given that the E-I network is performing a similar computation as to the 1CT model but with more neurons (i.e., instead of an E neuron directly providing lateral inhibition to its neighbor, it goes through an interneuron), this is unintuitive and again not supported by previous work. These may be valid emergent properties of the E-I spiking network derived here, but their presentation and description are not sufficient to determine this.

Alternatively, the methodology of the model suggests that ad hoc modeling choices may be playing a role. For example, an arbitrary weighting of coding error and metabolic cost of 0.7 to 0.3, respectively, is chosen without mention of how this affects the results. Furthermore, the scaling of synaptic weights appears to be controlled separately for each connection type in the network (Table 1), despite the fact that some of these quantities are likely linked in the optimal network derivation. Finally, the optimal threshold and metabolic constants are an order of magnitude larger than the synaptic weights (Table 1). All of these considerations suggest one of the following two possibilities. One, the model has a substantial number of unconstrained parameters to tune, in which case more parameter sweeps would be necessary to definitively make claims of optimality. Or two, parameters are being decoupled from those constrained by the optimal derivation, and the optima simply corresponds to the values that should come out of the derivation.

Reviewer #3 (Public Review):

Summary:

In their paper the authors tackle three things at once in a theoretical model: how can spiking neural networks perform efficient coding, how can such networks limit the energy use at the same time, and how can this be done in a more biologically realistic way than previous work?

They start by working from a long-running theory on how networks operating in a precisely balanced state can perform efficient coding. First, they assume split networks of excitatory (E) and inhibitory (I) neurons. The E neurons have the task to represent some lower dimensional input signal, and the I neurons have the task to represent the signal represented by the E neurons. Additionally, the E and I populations should minimize an energy cost represented by the sum of all spikes. All this results in two loss functions for the E and I populations, and the networks are then derived by assuming E and I neurons should only spike if this improves their respective loss. This results in networks of spiking neurons that live in a balanced state, and can accurately represent the network inputs.

They then investigate in-depth different aspects of the resulting networks, such as responses to perturbations, the effect of following Dale's law, spiking statistics, the excitation (E)/inhibition (I) balance, optimal E/I cell ratios, and others. Overall, they expand on previous work by taking a more biological angle on the theory and showing the networks can operate in a biologically realistic regime.

Strengths:

(1) The authors take a much more biological angle on the efficient spiking networks theory than previous work, which is an essential contribution to the field.

(2) They make a very extensive investigation of many aspects of the network in this context, and do so thoroughly.

(3) They put sensible constraints on their networks, while still maintaining the good properties these networks should have.

Weaknesses:

(1) The paper has somewhat overstated the significance of their theoretical contributions, and should make much clearer what aspects of the derivations are novel. Large parts were done in very similar ways in previous papers. Specifically: the split into E and I neurons was also done in Boerlin et al (2008) and in Barrett et al (2016). Defining the networks in terms of realistic units was already done by Boerlin et al (2008). It would also be worth it to discuss Barrett et al (2016) specifically more, as there they also use split E/I networks and perform biologically relevant experiments.

(2) It is not clear from an optimization perspective why the split into E and I neurons and following Dale's law would be beneficial. While the constraints of Dale's law are sensible (splitting the population in E and I neurons, and removing any non-Dalian connection), they are imposed from biology and not from any coding principles. A discussion of how this could be done would be much appreciated, and in the main text, this should be made clear.

(3) Related to the previous point, the claim that the network with split E and I neurons has a lower average loss than a 1 cell-type (1-CT) network seems incorrect to me. Only the E population coding error should be compared to the 1-CT network loss, or the sum of the E and I populations (not their average). In my author recommendations, I go more in-depth on this point.

(4) While the paper is supposed to bring the balanced spiking networks they consider in a more experimentally relevant context, for experimental audiences I don't think it is easy to follow how the model works, and I recommend reworking both the main text and methods to improve on that aspect.

Assessment and context:

Overall, although much of the underlying theory is not necessarily new, the work provides an important addition to the field. The authors succeeded well in their goal of making the networks more biologically realistic, and incorporating aspects of energy efficiency. For computational neuroscientists, this paper is a good example of how to build models that link well to experimental knowledge and constraints, while still being computationally and mathematically tractable. For experimental readers, the model provides a clearer link between efficient coding spiking networks to known experimental constraints and provides a few predictions.

Reviewer #1 (Public Review):

Summary:

The question of whether eyespots mimic eyes has certainly been around for a very long time and led to a good deal of debate and contention. This isn't purely an issue of how eyespots work either, but more widely an example of the potential pitfalls of adopting 'just-so-stories' in biology before conducting the appropriate experiments. Recent years have seen a range of studies testing eye mimicry, often purporting to find evidence for or against it, and not always entirely objectively. Thus, the current study is very welcome, rigorously analysing the findings across a suite of papers based on evidence/effect sizes in a meta-analysis.

Strengths:

The work is very well conducted, robust, objective, and makes a range of valuable contributions and conclusions, with an extensive use of literature for the research. I have no issues with the analysis undertaken, just some minor comments on the manuscript. The results and conclusions are compelling. It's probably fair to say that the topic needs more experiments to really reach firm conclusions but the authors do a good job of acknowledging this and highlighting where that future work would be best placed.

Weaknesses:

There are few weaknesses in this work, just some minor amendments to the text for clarity and information.

Reviewer #2 (Public Review):

Many prey animals have eyespot-like markings (called eyespots) which have been shown in experiments to hinder predation. However, why eyespots are effective against predation has been debated. The authors attempt to use a meta-analytical approach to address the issue of whether eye-mimicry or conspicuousness makes eyespots effective against predation. They state that their results support the importance of conspicuousness. However, I am not convinced by this.

There have been many experimental studies that have weighed in on the debate. Experiments have included manipulating target eyespot properties to make them more or less conspicuous, or to make them more or less similar to eyes. Each study has used its own set of protocols. Experiments have been done indoors with a single predator species, and outdoors where, presumably, a large number of predator species predated upon targets. The targets (i.e, prey with eyespot-like markings) have varied from simple triangular paper pieces with circles printed on them to real lepidopteran wings. Some studies have suggested that conspicuousness is important and eye-mimicry is ineffective, while other studies have suggested that more eye-like targets are better protected. Therefore, there is no consensus across experiments on the eye-mimicry versus conspicuousness debate.

The authors enter the picture with their meta-analysis. The manuscript is well-written and easy to follow. The meta-analysis appears well-carried out, statistically. Their results suggest that conspicuousness is effective, while eye-mimicry is not. I am not convinced that their meta-analysis provides strong enough evidence for this conclusion. The studies that are part of the meta-analysis are varied in terms of protocols, and no single protocol is necessarily better than another. Support for conspicuousness has come primarily from one research group (as acknowledged by the authors), based on a particular set of protocols.

Furthermore, although conspicuousness is amenable to being quantified, for e.g., using contrast or size of stimuli, assessment of 'similarity to eyes' is inherently subjective. Therefore, manipulation of 'similarity to eyes' in some studies may have been subtle enough that there was no effect.

There are a few experiments that have indeed supported eye-mimicry. The results from experiments so far suggest that both eye-mimicry and conspicuousness are effective, possibly depending on the predator(s). Importantly, conspicuousness can benefit from eye-mimicry, while eye-mimicry can benefit from conspicuousness.

Therefore, I argue that generalizing based on a meta-analysis of a small number of studies that conspicuousness is more important than eye-mimicry is not justified. To summarize, I am not convinced that the current study rules out the importance of eye-mimicry in the evolution of eyespots, although I agree with the authors that conspicuousness is important.

Reviewer #1 (Public Review):

Summary:

Weiss and co-authors presented a versatile probabilistic tool. aTrack helps in classifying tracking behaviors and understanding important parameters for different types of single particle motion types: Brwonian, Confined, or Directed motion. The tool can be used further to analyze populations of tracks and the number of motion states. This is a stand-alone software package, making it user-friendly for a broad group of researchers.

Strengths:

This manuscript presents a novel method for trajectory analysis.

Weaknesses:

(1) In the results section, is there any reason to choose the specific range of track length for determining the type of motion? The starting value is fine, and would be short enough, but do the authors have anything to report about how much is too long for the model?

(2) Robustness to model mismatches is a very important section that the authors have uplifted diligently. Understanding where and how the model is limited is important. For example, the authors mentioned the limitation of trajectory length, do the authors have any information on the trajectory length range at which this method works accurately? This would be of interest to readers who would like to apply this method to their own data.

(3) aTrack extracts certain parameters from the trajectories to determine the motion types. However, it is not very clear how certain parameters are calculated. For example, is the diffusion coefficient D calculated from fitting, and how is the confinement factor defined and estimated, with equations? This information will help the readers to understand the principles of this algorithm.

(4) The authors mentioned the scenario where a particle may experience several types of motion simultaneously. How do these motions simulated and what do they mean in terms of motion types? Are they mixed motion (a particle switches motion types in the same trajectory) or do they simply present features of several motion types? It is not intuitive to the readers that a particle can be diffusive (Brownian) and direct at the same time.

Reviewer #2 (Public Review):

Summary:

The authors present a software package "aTrack" for identification of motion types and parameter estimation in single-particle tracking data. The software is based on maximum likelihood estimation of the time-series data given an assumed motion model and likelihood ratio tests for model selection. They characterized the performance of the software mostly on simulated data and showed that it is applicable to experimental data.

Strengths:

A potential advantage of the presented method is its wide applicability to different motion types.

Weaknesses:

(1) There has been a lot of similar work in this field. Even though the authors included many relevant citations in the introduction, it is still not clear what this work uniquely offers. Is it the first time that direct MLE of the time-series data was developed? Suggestions to improve would include (a) better wording in the introduction section, (b) comparing to other popular methods (based on MSD, step-size statistics (Spot-On, eLife 2018;7:e33125), for example) using the simulated dataset generated by the authors, (c) comparing to other methods using data set in challenges/competitions (Nat. Comm (2021) 12:6253).

(2) The Hypothesis testing method presented here has a number of issues: first, there is no definition of testing statistics. Usually, the testing statistics are defined given a specific (Type I and/or Type II) error rate. There is also no discussion of the specificity and sensitivity of the testing results (i.e. what's the probability of misidentification of a Brownian trajectory as directed? etc). Related, it is not clear what Figure 2e (and other similar plots) means, as the likelihood ratio is small throughout the parameter space. Also, for likelihood ratio tests, the authors need to discuss how model complexity affects the testing outcome (as more complex models tend to be more "likely" for the data) and also how the likelihood function is normalized (normalization is not an issue for MLE but critical for ratio tests).

(3) Relating to the mathematical foundation (Figure 1b). The measured positions are drawn as direct arrows from the real position states: this infers instantaneous localization. In reality, there is motion blur which introduces a correlation of the measured locations. Motion blur is known to introduce bias in SPT analysis, how does it affect the method here?

(4) The authors did not go through the interpretation of the figure. This may be a matter of style, but I find the figures ambiguous to interpret at times.

(5) It is not clear to me how the classification of the 5 motion types was accomplished.

(6) Figure 3. Caption: what is ((d_{est}-0.1)/0.1)? Also panel labeled as "d" should be "e".

Reviewer #1 (Public Review):

Summary:

As our understanding of the immune system increases it becomes clear that murine models of immunity cannot always prove an accurate model system for human immunity. However, mechanistic studies in humans are necessarily limited. To bridge this gap many groups have worked on developing humanised mouse models in which human immune cells are introduced into mice allowing their fine manipulation. However, since human immune cells will attack murine tissues, it has proven complex to establish a human-like immune system in mice. To help address this, Vecchione et al have previously developed several models using human cell transfer into mice with or without human thymic fragments that allow negative selection of autoreactive cells. In this report they focus on the examination of the function of the B-helper CD4 T-cell subsets T-follicular helper (Tfh) and T-peripheral helper (Tph) cells. They demonstrate that these cells are able to drive both autoantibody production and can also induce B-cell independent autoimmunity.

Strengths:

A strength of this paper is that currently there is no well-established model for Tfh or Tph in HIS mice and that currently there is no clear murine Tph equivalent making new models for the study of this cell type of value. Equally, since many HIS mice struggle to maintain effective follicular structures Tfh models in HIS mice are not well established giving additional value to this model.

Weaknesses:

A weakness of the paper is that the models seem to lack a clear ability to generate germinal centres. For Tfh it is unclear how we can interpret their function without the structure where they have the greatest influence. In some cases, the definition of Tph does not seem to differentiate well between Tph and highly activated CD4 T-cells in general.

Reviewer #2 (Public Review):

Summary:

Humanized mice, developed by transplanting human cells into immunodeficient NSG mice to recapitulate the human immune system, are utilized in basic life science research and preclinical trials of pharmaceuticals in fields such as oncology, immunology, and regenerative medicine. However, there are limitations to using humanized mice for mechanistic analysis as models of autoimmune diseases due to the unnatural T cell selection, antigen presentation/recognition process, and immune system disruption due to xenogeneic GVHD onset.

In the present study, Vecchione et al. detailed the mechanisms of autoimmune disease-like pathologies observed in a humanized mouse (Human immune system; HIS mouse) model, demonstrating the importance of CD4+ Tfh and Tph cells for the disease onset. They clarified the conditions under which these T cells become reactive using techniques involving the human thymus engraftment and mouse thymectomy, showing their ability to trigger B cell responses, although this was not a major factor in the mouse pathology. These valuable findings provide an essential basis for interpreting past and future autoimmune disease research conducted using HIS mice.

Strengths:

(1) Mice transplanted with human thymus and HSCs were repeatedly executed with sufficient reproducibility, with each experiment sometimes taking over 30 weeks and requiring desperate efforts. While the interpretation of the results is still debatable, these description is valuable knowledge for this field of research.

(2) Mechanistic analysis of T-B interaction in humanized mice, which has not been extensively addressed before, suggests part of the activation mechanism of autoreactive B cells. Additionally, the differences in pathogenicity due to T cell selection by either the mouse or human thymus are emphasized, which encompasses the essential mechanisms of immune tolerance and activation in both central and peripheral systems.

Weaknesses:

(1) In this manuscript, for example in Figure 2, the proportion of suppressive cells like regulatory T cells is not clarified, making it unclear to what extent the percentages of Tph or Tfh cells reflect immune activation. It would have been preferable to distinguish follicular regulatory T cells, at least. While Figure 3 shows Tregs are gated out using CD25- cells, it is unclear how the presence of Treg cells affects the overall cell population immunogenic functionally.

(2) The definition of "Disease" discussed after Figure 6 should be explicitly described in the Methods section. It seems to follow Khosravi-Maharlooei et al. 2021. If the disease onset determination aligns with GVHD scoring, generally an indicator of T cell response, it is unsurprising that B cell contribution is negligible. The accelerated disease onset by B cell depletion likely results from lymphopenia-induced T cell activation. However, this result does not prove that these mice avoid organ-specific autoimmune diseases mediated by auto-antibodies and the current conclusion by the authors may overlook significant changes. For instance, would defining Disease Onset by the appearance of circulating autoantibodies alter the result of Disease-Free curve? Are there possibly histological findings at the endpoint of the experiment suggesting tissue damage by autoantibodies?

(3) Helper functions, such as differentiating B cells into CXCR5+, were demonstrated for both Hu/Hu and Mu/Hu-derived T cells. This function seemed higher in Hu/Hu than in Mu/Hu. From the results in Figure 7-8, Hu/Hu Tph/Tfh cells have a stronger T cell identity and higher activation capacity in vivo on a per-cell basis than Mu/Hu's ones. However, Hu/Hu-T cells lacked an ability to induce class-switching in contrast to Mu/Hu's. The mechanisms causing these functional differences were not fully discussed. Discussions touching on possible changes in TCR repertoire diversity between Mu/Hu- and Hu/Hu- T cells would have been beneficial.

Reviewer #1 (Public Review):

Summary:

Cording et al. investigated how deletion of CNTNAP2, a gene associated with autism spectrum disorder, alters corticostriatal engagement and behavior. Specifically, the authors present slice electrophysiology data showing that striatal projection neurons (SPNs) are more readily driven to fire action potentials in response to stimulation of corticostriatal afferents, and this is due to increases in SPN intrinsic excitability rather than changes in excitatory or inhibitory synaptic inputs. The authors show that CNTNAP2 mice display repetitive behaviors, enhanced motor learning, and cognitive inflexibility. Overall the authors' conclusions are supported by their data, but a few claims could use some more evidence to be convincing.

Strengths:

The use of multiple behavioral techniques, both traditional and cutting-edge machine learning-based analyses, provides a powerful means of assessing repetitive behaviors and behavioral transitions/rigidity. Characterization of both excitatory and inhibitory synaptic responses in slice electrophysiology experiments offers a broad survey of the synaptic alterations that may lead to increased corticostriatal engagement of SPNs.

Weaknesses:

(1) The authors conclude that increased cortical engagement of SPNs is due to changes in SPN intrinsic excitability rather than synaptic strength (either excitatory or inhibitory). One weakness is that only AMPA receptor-mediated responses were measured. Though the holding potential used for experiments in Figure 1F-I wasn't clear, recordings were presumably performed at a hyperpolarized potential that limits NMDA receptor-mediated responses. Because the input-output experiments used to conclude that corticostriatal engagement of SPNs is elevated (Figure 1B-E) were conducted in the current clamp, it is possible that enhanced NMDA receptor engagement contributed to increased SPN responses to cortical stimulation. Confirming that NMDA receptor-mediated EPSC components are not altered would strengthen the main conclusion.

(2) Data clearly show that SPN intrinsic excitability is increased in knockout mice. Given that CNTNAP2 has been linked to potassium channel regulation, it would be helpful to show and quantify additional related electrophysiology data such as negative IV curve responses and action potential hyperpolarization.

(3) As it stands, the reported changes in dorsolateral striatum SPN excitability are only correlative with reported changes in repetitive behaviors, motor learning, and cognitive flexibility.

Reviewer #2 (Public Review):

Summary:

This is an important study characterizing striatal dysfunction and behavioral deficits in Cntnap2-/- mice. There is growing evidence suggesting that striatal dysfunction underlies core symptoms of ASD but the specific cellular and circuit level abnormalities disrupted by different risk genes remain unclear. This study addresses how the deletion of Cntnap2 affects the intrinsic properties and synaptic connectivity of striatal spiny projection neurons (SPN) of the direct (dSPN) and indirect (iSPN) pathways. Using Thy1-ChR2 mice and optogenetics the authors found increased firing of both types of SPNs in response to cortical afferent stimulation. However, there was no significant difference in the amplitude of optically-evoked excitatory postsynaptic currents (EPSCs) or spine density between Cntnap2-/- and WT SPNs, suggesting that the increased corticostriatal coupling might be due to changes in intrinsic excitability. Indeed, the authors found Cntnap2-/- SPNs, particularly dSPNs, exhibited higher intrinsic excitability, reduced rheobase current, and increased membrane resistance compared to WT SPNs. The enhanced spiking probability in Cntnap2-/- SPNs is not due to reduced inhibition. Despite previous reports of decreased parvalbumin-expressing (PV) interneurons in various brain regions of Cntnap2-/- mice, the number and function (IPSC amplitude and intrinsic excitability) of these interneurons in the striatum were comparable to WT controls.

This study also includes a comprehensive behavioral analysis of striatal-related behaviors. Cntnap2-/- mice demonstrated increased repetitive behaviors (RRBs), including more grooming bouts, increased marble burying, and increased nose poking in the holeboard assay. MoSeq analysis of behavior further showed signs of altered grooming behaviors and sequencing of behavioral syllables. Cntnap2-/- mice also displayed cognitive inflexibility in a four-choice odor-based reversal learning assay. While they performed similarly to WT controls during acquisition and recall phases, they required significantly more trials to learn a new odor-reward association during reversal, consistent with potential deficits in corticostriatal function.

Strengths:

This study provides significant contributions to the field. The finding of altered SPN excitability, the detailed characterization of striatal inhibition, and the comprehensive behavioral analysis are novel and valuable to understanding the pathophysiology of Cntnap2-/- mice.

Weaknesses:

(1) The approach based on Thy-ChR2 mice has the advantage of overcoming issues caused by injection efficiency and targeting variability. However, the spread of oEPSC amplitudes across mice shown in panels of Figure 1 G/I is very high with almost one order of magnitude difference between some mice. Given this is one of the most important points of the study it will be important to further analyze and discuss what this variability might be due to. Typically, in acute slice recordings, the within-animal variability is larger than the variability across animals. From the sample sizes reported it seems the authors sampled a large number of animals, but with a relatively low number of neurons per animal (per condition). Could this be one of the reasons for this variability?

(2) This is particularly important because the analysis of corticostriatal evoked APs in panels C and E is performed on pooled data without considering the variability in evoked current amplitudes across animals shown in G and I. Were the neurons in panels C/E recorded from the same mice as shown in G/I? If so, it would be informative to regress AP firing data (say at 20% LED) to the average oEPSC amplitude recorded on those mice at the same light intensity. However, if the low number of neurons recorded per mouse is due to technical limitations, then increasing the sample size of these experiments would strengthen the study.

(3) On a similar note, there is no discussion of why iSPNs also show increased corticostriatal evoked firing in Figure 1E, despite the difference in intrinsic excitability shown in Figure 3. This suggests other potential mechanisms that might underlie altered corticostriatal responses. Given the role of Caspr2 in clustering K channels in axons, altered presynaptic function or excitability could also contribute to this phenotype, but potential changes in PPR have not been explored in this study.

(4) Male and female SPNs have different intrinsic properties but the number and/or balance of M/F mice used for each experiment is not reported.

(5) There is no mention of how membrane resistance was calculated, and no I/V plots are shown.

(6) It would be interesting to see which behavior transitions most contribute to the decrease in entropy. Are these caused by repeated or perseverative grooming bouts? Or is this inflexibility also observed across other behaviors? The transition map in Figure S5 shows the overall number of syllables and transitions but not their sequence during behavior. Can this be analyzed by calculating the ratio of individual 𝑢𝑖 × 𝑝𝑖,𝑗 × log2 𝑝𝑖,𝑗 factors across genotypes?

Reviewer #3 (Public Review):

Summary:

The authors analyzed Cntnap2 KO mice to determine whether loss of the ASD risk gene CNTNAP2 alters the dorsal striatum's function.

Strengths:

The results demonstrate that loss of Cntnap2 results in increased excitability of striatal projection neurons (SPNs) and altered striatal-dependent behaviors, such as repetitive, inflexible behaviors. Unlike other brain areas and cell types, synaptic inputs onto SPNs were normal in Cntnap2 KO mice. The experiments are well-designed, and the results support the authors' conclusions.

Weaknesses:

The mechanism underlying SPN hyperexcitability was not explored, and it is unclear whether this cellular phenotype alone can account for the behavioral alterations in Cntnap2 KO mice. No clear explanation emerges for the variable phenotype in different brain areas and cell types.

Reviewer #1 (Public Review):

Summary:

Boldt et al test several possible relationships between trandiagnostically-defined compulsivity and cognitive offloading in a large online sample. To do so, they develop a new and useful cognitive task to jointly estimate biases in confidence and reminder-setting. In doing so, they find that over-confidence is related to less utilization of reminder-setting, which partially mediates the negative relationship between compulsivity and lower reminder-setting. The paper thus establishes that, contrary to the over-use of checking behaviors in patients with OCD, greater levels of transdiagnostically-defined compulsivity predict less deployment of cognitive offloading. The authors offer speculative reasons as to why (perhaps it's perfectionism in less clinically-severe presentations that lowers the cost of expending memory resources), and set an agenda to understand the divergence in cognition between clinical and nonclinical samples. Because only a partial mediation had robust evidence, multiple effects may be at play, whereby compulsivity impacts cognitive offloading via overconfidence and also by other causal pathways.

Strengths:

The study develops an easy-to-implement task to jointly measure confidence and replicates several major findings on confidence and cognitive-offloading. The study uses a useful measure of cognitive offloading - the tendency to set reminders to augment accuracy in the presence of experimentally manipulated costs. Moreover, the utilizes multiple measures of presumed biases - overall tendency to set reminders, the empirically estimated indifference point at which people engage reminders, and a bias measure that compares optimal indifference points to engage reminders relative to the empirically-observed indifference points. That the study observes convergenence along all these measures strengthens the inferences made relating compulsivity to the under-use of reminder-setting. Lastly, the study does find evidence for one of several a priori hypotheses and sets a compelling agenda to try to explain why such a finding diverges from an ostensible opposing finding in clinical OCD samples and the over-use of cognitive offloading.

Weaknesses:

Although I think this design and study are very helpful for the field, I felt that a feature of the design might reduce the tasks's sensitivity to measuring dispositional tendencies to engage cognitive offloading. In particular, the design introduces prediction errors, that could induce learning and interfere with natural tendencies to deploy reminder-setting behavior. These PEs comprise whether a given selected strategy will be or not be allowed to be engaged. We know individuals with compulsivity can learn even when instructed not to learn (e.g., Sharp, Dolan, and Eldar, 2021, Psychological Medicine), and that more generally, they have trouble with structure knowledge (eg Seow et al; Fradkin et al), and thus might be sensitive to these PEs. Thus, a dispositional tendency to set reminders might be differentially impacted for those with compulsivity after an NPE, where they want to set a reminder, but aren't allowed to. After such an NPE, they may avoid more so the tendency to set reminders. Those with compulsivity likely have superstitious beliefs about how checking behaviors leads to a resolution of catastrophes, which might in part originate from inferring structure in the presence of noise or from purely irrelevant sources of information for a given decision problem.

It would be good to know if such learning effects exist if they're modulated by PE (you can imagine PEs are higher if you are more incentivized - e.g., 9 points as opposed to only 3 points - to use reminders, and you are told you cannot use them), and if this learning effect confounds the relationship between compulsivity and reminder-setting.

A more subtle point, I think this study can be more said to be an exploration than a deductive test of a particular model -> hypothesis -> experiment. Typically, when we test a hypothesis, we contrast it with competing models. Here, the tests were two-sided because multiple models, with mutually exclusive predictions (over-use or under-use of reminders) were tested. Moreover, it's unclear exactly how to make sense of what is called the direct mechanism, which is supported by partial (as opposed to complete) mediation.

Reviewer #2 (Public Review):

Summary:

Boldt et al. investigated whether previously established relationships between transdiagnostic psychiatric symptom dimensions and confidence distortions would result in downstream influences on the confidence-related behaviour of reminder setting. 600 individuals from the general population completed a battery of psychiatric symptom questionnaires and an online reminder-setting task. In line with previous studies, individuals high in compulsivity (CIT) showed over-confidence in their task performance, whereas individuals high in anxious depression (AD) tended to be under-confident. Crucially, the over-confidence associated with CIT partially mediated a decreased tendency to use external reminders during task performance, whereas the under-confidence associated with AD did not result in any alteration in the external reminder setting. The authors suggest that metacognitive monitoring is impaired in CIT which has a knock-on effect on reminder setting behaviour, but that a direct link also exists between CIT and reduced reminder setting independently of confidence.

Strengths:

The study combines the latest advances in transdiagnostic approaches to psychopathology with a cleverly designed external reminder-setting task. The approach allows for investigation of what some of the downstream consequences associated with impaired metacognition in sub-clinical psychopathology may be.

The experimental design and hypotheses were pre-registered prior to data collection.

The manuscript is well written and rigorous analysis approaches are used throughout.

Weaknesses:

Participants only performed a single task so it remains unclear if the observed effects would generalise to reminder-setting in other cognitive domains.

The sample consisted of participants recruited from the general population. Future studies should investigate whether the effects observed extend to individuals with the highest levels of symptoms (including clinical samples).

Reviewer #1 (Public Review):

Summary:

In this manuscript, the authors investigate the impact of rare and extreme events on rodents' decision-making under risk, in gain and loss contexts. They describe the behavior of 20 rats performing a four-armed bandit task, where probabilistic gains (sugar pellets) and losses (time-out punishments) can - in some arms - incorporate extremely large - but rare - outcomes. They report that most rats are sensitive to rare and extreme outcomes despite their infrequent occurrence, and that this sensitivity is primarily driven by extreme loss events which they try to avoid, rather than extreme gains that they seek to obtain.

They finally propose a modification of standard reinforcement-learning, which features a specific sensitivity to rare and extreme outcomes and can account for the observed behavior.

Strengths:

The manuscript really taps into a surprisingly neglected but very relevant aspect of decision-making: the effect of rare and extreme events (REE). The authors have developed an experimental setup that seemingly allows investigation of this aspect, which is not trivial given the idiosyncratic properties of rare and extreme events.

The parameters of the experimental setup seem also to be well thought off: basically, in the absence of REE, some options are objectively better than others (because, in expectation, they overall deliver more food, or minimize time-out punishments), but this ordering reverses if REE are taken into account. This allows for a clean test of the integration of REE in the rodent's decision-making model.

The data is presented and analyzed in a very descriptive but exhaustive and transparent way, down to the description of individual rodent's behavior.

Weaknesses:

While the description and analyses of the behavioral patterns are rigorously done under the economic lens of risky decision-making, the authors' interpretation heavily relies on the assumption that rodents have built the correct model of the task during the training. Extensive details are provided about the training procedure, and the observed behavior at the end of the training, but it remains virtually impossible to disambiguate choices due to imperfect learning to choices made due to intrinsic preferences for risk or REE.

By nature, gains (food pellets) and losses (time-out punishments) are somewhat incommensurable so the interpretation of the asymmetry due to outcome valence is also subject to interpretation. There might be some additional subtleties due e.g. satiety that could come from gaining REE (i.e. the delivery of 80 pellets from the Jackpot).

In its current form, the paper is quite hard to digest. This is naturally the case with interdisciplinary work (here mixing economists and neurobiologists). But I am afraid that with the current frame, the paper is going to miss its target, in terms of audience.

The proposed model seems somewhat disconnected from the behavioral patterns: while the model suggests an effect of REE at the decision stage (i.e. with specific decision weights for those rare events), this formalism seems at odds with the observation that REE (notably in the loss domain) has an impact of subsequent behavior - (Black Swans tend to reinforce Total Sensitivity to REE) which rather suggests an effect at the learning stage.

Discussion:

This study convincingly demonstrates that REEs are processed rather uniquely, which makes sense given their evolutionary relevance. REE has indeed been somewhat neglected in previous research, and this study therefore opens an interesting new front on the fundamental aspects of decision under risk. The authors have devised an original theoretical and empirical framework that will be useful for the community, and the combination of economics analysis and rodent behavior constitutes a thought-provoking ground to think about the nature of risk preferences. The interpretation and mechanistic account of these aspects, as well as their generalizability outside the specific context of this study, remain to be strengthened.

Reviewer #2 (Public Review):

Summary:

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

Strengths:

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

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

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

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

Weaknesses:

(1) The primary issue with this work is that the primary experimental manipulation fails to isolate the rare, extreme events in choice. As I understand the task, in all the conditions with a rare extreme event (e.g., 80 pellets with probability epsilon), there is also a less-rare, less-extreme event (e.g., 12 pellets with probability 5). In addition, the variance differs between the two conditions. So, any impact attributable to the rare, extreme event could be due to the less rare event or due difference in the variance. The design does not support the conclusions. Finally, by deliberately confounding rarity and extremity, the design does not allow for assessing the impact of either aspect.

(2) The RL-modelling work also fails to show a specific impact of the rare extreme event. As best as I can understand Eq 2, the model provides a free parameter that adds a bonus to the value of either the two options with high-variance gains (A and V in the paper) or to the two options with high-variance losses (F and V in the paper). This parameter only depends on whether this option could have possibly yielded the rare, extreme outcome (i.e., based on the generative probability) and was not connected to its actual appearance. That makes it a free parameter that just bumps up (or down) the probability of selecting a pair of options. In the case of the "black swan" or high-variance loss conditions, this seems very much like a loss aversion parameter, but an additive one instead of a multiplicative one.

(3) The paper presented the methods and results with lots of neologisms and fairly obscure jargon (e.g., fragility, total REE sensitivity). That made it very hard to decipher exactly what was done and what was found. For example, on p. 4, the use of concave and convex was very hard to decipher; the text even has to repeat itself 3 times (i.e., "to repeat" and "in other words") and is still not clear. It would be much clearer (and probably accurate) to say that the options varied along the variance dimension, separately for gains and losses. Option A was low-variance gains and losses. Option B was low-variance losses and high-variance gains. Option C was high-variance losses and low-variance gains, and Option D was high-variance losses and gains. That tells much more clearly what the animals experienced without the reader having to master a set of new terminologies around fragility and robustness, which brings a set of theoretical assumptions unnecessarily into the description of the experimental design. In terms of results, "Black Swan" avoidance is more simply known as risk aversion for losses.

(4) Were the probabilities shuffled or truly random (seem to be fixed sequences, so neither)? What were the experienced probabilities? Given the fixed sequences, these experienced ("ex-post") probabilities, could differ tremendously from the scheduled ("ex ante") probabilities. It's quite possible that an animal never experienced the rare, extreme event for a specific option. It's even possible (if they only picked it on the 10th/60th choices by chance), that they only ever experienced that rare extreme event. This cannot be known given the information provided. The Supplemental info on p.55 only gives gross overall numbers but does not indicate what the rats experienced for each choice/option-which is what matters here. A simple table that indicates for each of the 4 options, how often they were selected, and how often the animals experienced each of the 6-8 possible outcome would make it much clearer how closely the experience matched the planned outcomes. In addition, by restricting the rare outcome to either the 10th or 60th activations in a session, these are not random. Did the animals learn this association?

(5) The choice data are only presented in an overprocessed fashion with a sum and a difference (in both figures and tables). The basic datum (probability/frequency of selecting each of the 4 options) is not provided directly, even if it can theoretically be inferred from the sum and the difference. To understand what the rats actually do, we first need to see how often they select each option, without these transformations.

(6) There is insufficient detail provided on the inferential statistical tests (e.g., no degrees of freedom or effect sizes), and only limited information on exactly what tests were run and how (bootstrapping, but little detail). Without code or data (only summary information is provided in the supplement), this is difficult to evaluate. In addition, the studies seem not to be pre-registered in any way, leaving many researchers with degrees of freedom. Were any alternative analysis pipelines attempted? Similarly, there were many sub-groupings of the animals, and then comparisons between them - were these post-hoc?

(7) On p. 17, there is an attempt to look at the impact of a rare, extreme event by plotting a measure of preference for the 10 trials before/after the rare, extreme event. In the human literature, the main impact of experiencing a rare, extreme event is what is known as the wavy recency effect (See Plonsky et al. 2015 in Psych Review for example). What this means is that there tends to be some immediate negative recency (e.g., avoiding a rare gain) followed by positive recency (e.g., chasing the rare gain). Using a 10-trial window would thus obscure any impact of this rare, extreme event. An analysis that looks at a time course trial-by-trial could reveal any impact.

(8) As I understood the method (p. 31), the assignment of options to physical locations was not random or counterbalanced, but deliberately biased to have one of the options in the preferred location. This would seem to create a bias towards a particular option and a bias away from the other options, which confounds the preference data in subsequent analyses.

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

(10) The paper does not sufficiently accurately represent the existing literature on human risky decision-making (with and without rare events). Here are a few examples of misrepresented and/or missing literature:<br /> -Most studies on decision-making do not only rely on p > 10% (as per p. 2). Maybe that is true with animals, but not a fair statement generally. Some do, and some don't. There is substantial literature looking at rarer events in both descriptions (most famously with Kahneman & Tversky's work), but also in experience (which is alluded to in reference 19). That reference is not only about the situation when choices are not repeated (e.g. the sampling paradigm), but also partial feedback and full-feedback situations.

The literature on learning from rewarding experiences in humans is obliquely referenced but not really incorporated. In short, there are two main findings - firstly people underweight rare events in experience; second, people overweight extreme outcomes in experience (both contrary to description). Some related papers are cited, but their content is not used or incorporated into the logic of the manuscript.

One recent study systematically examined rarity and extremity in human risky decision-making, which seems very relevant here: Mason et al. (2024). Rare and extreme outcomes in risky choice. Psychonomic Bulletin & Review, 31, 1301-1308.

There is a fair bit of research on the human perception of the risk of rare events (including from experience) and important events like climate. One notable paper is Newell et al (2015) in Nature Climate Change.

Reviewer #1 (Public Review):

Summary:

Lloyd et al employ an evolutionary comparative approach to study how sleep deprivation affects DNA damage repair in Astyanax mexicanus, using the cave vs surface species evolution as a playground. The work shows, convincingly, that the cavefish population has evolved an impaired DNA damage response both following sleep deprivation or a classical paradigm of DNA damage (UV).

Strengths:

The study employs a thorough multidisciplinary approach. The experiments are well conducted and generally well presented.

Weaknesses:

Having a second experimental mean to induce DNA damage would strengthen and generalise the findings.

Overall, the study represents a very important addition to the field. The model employed underlines once more the importance of using an evolutionary approach to study sleep and provides context and caveats to statements that perhaps were taken a bit too much for granted before. At the same time, the paper manages to have an extremely constructive approach, presenting the platform as a clear useful tool to explore the molecular aspects behind sleep and cellular damage in general. The discussion is fair, highlighting the strengths and weaknesses of the work and its implications.

Reviewer #2 (Public Review):

The manuscript investigates the relationship between sleep, DNA damage, and aging in the Mexican cavefish (Astyanax mexicanus), a species that exhibits significant differences in sleep patterns between surface-dwelling and cave-dwelling populations. The authors aim to understand whether these evolved sleep differences influence the DNA damage response (DDR) and oxidative stress levels in the brain and gut of the fish.

Summary of the Study:

The primary objective of the study is to determine if the reduced sleep observed in cave-dwelling populations is associated with increased DNA damage and altered DDR. The authors compared levels of DNA damage markers and oxidative stress in the brains and guts of surface and cavefish. They also analyzed the transcriptional response to UV-induced DNA damage and evaluated the DDR in embryonic fibroblast cell lines derived from both populations.

Strengths of the Study:

Comparative Approach:<br /> The study leverages the unique evolutionary divergence between surface and cave populations of A. mexicanus to explore fundamental biological questions about sleep and DNA repair.

Multifaceted Methodology:<br /> The authors employ a variety of methods, including immunohistochemistry, RNA sequencing, and in vitro cell line experiments, providing a comprehensive examination of DDR and oxidative stress.

Interesting Findings:

The study presents intriguing results showing elevated DNA damage markers in cavefish brains and increased oxidative stress in cavefish guts, alongside a reduced transcriptional response to UV-induced DNA damage.

Weaknesses of the Study:

Link to Sleep Physiology:<br /> The evidence connecting the observed differences in DNA damage and DDR directly to sleep physiology is not convincingly established. While the study shows distinct DDR patterns, it does not robustly demonstrate that these are a direct result of sleep differences.

Causal Directionality:<br /> The study fails to establish a clear causal relationship between sleep and DNA damage. It is possible that both sleep patterns and DDR responses are downstream effects of a common cause or independent adaptations to the cave environment.

Environmental Considerations:<br /> The lab conditions may not fully replicate the natural environments of the cavefish, potentially influencing the results. The impact of these conditions on the study's findings needs further consideration.

Photoreactivity in Albino Fish:<br /> The use of UV-induced DNA damage as a primary stressor may not be entirely appropriate for albino, blind cavefish. Alternative sources of genotoxic stress should be explored to validate the findings.

Assessment of the Study's Achievements:

The authors partially achieve their aims by demonstrating differences in DNA damage and DDR between surface and cavefish. However, the results do not conclusively support the claim that these differences are driven by or directly related to the evolved sleep patterns in cavefish. The study's primary claims are only partially supported by the data.

Impact and Utility:

The findings contribute valuable insights into the relationship between sleep and DNA repair mechanisms, highlighting potential areas of resilience to DNA damage in cavefish. While the direct link to sleep physiology remains unsubstantiated, the study's data and methods will be useful to researchers investigating evolutionary biology, stress resilience, and the molecular basis of sleep.

Reviewer #3 (Public Review):

Lloyd, Xia, et al. utilised the existence of surface-dwelling and cave-dwelling morphs of Astyanax mexicanus to explore a proposed link between DNA damage, aging, and the evolution of sleep. Key to this exploration is the behavioural and physiological differences between cavefish and surface fish, with cavefish having been previously shown to have low levels of sleep behaviour, along with metabolic alterations (for example chronically elevated blood glucose levels) in comparison to fish from surface populations. Sleep deprivation, metabolic dysfunction, and DNA damage are thought to be linked and to contribute to aging processes. Given that cavefish seem to show no apparent health consequences of low sleep levels, the authors suggest that they have evolved resilience to sleep loss. Furthermore, as extended wake and loss of sleep are associated with increased rates of damage to DNA (mainly double-strand breaks) and sleep is linked to repair of damaged DNA, the authors propose that changes in DNA damage and repair might underlie the reduced need for sleep in the cavefish morphs relative to their surface-dwelling conspecifics.

To fulfill their aim of exploring links between DNA damage, aging, and the evolution of sleep, the authors employ methods that are largely appropriate, and comparison of cavefish and surface fish morphs from the same species certainly provides a lens by which cellular, physiological and behavioural adaptations can be interrogated. Fluorescence and immunofluorescence are used to measure gut reactive oxygen species and markers of DNA damage and repair processes in the different fish morphs, and measurements of gene expression and protein levels are appropriately used. However, although the sleep tracking and quantification employed are quite well established, issues with the experimental design relate to attempts to link induced DNA damage to sleep regulation (outlined below). Moreover, although the methods used are appropriate for the study of the questions at hand, there are issues with the interpretation of the data and with these results being over-interpreted as evidence to support the paper's conclusions.

This study shows that a marker of DNA repair molecular machinery that is recruited to DNA double-strand breaks (γH2AX) is elevated in brain cells of the cavefish relative to the surface fish and that reactive oxygen species are higher in most areas of the digestive tract of the cavefish than in that of the surface fish. As sleep deprivation has been previously linked to increases in both these parameters in other organisms (both vertebrates and invertebrates), their elevation in the cavefish morph is taken to indicate that the cavefish show signs of the physiological effects of chronic sleep deprivation.

It has been suggested that induction of DNA damage can directly drive sleep behaviour, with a notable study describing both the induction of DNA damage and an increase in sleep/immobility in zebrafish (Danio rerio) larvae by exposure to UV radiation (Zada et al. 2021 doi:10.1016/j.molcel.2021.10.026). In the present study, an increase in sleep/immobility is induced in surface fish larvae by exposure to UV light, but there is no effect on behaviour in cavefish larvae. This finding is interpreted as representing a loss of a sleep-promoting response to DNA damage in the cavefish morph. However, induction of DNA damage is not measured in this experiment, so it is not certain if similar levels of DNA damage are induced in each group of intact larvae, nor how the amount of damage induced compares to the pre-existing levels of DNA damage in the cavefish versus the surface fish larvae. In both this study with A. mexicanus surface morphs and the previous experiments from Zada et al. in zebrafish, observed increases in immobility following UV radiation exposure are interpreted as following from UV-induced DNA damage. However, in interpreting these experiments it is important to note that the cavefish morphs are eyeless and blind. Intense UV radiation is aversive to fish, and it has previously been shown in zebrafish larvae that (at least some) behavioural responses to UV exposure depend on the presence of an intact retina and UV-sensitive cone photoreceptors (Guggiana-Nilo and Engert, 2016, doi:10.3389/fnbeh.2016.00160). It is premature to conclude that the lack of behavioural response to UV exposure in the cavefish is due to a different response to DNA damage, as their lack of eyes will likely inhibit a response to the UV stimulus. Indeed, were the equivalent zebrafish experiment from Zada et al. to be repeated with mutant larvae fish lacking the retinal basis for UV detection it might be found that in this case too, the effects of UV on behaviour are dependent on visual function. Such a finding should prompt a reappraisal of the interpretation that UV exposure's effects on fish sleep/locomotor behaviour are mediated by DNA damage. An additional note, relating to both Lloyd, Xia, et al., and Zada et al., is that though increases in immobility are induced following UV exposure, in neither study have assays of sensory responsiveness been performed during this period. As a decrease in sensory responsiveness is a key behavioural criterion for defining sleep, it is, therefore, unclear that this post-UV behaviour is genuinely increased sleep as opposed to a stress-linked suppression of locomotion due to the intensely aversive UV stimulus.

The effects of UV exposure, in terms of causing damage to DNA, inducing DNA damage response and repair mechanisms, and in causing broader changes in gene expression are assessed in both surface and cavefish larvae, as well as in cell lines derived from these different morphs. Differences in the suite of DNA damage response mechanisms that are upregulated are shown to exist between surface fish and cavefish larvae, though at least some of this difference is likely to be due to differences in gene expression that may exist even without UV exposure (this is discussed further below).

UV exposure induced DNA damage (as measured by levels of cyclobutene pyrimidine dimers) to a similar degree in cell lines derived from both surface fish and cave fish. However, γH2AX shows increased expression only in cells from the surface fish, suggesting induction of an increased DNA repair response in these surface morphs, corroborated by their cells' increased ability to repair damaged DNA constructs experimentally introduced to the cells in a subsequent experiment. This "host cell reactivation assay" is a very interesting assay for measuring DNA repair in cell lines, but the power of this approach might be enhanced by introducing these DNA constructs into larval neurons in vivo (perhaps by electroporation) and by tracking DNA repair in living animals. Indeed, in such a preparation, the relationship between DNA repair and sleep/wake state could be assayed.

Comparing gene expression in tissues from young (here 1 year) and older (here 7-8 years) fish from both cavefish and surface fish morphs, the authors found that there are significant differences in the transcriptional profiles in brain and gut between young and old surface fish, but that for cavefish being 1 year old versus being 7-8 years old did not have a major effect on transcriptional profile. The authors take this as suggesting that there is a reduced transcriptional change occurring during aging and that the transcriptome of the cavefish is resistant to age-linked changes. This seems to be only one of the equally plausible interpretations of the results; it could also be the case that alterations in metabolic cellular and molecular mechanisms, and particularly in responses to DNA damage, in the cavefish mean that these fish adopt their "aged" transcriptome within the first year of life.

A major weakness of the study in its current form is the absence of sleep deprivation experiments to assay the effects of sleep loss on the cellular and molecular parameters in question. Without such experiments, the supposed link of sleep to the molecular, cellular, and "aging" phenotypes remains tenuous. Although the argument might be made that the cavefish represent a naturally "sleep-deprived" population, the cavefish in this study are not sleep-deprived, rather they are adapted to a condition of reduced sleep relative to fish from surface populations. Comparing the effects of depriving fish from each morph on markers of DNA damage and repair, gut reactive oxygen species, and gene expression will be necessary to solidify any proposed link of these phenotypes to sleep.

A second important aspect that limits the interpretability and impact of this study is the absence of information about circadian variations in the parameters measured. A relationship between circadian phase, light exposure, and DNA damage/repair mechanisms is known to exist in A. mexicanus and other teleosts, and differences exist between the cave and surface morphs in their phenomena (Beale et al. 2013, doi: 10.1038/ncomms3769). Although the present study mentions that their experiments do not align with these previous findings, they do not perform the appropriate experiments to determine if such a misalignment is genuine. Specifically, Beale et al. 2013 showed that white light exposure drove enhanced expression of DNA repair genes (including cpdp which is prominent in the current study) in both surface fish and cavefish morphs, but that the magnitude of this change was less in the cave fish because they maintained an elevated expression of these genes in the dark, whereas the darkness suppressed the expression of these genes in the surface fish. If such a phenomenon is present in the setting of the current study, this would likely be a significant confound for the UV-induced gene expression experiments in intact larvae, and undermine the interpretation of the results derived from these experiments: as samples are collected 90 minutes after the dark-light transition (ZT 1.5) it would be expected that both cavefish and surface fish larvae should have a clear induction of DNA repair genes (including cpdp) regardless of 90s of UV exposure. The data in Supplementary Figure 3 is not sufficient to discount this potentially serious confound, as for larvae there is only gene expression data for time points from ZT2 to ZT 14, with all of these time points being in the light phase and not capturing any dynamics that would occur at the most important timepoints from ZT0-ZT1.5, in the relevant period after dark-light transition. Indeed, an appropriate control for this experiment would involve frequent sampling at least across 48 hours to assess light-linked and developmentally-related changes in gene expression that would occur in 5-6dpf larvae of each morph independently of the exposure to UV.

On a broader point, given the effects of both circadian rhythm and lighting conditions that are thought to exist in A. mexicanus (e.g. Beale et al. 2013) experiments involving measurements of DNA damage and repair, gene expression, and reactive oxygen species, etc. at multiple times across >1 24 hour cycle, in both light-dark and constant illumination conditions (e.g. constant dark) would be needed to substantiate the authors' interpretation that their findings indicate consistently altered levels of these parameters in the cavefish relative to the surface fish. Most of the data in this study is taken at only single time points.

In summary, the authors show that there are differences in gene expression, activity of DNA damage response and repair pathways, response to UV radiation, and gut reactive oxygen species between the Pachón cavefish morph and the surface morph of Astyanax mexicanus. However, the data presented does not make the precise nature of these differences very clear, and the interpretation of the results appears to be overly strong. Furthermore, the evidence of a link between these morph-specific differences and sleep is unconvincing.

Reviewer #1 (Public Review):

Summary:

In this article, the authors investigated how the brain anticipates sequences of potential sensory events, using temporal predictability to enhance perception. To do so, they combined a tone detection task, electrophysiological recordings, and recurrent neural network models. The stimuli consisted of continuous white noise embedded with either a single tone presented at one of 3 equidistant (500ms) temporal locations, or no tone. The main analyses were carried out on no-tone trials, in which subjects only anticipated future events. First, a modulation power spectrum analysis revealed 4 frequency clusters, and a coupling analysis allowed the authors to group 3 of them together into cluster 234. The time course of the latter aligned with the temporal locations, reaching a local maximum following each of them. The power of cluster 234 during no-tone trials was positively correlated with behavioral performance (d') during tone trials, but not with false alarm rate. Then, the authors trained several continuous-time recurrent neural networks to model the experimental paradigm. After the networks were tuned to reflect the average d' of human subjects, a neural network analogue of EEG was extracted from the activity of neurons. The latter displayed a peak at 2Hz, its time course aligned with the temporal locations, reaching a local maximum both before and after each of them, and its d' score was higher for tones located at one of the temporal locations. A network trained with randomly occurring tones displayed no 2Hz activity and d' independent from tone location. Finally, the authors perturbed the excitatory/inhibitory ratio of neurons within the network, finding that more inhibition resulted in earlier peaks in the neural network activity.

Strengths:

(1) The experimental paradigm introduced in this study is original and well-built, allowing for the study of the targeted phenomenon. The fact that relevant neural signals were found despite the absence of sensory cues proves the setup is promising, opening the way for future works, playing with different parameters: number of tones, time between tones, sequence of temporal locations complexity, sequence of events...etc.

(2) The statistical analysis was exhaustive, the authors consistently introduced controls for different conditions and alternative hypotheses, thoroughly explaining each step of the analysis as well as the choices behind them. The supplementary figures further helped understand the data and answer interrogation one might have. This comprehensive approach was well-appreciated.

(3) The use of more biologically plausible networks, compared to traditional RNNs, to model the response of subjects is a promising approach, which can give clues as to the mechanism at play, but also make predictions that can then be proven (or disproven) by future experiments.

The authors provided a work of good technical quality and reported their methods and findings transparently, making for good reproducibility and evaluation.

Weaknesses:

(1) The most glaring weakness of the paper lies in its interpretation of the different results. Conclusions are scattered around the paper, mostly unclear, and do not always make much sense with regard to the data. For example, the authors never address the absence of a peak before the first temporal location: why would subjects not "suppress" noise before the first temporal location given its (strong) predictability? Moreover, they immediately assume a functional role for the neural signature they found, as well as a direct link between the mechanisms at play in their RNN and the human brain, thus jumping to hasty and unreliable conclusions. The authors seemed to have a strong bias towards a hypothesis (predictive gain control) and tried to fit their data into it.

- The authors cited very few relevant papers on related fields, notably on omission, and therefore did not build efficiently on previous works (e.g., Yabe, Raij, Schröger, Bekinschtein, Chait, Auksztulewicz...). Moreover, at several points in the paper, they make choices about their analysis or model without proper justification or cited sources, even when explicitly pointing to the existence of research supporting said choices.

- Only a single electrode (out of 64) was used (Cz) to carry out every analysis. Without proper justification, this choice could be misinterpreted. Moreover, adopting instead a multivariate approach (incorporating all channels) would give more strength to the paper.

- Overall, the observed electrophysiological results could be more simply explained by a mechanism akin to a go/no-go (a tone/no-tone) or omission response happening after each temporal location, as subjects have learned when to make that inference. The delay of the response with regards to temporal location would change due to error accumulation in time perception, rather than "the anticipation of the first temporal location facilitating the anticipation of the second", which makes little sense. Moreover, a response in Cz could be expected.

- As for the results of RNN, not only is the analogy with actual neurophysiological activity limited, both in principle (simple E/I dynamics) and in implementation (inference is only done at the end of each trial), but the authors do not address the activity before the first temporal location, which is a major difference with human data. Their assumption that both RNN and cluster 234 are functionally related to gain control is thus further flawed. Moreover, the analysis of the RNN is lacking, for example, the authors did not compare false positive/negative of different delays, or analyzed Wout.

- The phrasing and introduction of the paper are misleading, as confusion can arise between predicting a sequence of events (several events in a row) and predicting a single event appearing at different potential locations. It should be clarified that the paper does not address sequences of events at any point.

It seems the authors already drew their conclusion beforehand and fit the data to match this bias. As such, the interpretation of the data is messy, flawed, and often hasty, drawing erroneous conclusions and parallels.

Overall, the manuscript is of good technical quality and communicated results very transparently, but the authors seem to have a strong confirmation bias towards temporal anticipation and gain control, thus leading to flawed interpretations.

Reviewer #1 (Public Review):

Summary:

In this study, Gu et al. employed novel viral strategies, combined with in vivo two-photon imaging, to map the tone response properties of two groups of cortical neurons in A1. The thalamocortical recipient (TR neurons) and the corticothalamic (CT neurons). They observed a clear tonotopic gradient among TR neurons but not in CT neurons. Moreover, CT neurons exhibited high heterogeneity of their frequency tuning and broader bandwidth, suggesting increased synaptic integration in these neurons. By parsing out different projecting-specific neurons within A1, this study provides insight into how neurons with different connectivity can exhibit different frequency response-related topographic organization.

Strengths:

This study reveals the importance of studying neurons with projection specificity rather than layer specificity since neurons within the same layer have very diverse molecular, morphological, physiological, and connectional features. By utilizing a newly developed rabies virus CSN-N2c GCaMP-expressing vector, the authors can label and image specifically the neurons (CT neurons) in A1 that project to the MGB. To compare, they used an anterograde trans-synaptic tracing strategy to label and image neurons in A1 that receive input from MGB (TR neurons).

Weaknesses:

- Perhaps as cited in the introduction, it is well known that tonotopic gradient is well preserved across all layers within A1, but I feel if the authors want to highlight the specificity of their virus tracing strategy and the populations that they imaged in L2/3 (TR neurons) and L6 (CT neurons), they should perform control groups where they image general excitatory neurons in the two depths and compare to TR and CT neurons, respectively. This will show that it's not their imaging/analysis or behavioral paradigms that are different from other labs.  

- Figures 1D and G, the y-axis is Distance from pia (%). I'm not exactly sure what this means. How does % translate to real cortical thickness? 

- For Figure 2G and H, is each circle a neuron or an animal? Why are they staggered on top of each other on the x-axis? If the x-axis is the distance from caudal to rostral, each neuron should have a different distance? Also, it seems like it's because Figure 2H has more circles, which is why it has more variation, thus not significant (for example, at 600 or 900um, 2G seems to have fewer circles than 2H).  

- Similarly, in Figures 2J and L, why are the circles staggered on the y-axis now? And is each circle now a neuron or a trial? It seems they have many more circles than Figure 2G and 2H. Also, I don't think doing a correlation is the proper stats for this type of plot (this point applies to Figures 3H and 3J).

- What does the inter-quartile range of BF (IQRBF, in octaves) imply? What's the interpretation of this analysis? I am confused as to why TR neurons show high IQR in HF areas compared to LF areas, which means homogeneity among TR neurons (lines 213 - 216). On the same note, how is this different from the BF variability?  Isn't higher IQR equal to higher variability?

- Figure 4A-B, there are no clear criteria on how the authors categorize V, I, and O shapes. The descriptions in the Methods (lines 721 - 725) are also very vague.

Reviewer #2 (Public Review):

Summary:

Gu and Liang et. al investigated how auditory information is mapped and transformed as it enters and exits an auditory cortex. They use anterograde transsynaptic tracers to label and perform calcium imaging of thalamorecipient neurons in A1 and retrograde tracers to label and perform calcium imaging of corticothalamic output neurons. They demonstrate a degradation of tonotopic organization from the input to output neurons.

Strengths:

The experiments appear well executed, well described, and analyzed.

Weaknesses:

(1) Given that the CT and TR neurons were imaged at different depths, the question as to whether or not these differences could otherwise be explained by layer-specific differences is still not 100% resolved. Control measurements would be needed either by recording (1) CT neurons in upper layers, (2) TR in deeper layers, (3) non-CT in deeper layers and/or (4) non-TR in upper layers.

(2) What percent of the neurons at the depths are CT neurons? Similar questions for TR neurons?

(3) V-shaped, I-shaped, or O-shaped is not an intuitively understood nomenclature, consider changing. Further, the x/y axis for Figure 4a is not labeled, so it's not clear what the heat maps are supposed to represent.

(4) Many references about projection neurons and cortical circuits are based on studies from visual or somatosensory cortex. Auditory cortex organization is not necessarily the same as other sensory areas. Auditory cortex references should be used specifically, and not sources reporting on S1, and V1.

Reviewer #3 (Public Review):

Summary:

The authors performed wide-field and 2-photon imaging in vivo in awake head-fixed mice, to compare receptive fields and tonotopic organization in thalamocortical recipient (TR) neurons vs corticothalamic (CT) neurons of mouse auditory cortex. TR neurons were found in all cortical layers while CT neurons were restricted to layer 6. The TR neurons at nominal depths of 200-400 microns have a remarkable degree of tonotopy (as good if not better than tonotopic maps reported by multiunit recordings). In contrast, CT neurons were very heterogenous in terms of their best frequency (BF), even when focusing on the low vs high-frequency regions of the primary auditory cortex. CT neurons also had wider tuning.

Strengths:

This is a thorough examination using modern methods, helping to resolve a question in the field with projection-specific mapping.

Weaknesses:

There are some limitations due to the methods, and it's unclear what the importance of these responses are outside of behavioral context or measured at single timepoints given the plasticity, context-dependence, and receptive field 'drift' that can occur in the cortex.

(1) Probably the biggest conceptual difficulty I have with the paper is comparing these results to past studies mapping auditory cortex topography, mainly due to differences in methods. Conventionally, the tonotopic organization is observed for characteristic frequency maps (not best frequency maps), as tuning precision degrades and the best frequency can shift as sound intensity increases. The authors used six attenuation levels (30-80 dB SPL) and reported that the background noise of the 2-photon scope is <30 dB SPL, which seems very quiet. The authors should at least describe the sound-proofing they used to get the noise level that low, and some sense of noise across the 2-40 kHz frequency range would be nice as a supplementary figure. It also remains unclear just what the 2-photon dF/F response represents in terms of spikes. Classic mapping using single-unit or multi-unit electrodes might be sensitive to single spikes (as might be emitted at characteristic frequency), but this might not be as obvious for Ca2+ imaging. This isn't a concern for the internal comparison here between TR and CT cells as conditions are similar, but is a concern for relating the tonotopy or lack thereof reported here to other studies.

(2) It seems a bit peculiar that while 2721 CT neurons (N=10 mice) were imaged, less than half as many TR cells were imaged (n=1041 cells from N=5 mice). I would have expected there to be many more TR neurons even mouse for mouse (normalizing by number of neurons per mouse), but perhaps the authors were just interested in a comparison data set and not being as thorough or complete with the TR imaging?

(3) The authors' definitions of neuronal response type in the methods need more quantitative detail. The authors state: ""Irregular" neurons exhibited spontaneous activity with highly variable responses to sound stimulation. "Tuned" neurons were responsive neurons that demonstrated significant selectivity for certain stimuli. "Silent" neurons were defined as those that remained completely inactive during our recording period (> 30 min). For tuned neurons, the best frequency (BF) was defined as the sound frequency associated with the highest response averaged across all sound levels.". The authors need to define what their thresholds are for 'highly variable', 'significant', and 'completely inactive'. Is best frequency the most significant response, the global max (even if another stimulus evokes a very close amplitude response), etc.

Reviewer #1 (Public Review):

Summary:

This study resolves a cryo-EM structure of the GPCR, GPR30, which was recently identified as a bicarbonate receptor by the authors' lab. Understanding the ligand and the mechanism of activation is of fundamental importance to the field of receptor signaling. However, the main claim of the paper, the identification of the bicarbonate binding site, is only partly supported by the structural and functional data, leaving the study incomplete.

Strengths:

The overall structure, and proposed mechanism of G-protein coupling seem solid. The authors perform fairly extensive unbiased mutagenesis to identify a host of positions that are important to G-protein signaling. To my knowledge, bicarbonate is the only physiological ligand that has been identified for GPR30, making this study a particularly important contribution to the field.

Weaknesses:

Without higher resolution structures and/or additional experimental assessment of the binding pocket, the assignment of the bicarbonate remains highly speculative. The local resolution is especially poor in the ECL loop region where the ligand is proposed to bind (4.3 - 4 .8 Å range). Of course, sometimes it is difficult to achieve high structural resolution, but in these cases, the assignment of ligands should be backed up by even more rigorous experimental validation.

The functional assay monitors activation of GPR30, and thus reports on not only bicarbonate binding, but also the integrity of the allosteric network that transduces the binding signal across the membrane. Thus, disruption of bicarbonate signaling by mutagenesis of the putative coordinating residues does not necessarily mean that bicarbonate binding has been disrupted. Moreover, the mutagenesis was apparently done prior to structure determination, meaning that residues proposed to directly surround bicarbonate binding, such as E218, were not experimentally validated. Targeted mutagenesis based on the structure would strengthen the story.

Moreover, the proposed bicarbonate binding site is surprising in a chemical sense, as it is located within an acidic pocket. The authors cite several other structural studies to support the surprising observation of anionic bicarbonate surrounded by glutamate residues in an acidic pocket (references 31-34). However, it should be noted that in general, these other structures also possess a metal ion (sodium or calcium) and/or a basic sidechain (arginine or lysine) in the coordination sphere, forming a tight ion pair. Thus, the assigned bicarbonate binding site in GPR30 remains an anomaly in terms of the chemical properties of the proposed binding site.

Reviewer #2 (Public Review):

Summary:

In this manuscript, "Cryo-EM structure of the bicarbonate receptor GPR30," the authors aimed to enrich our understanding of the role of GPR30 in pH homeostasis by combining structural analysis with a receptor function assay. This work is a natural development and extension of their previous work (PMID: 38413581). In the current body of work, they solved the first cryo-EM structure of the human GPR30-G-protein (mini-Gsqi) complex in the presence of bicarbonate ions at 3.21 Å resolution. From the atomic model built based on this map, they observed the overall canonical architecture of class A GPCR and also identified 4 extracellular pockets created by extracellular loops (ECLs) (Pockets A-D). Based on the polarity, location, and charge of each pocket, the authors hypothesized that pocket D is a good candidate for the bicarbonate binding site. To verify their structural observation, on top of the 10 mutations they generated in the previous work, the authors introduced another 11 mutations to map out the essential residues for the bicarbonate response on hGPR30. In addition, the human GPR30-G-protein complex model also allowed the authors to untangle the G-protein coupling mechanism of this special class A GPCR that plays an important role in pH homeostasis.

Strengths:

As a continuation of their recent Nature Communication publication (PMID: 38413581), this study was carefully designed, and the authors used mutagenesis and functional studies to confirm their structural observations. This work provided high-resolution structural observations for the receptor in complex with G-protein, allowing us to explore its mechanism of action, and will further facilitate drug development targeting GPR30. There were 4 extracellular pockets created by ECLs (Pockets A-D). The authors were able to filter out 3 of them and identified that pocket D was a good candidate for the bicarbonate binding site based on the polarity, location, and charge of each pocket. From there, the authors identified the key residues on GPR30 for its interaction with the substrate, bicarbonate. Together with their previous work, they carefully mapped out nine amino acids that are critical for receptor reactivity.

Weaknesses:

It is unclear how novel the aspects presented in the new paper are compared to the most recent Nature Communications publication (PMID: 38413581). Some areas of the manuscript appear to be mixed with the previous publication. The work is still impactful to the field. The new and novel aspects of this manuscript could be better highlighted.

I also have some concerns about the TGFα shedding assay the authors used to verify their structural observation. I understand that this assay was also used in the authors' previous work published in Nature Communications. However, there are still several things in the current data that raised concerns:

(1) The authors confirmed the "similar expression levels of HA-tagged hGPR30" mutants by WB in Supplemental Figure 1A and B. However, compared to the hGPR30-HA (~6.5 when normalized to the housekeeping gene, Na-K-ATPase), several mutants of the key amino acids had much lower surface expression: S134A, D210A, C207A had ~50% reduction, D125A had ~30% reduction, and Q215A and P71A had ~20% reduction. This weakens the receptor reactivity measured by the TGFα shedding assay.

(2) In the previous work, the authors demonstrated that hGPR30 signals through the Gq signaling pathway and can trigger calcium mobilization. Given that calcium mobilization is a more direct measurement for the downstream signaling of hGPR30 than the TGFα shedding assay, pairing the mutagenesis study with the calcium assay will be a better functional validation to confirm the disruption of bicarbonate signaling.

(3) It was quite confusing for Figure 4B that all statistical analyses were done by comparing to the mock group. It would be clearer to compare the activity of the mutants to the wild-type cell line.

Additional concerns about the structural data include:

(1) E218 was in close contact with bicarbonate in Figure 4D. However, there is no functional validation for this observation. Including the mutagenesis study of this site in the cell-based functional assay will strengthen this structural observation.

(2) For the flow chart of the cryo-EM data processing in Supplemental data 2, the authors started with 10,148,422 particles after template picking, then had 441,348 Particles left after 2D classification/heterogenous refinement, and finally ended with 148,600 particles for the local refinement for the final map. There seems to be a lot of heterogeneity in this purified sample. GPCRs usually have flexible and dynamic loop regions, which explains the poor resolution of the ECLs in this case. Thus, a solid cell-based functional validation is a must to assign the bicarbonate binding pocket to support their hypothesis.

Reviewer #3 (Public Review):

Summary:

GPR30 responds to bicarbonate and regulates cellular responses to pH and ion homeostasis. However, it remains unclear how GPR30 recognizes bicarbonate ions. This paper presents the cryo-EM structure of GPR30 bound to a chimeric mini-Gq in the presence of bicarbonate. The structure together with functional studies aims to provide mechanistic insights into bicarbonate recognition and G protein coupling.

Strengths:

The authors performed comprehensive mutagenesis studies to map the possible binding site of bicarbonate.

Weaknesses:

Owing to the poor resolution of the structure, some structural findings may be overclaimed.

Based on EM maps shown in Figure 1a and Figure Supplement 2, densities for side chains in the receptor particularly in ECLs (around 4 Å) are poorly defined. At this resolution, it is unlikely to observe a disulfide bond (C130ECL1-C207ECl2) and bicarbonate ions. Moreover, the disulfide between ECL1 and ECL2 has not been observed in other GPCRs and the published structure of GPR30 (PMID: 38744981). The density of this disulfide bond could be noise.

The authors observed a weak density in pocket D, which is accounted for by the bicarbonate ions. This ion is mainly coordinated by Q215 and Q138. However, the Q215A mutation only reduced but not completely abolished bicarbonate response, and the author did not present the data of Q138A mutation. Therefore, Q215 and Q138 could not be bicarbonate binding sites. While H307A completely abolished bicarbonate response, the authors proposed that this residue plays a structural role. Nevertheless, based on the structure, H307 is exposed and may be involved in binding bicarbonate. The assignment of bicarbonate in the structure is not supported by the data.

Reviewer #1 (Public Review):

Summary:

The study "Impact of Maximal Overexpression of a Non-toxic Protein on Yeast Cell Physiology" by Fujita et al. aims to elucidate the physiological impacts of overexpressing non-toxic proteins in yeast cells. By identifying model proteins with minimal cytotoxicity, the authors claim to provide insights into cellular stress responses and metabolic shifts induced by protein overexpression.

Strengths:

The study introduces a neutrality index to quantify cytotoxicity and investigates the effects of protein burden on yeast cell physiology. The study identifies mox-YG (a non-fluorescent fluorescent protein) and Gpm1-CCmut (an inactive glycolytic enzyme) as proteins with the lowest cytotoxicity, capable of being overexpressed to more than 40% of total cellular protein while maintaining yeast growth. Overexpression of mox-YG leads to a state resembling nitrogen starvation probably due to TORC1 inactivation, increased mitochondrial function, and decreased ribosomal abundance, indicating a metabolic shift towards more energy-efficient respiration and defects in nucleolar formation.

Weaknesses:

While the introduction of the neutrality index seems useful to differentiate between cytotoxicity and protein burden, the biological relevance of the effects of overexpression of the model proteins is unclear.

Reviewer #2 (Public Review):

Summary:

In this manuscript, Fujita et al. characterized the neutrality indexes of several protein mutants in S. cerevisiae and uncovered that mox-YG and Gpm1-CCmut can be expressed as abundant as 40% of total proteins without causing severe growth defects. The authors then looked at the transcriptome and proteome of cells expressing excess mox-YG to investigate how protein burden affects yeast cells. Based on RNA-seq and mass-spectrometry results, the authors uncover that cells with excess mox-YG exhibit nitrogen starvation, respiration increase, inactivated TORC1 response, and decreased ribosomal abundance. The authors further showed that the decreased ribosomal amount is likely due to nucleoli defects, which can be partially rescued by nuclear exosome mutations.

Strengths:

Overall, this is a well-written manuscript that provides many valuable resources for the field, including the neutrality analysis on various fluorescent proteins and glycolytic enzymes, as well as the RNA-seq and proteomics results of cells overexpressing mox-YG. Their model on how mox-YG overexpression impairs the nucleolus and thus leads to ribosomal abundance decline will also raise many interesting questions for the field.

Weaknesses:

The authors concluded from their RNA-seq and proteomics results that cells with excess mox-YG expression showed increased respiration and TORC1 inactivation. I think it will be more convincing if the authors can show some characterization of mitochondrial respiration/membrane potential and the TOR responses to further verify their -omic results.

In addition, the authors only investigated how overexpression of mox-YG affects cells. It would be interesting to see whether overexpressing other non-toxic proteins causes similar effects, or if there are protein-specific effects. It would be good if the authors could at least discuss this point considering the workload of doing another RNA-seq or mass-spectrum analysis might be too heavy.

Reviewer #3 (Public Review):

Summary:

Protein overexpression is widely used in experimental systems to study the function of the protein, assess its (beneficial or detrimental) effects in disease models, or challenge cellular systems involved in synthesis, folding, transport, or degradation of proteins in general. Especially at very high expression levels, protein-specific effects and general effects of a high protein load can be hard to distinguish. To overcome this issue, Fujita et al. use the previously established genetic tug-of-war system to identify proteins that can be expressed at extremely high levels in yeast cells with minimal protein-specific cytotoxicity (high 'neutrality'). They focus on two versions of the protein mox-GFP, the fluorescent version and a point mutation that is non-fluorescent (mox-YG) and is the most 'neutral' protein on their screen. They find that massive protein expression (up to 40% of the total proteome) results in a nitrogen starvation phenotype, likely inactivation of the TORC1 pathway, and defects in ribosome biogenesis in the nucleolus.

Strengths:

This work uses an elegant approach and succeeds in identifying proteins that can be expressed at surprisingly high levels with little cytotoxicity. Many of the changes they see have been observed before under protein burden conditions, but some are new and interesting. This work solidifies previous hypotheses about the general effects of protein overexpression and provides a set of interesting observations about the toxicity of fluorescent proteins (that is alleviated by mutations that render them non-fluorescent) and metabolic enzymes (that are less toxic when mutated into inactive versions).

Weaknesses:

The data are generally convincing, however in order to back up the major claim of this work - that the observed changes are due to general protein burden and not to the specific protein or condition - a broader analysis of different conditions would be highly beneficial.

Major points:

(1) The authors identify several proteins with high neutrality scores but only analyze the effects of mox/mox-YG overexpression in depth. Hence, it remains unclear which molecular phenotypes they observe are general effects of protein burden or more specific effects of these specific proteins. To address this point, a proteome (and/or transcriptome) of at least a Gpm1-CCmut expressing strain should be obtained and compared to the mox-YG proteome. Ideally, this analysis should be done simultaneously on all strains to achieve a good comparability of samples, e.g. using TMT multiplexing (for a proteome) or multiplexed sequencing (for a transcriptome). If feasible, the more strains that can be included in this comparison, the more powerful this analysis will be and can be prioritized over depth of sequencing/proteome coverage.

(2) The genetic tug-of-war system is elegant but comes at the cost of requiring specific media conditions (synthetic minimal media lacking uracil and leucine), which could be a potential confound, given that metabolic rewiring, and especially nitrogen starvation are among the observed phenotypes. I wonder if some of the changes might be specific to these conditions. The authors should corroborate their findings under different conditions. Ideally, this would be done using an orthogonal expression system that does not rely on auxotrophy (e.g. using antibiotic resistance instead) and can be used in rich, complex mediums like YPD. Minimally, using different conditions (media with excess or more limited nitrogen source, amino acids, different carbon source, etc.) would be useful to test the robustness of the findings towards changes in media composition.

(3) The authors suggest that the TORC1 pathway is involved in regulating some of the changes they observed. This is likely true, but it would be great if the hypothesis could be directly tested using an established TORC1 assay.

(4) The finding that the nucleolus appears to be virtually missing in mox-YG-expressing cells (Figure 6B) is surprising and interesting. The authors suggest possible mechanisms to explain this and partially rescue the phenotype by a reduction-of-function mutation in an exosome subunit. I wonder if this is specific to the mox-YG protein or a general protein burden effect, which the experiments suggested in point 1 should address. Additionally, could a mox-YG variant with a nuclear export signal be expressed that stays exclusively in the cytosol to rule out that mox-YG itself interferes with phase separation in the nucleus?

Minor points:

(5) It would be great if the authors could directly compare the changes they observed at the transcriptome and proteome levels. This can help distinguish between changes that are transcriptionally regulated versus more downstream processes (like protein degradation, as proposed for ribosome components).

Reviewer #1 (Public Review):

In this manuscript, Satouh et al. report giant organelle complexes in oocytes and early embryos. Although these structures have often been observed in oocytes and early embryos, their exact nature has not been characterized. The authors named these structures "endosomal-lysosomal organelles form assembly structures (ELYSAs)". ELYSAs contain organelles such as endosomes, lysosomes, and probably autophagic structures. ELYSAs are initially formed in the perinuclear region and then migrate to the periphery in an actin-dependent manner. When ELYSAs are disassembled after the 2-cell stage, the V-ATPase V1 subunit is recruited to make lysosomes more acidic and active. The ELYSAs are most likely the same as the "endolysosomal vesicular assemblies (ELVAs)", reported by Elvan Böke's group earlier this year (Zaffagnini et al. doi.org/10.1016/j.cell.2024.01.031). However, it is clear that Satouh et al. identified and characterized these structures independently. These two studies could be complementary. Although the nature of the present study is generally descriptive, this paper provides valuable information about these giant structures. The data are mostly convincing, and only some minor modifications are needed for clarification and further explanation to fully understand the results.

Reviewer #2 (Public Review):

Satouh et al report the presence of spherical structures composed of endosomes, lysosomes, and autophagosomes within immature mouse oocytes. These endolysosomal compartments have been named as Endosomal-LYSosomal organellar Assembly (ELYSA). ELYSAs increase in size as the oocytes undergo maturation. ELYSAs are distributed throughout the oocyte cytoplasm of GV stage immature oocytes but these structures become mostly cortical in the mature oocytes. Interestingly, they tend to avoid the region which contains metaphase II spindle and chromosomes. They show that the endolysosomal compartments in oocytes are less acidic and therefore non-degradative but their pH decreases and becomes degradative as the ELYSAs begin to disassemble in the embryos post-fertilization. This manuscript shows that lysosomal switching does not happen during oocyte development, and the formation of ELYSAs prevents lysosomes from being activated. Structures similar to these ELYSAs have been previously described in mouse oocytes (Zaffagnini et al, 2024) and these vesicular assemblies are important for sequestering protein aggregates in the oocytes but facilitate proteolysis after fertilization. The current manuscript, however, provides further details of endolysosomal disassembly post-fertilization. Specifically, the V1-subunit of V-ATPase targeting the ELYSAs increases the acidity of lysosomal compartments in the embryos. This is a well-conducted study and their model is supported by experimental evidence and data analyses.

Reviewer #3 (Public Review):

Fertilization converts a cell defined as an egg to a cell defined as an embryo. An essential component of this switch in cell fate is the degradation (autophagy) of cellular elements that serve a function in the development of the egg but could impede the development of the embryo. Here, the authors have focused on the behavior during the egg-to-embryo transition of endosomes and lysosomes, which are cytoplasmic structures that mediate autophagy. By carefully mapping and tracking the intracellular location of well-established marker proteins, the authors show that in oocytes endosomes and lysosomes aggregate into giant structures that they term Endosomal LYSosomal organellar Assembl[ies] (ELYSA). Both the size distribution of the ELYSAs and their position within the cell change during oocyte meiotic maturation and after fertilization. Notably, during maturation, there is a net actin-dependent movement towards the periphery of the oocyte. By the late 2-cell stage, the ELYSAs are beginning to disintegrate. At this stage, the endo-lysosomes become acidified, likely reflecting the activation of their function to degrade cellular components.

This is a carefully performed and quantified study. The fluorescent images obtained using well-known markers, using both antibodies and tagged proteins, support the interpretations, and the quantification method is sophisticated and clearly explained. Notably, this type of quantification of confocal z-stack images is rarely performed and so represents a real strength of the study. It provides sound support for the conclusions regarding changes in the size and position of the ELYSAs. Another strength is the use of multiple markers, including those that indicate the activity state of the endo-lysosomes. Altogether, the manuscript provides convincing evidence for the existence of ELYSAs and also for regulated changes in their location and properties during oocyte maturation and the first few embryonic cell cycles following fertilization.

At present, precisely how the changes in the location and properties of the ELYSAs affect the function of the endo-lysosomal system is not known. While the authors' proposal that they are stored in an inactive state is plausible, it remains speculative. Nonetheless, this study lays the foundation for future work to address this question.

Minor point: l. 299. If I am not mistaken, there is a typo. It should read that the inhibitors of actin polymerization prevent redistribution from the cytoplasm to the cortex during maturation.<br /> Minor point: A few statements in the Introduction would benefit from clarification. These are noted in the comments to the authors.

Reviewer #1 (Public Review):

Summary:

PROTACs are heterobifunctional molecules that utilize the Ubiquitin Proteasome System to selectively degrade target proteins within cells. Upon introduction to the cells, PROTACs capture the activity of the E3 ubiquitin ligases for ubiquitination of the targeted protein, leading to its subsequent degradation by the proteasome. The main benefit of PROTAC technology is that it expands the "druggable proteome" and provides numerous possibilities for therapeutic use. However, there are also some difficulties, including the one addressed in this manuscript: identifying suitable target-E3 ligase pairs for successful degradation. Currently, only a few out of about 600 E3 ligases are used to develop PROTAC compounds, which creates the need to identify other E3 ligases that could be used in PROTAC synthesis. Testing the efficacy of PROTAC compounds has been limited to empirical tests, leading to lengthy and often failure-prone processes. This manuscript addressed the need for faster and more reliable assays to identify the compatible pairs of E3 ligases-target proteins. The authors propose using the RiPA assay, which depends on rapamycin-induced dimerization of FKBP12 protein with FRB domain. The PROTAC technology is advancing rapidly, making this manuscript both timely and essential. The RiPA assay might be useful in identifying novel E3 ligases that could be utilized in PROTAC technology. Additionally, it could be used at the initial stages of PROTAC development, looking for the best E3 ligase for the specific target.

The authors described an elegant assay that is scalable, easy-to-use, and applicable to a wide range of cellular models. This method allows for the quantitative validation of the degradation efficacy of a given pair of E3 ligase-target proteins, using luciferase activity as a measure. Importantly, the assay also enables the measurement of kinetics in living cells, enhancing its practicality.

Strengths:

(1) The authors have addressed the crucial needs that arise during PROTAC development. In the introduction, they nicely describe the advantages and disadvantages of the PROTAC technology and explain why such an assay is needed.

(2) The study includes essential controls in experiments (important for generating new assay), such as using the FRB vector without E3 ligase as a negative control, testing different linkers (which may influence the efficacy of the degradation), and creating and testing K-less vectors to exclude the possibility of luciferase or FKBP12 ubiquitination instead of WDR5 (the target protein). Additionally, the position of the luc in the FKBP12 vector and the position of VHL in the FRB vector are tested. Different E3 ligases are tested using previously identified target proteins, confirming the assay's utility and accuracy.

(3) The study identified a "new" E3 ligase that is suitable for PROTAC technology (FBXL).

Weaknesses:

It is not clear how feasible it would be to adapt the assay for high-throughput screens. In some experiments, the efficacy of WDR5 degradation tested by immunoblotting appears to be lower than luciferase activity (e.g., Figure 2G and H).

Reviewer #2 (Public Review):

Summary:

Adhikari and colleagues developed a new technique, rapamycin-induced proximity assay (RiPA), to identify E3-ubiquitin (ub) ligases of a protein target, aiming at identifying additional E3 ligases that could be targeted for PROTAC generation or ligases that may degrade a protein target. The study is timely, as expanding the landscape of E3-ub ligases for developing targeted degraders is a primary direction in the field.

Strengths:

The study's strength lies in its practical application of the FRB:FKBP12 system. This system is used to identify E3-ub ligases that would degrade a target of interest, as evidenced by the reduction in luminescence upon the addition of rapamycin. This approach effectively mimics the potential action of a PROTAC.

Weaknesses:

(1) While the technique shows promise, its application in a discovery setting, particularly for high-throughput or unbiased E3-ub ligase identification, may pose challenges. The authors should provide more detailed insights into these potential difficulties to foster a more comprehensive understanding of RiPA's limitations.

(2) While RiPA will help identify E3 ligases, PROTAC design would still be empirical. The authors should discuss this limitation. Could the technology be applied to molecular glue generation?

(3) Controls to verify the intended mechanism of action are missing, such as using a proteasome inhibitor or VHL inhibitors/siRNA to verify on-target effects. Verification of the target E3 ligase complex after rapamycin addition via orthogonal approaches, such as IP, should be considered.

Minor concern:

The graphs in Figure 1E are missing.

Reviewer #1 (Public Review):

This manuscript presents insights into biased signaling in GPCRs, namely cannabinoid receptors. Biased signaling is of broad interest in general, and cannabinoid signaling is particularly relevant for understanding the impact of new drugs that target this receptor. Mechanistic insight from work like this could enable new approaches to mitigate the public health impact of new psychoactive drugs. Towards that end, this manuscript seeks to understand how new psychoactive substances (NPS, e.g. MDMB-FUBINACA) elicit more signaling through β-arrestin than classical cannabinoids (e.g. HU-210). The authors use an interesting combination of simulations and machine learning.

The caption for Figure 3 doesn't explain the color scheme, so it's not obvious what the start and end states of the ligand are.

For the metadynamics simulations were multiple Gaussian heights/widths tried to see what, if any, impact that has on the unbinding pathway? That would be useful to help ensure all the relevant pathways were explored.

It would be nice to acknowledge previous applications of metadynamics+MSMs and (separately) TRAM, such as the Simulation of spontaneous G protein activation... (Sun et al. eLife 2018) and Estimation of binding rates and affinities... (Ge and Voelz JCP 2022).

What is KL divergence analysis between macrostates? I know KL divergence compares probability distributions, but it is not clear what distributions are being compared.

I suggest being more careful with the language of universality. It can be "supported" but "showing" or "proving" its universal would require looking at all possible chemicals in the class.

Reviewer #2 (Public Review):

Summary:

The investigation provides computational as well as biochemical insights into the (un)binding mechanisms of a pair of psychoactive substances into cannabinoid receptors. A combination of molecular dynamics simulation and a set of state-of-the art statistical post-processing techniques were employed to exploit GPCR-ligand dynamics.

Strengths:

The strength of the manuscript lies in the usage and comparison of TRAM as well as Markov state modelling (MSM) for investigating ligand binding kinetics and thermodynamics. Usually, MSMs have been more commonly used for this purpose. But as the authors have pointed out, implicit in the usage of MSMs lies the assumption of detailed balance, which would not hold true for many cases especially those with skewed binding affinities. In this regard, the author's usage of TRAM which harnesses both biased and unbiased simulations for extracting the same, provides a more appropriate way out.

Weaknesses:

(1) While the authors have used TRAM (by citing MSM to be inadequate in these cases), the thermodynamic comparisons of both techniques provide similar values. In this case, one would wonder what advantage TRAM would hold in this particular case.

(2) The initiation of unbiased simulations from previously run biased metadynamics simulations would almost surely introduce hysteresis in the analysis. The authors need to address these issues.

(3) The choice of ligands in the current work seems very forced and none of the results compare directly with any experimental data. An ideal case would have been to use the seminal D.E. Shaw research paper on GPCR/ligand binding as a benchmark and then show how TRAM, using much lesser biased simulation times, would fare against the experimental kinetics or even unbiased simulated kinetics of the previous report

(4) The method section of the manuscript seems to suggest all the simulations were started from a docked structure. This casts doubt on the reliability of the kinetics derived from these simulations that were spawned from docked structure, instead of any crystallographic pose. Ideally, the authors should have been more careful in choosing the ligands in this work based on the availability of the crystallographic structures.

(5) The last part of using a machine learning-based approach to analyse allosteric interaction seems to be very much forced, as there are numerous distance-based more traditional precedent analyses that do a fair job of identifying an allosteric job.

(6) While getting busy with the methodological details of TRAM vs MSM, the manuscript fails to share with sufficient clairty what the distinctive features of two ligand binding mechanisms are.

Reviewer #1 (Public Review):

Summary:

In this study, the authors identified and described the transcriptional trajectories leading to CMs during early mouse development, and characterized the epigenetic landscapes that underlie early mesodermal lineage specification.

The authors identified two transcriptomic trajectories from a mesodermal population to cardiomyocytes, the MJH and PSH trajectories. These trajectories are relevant to the current model for the First Heart Field (FHF) and the Second Heart Field (SHF) differentiation. Then, the authors characterized both gene expression and enhancer activity of the MJH and PSH trajectories, using a multiomics analysis. They highlighted the role of Gata4, Hand1, Foxf1, and Tead4 in the specification of the MJH trajectory. Finally, they performed a focused analysis of the role of Hand1 and Foxf1 in the MJH trajectory, showing their mutual regulation and their requirement for cardiac lineage specification.

Strengths:

The authors performed an extensive transcriptional and epigenetic analysis of early cardiac lineage specification and differentiation which will be of interest to investigators in the field of cardiac development and congenital heart disease. The authors considered the impact of the loss of Hand1 and Foxf1 in-vitro and Hand1 in-vivo.

Weaknesses:

The authors used previously published scRNA-seq data to generate two described transcriptomic trajectories.

(1) Details of the re-analysis step should be added, including a careful characterization of the different clusters and maker genes, more details on the WOT analysis, and details on the time stamp distribution along the different pseudotimes. These details would be important to allow readers to gain confidence that the two major trajectories identified are realistic interpretations of the input data.

The authors have also renamed the cardiac trajectories/lineages, departing from the convention applied in hundreds of papers, making the interpretation of their results challenging.

(2) The concept of "reverse reasoning" applied to the Waddington-OT package for directional mass transfer is not adequately explained. While the authors correctly acknowledged Waddington-OT's ability to model cell transitions from ancestors to descendants (using optimal transport theory), the justification for using a "reverse reasoning" approach is missing. Clarifying the rationale behind this strategy would be beneficial.

(3) As the authors used the EEM cell cluster as a starting point to build the MJH trajectory, it's unclear whether this trajectory truly represents the cardiac differentiation trajectory of the FHF progenitors:<br /> - This strategy infers that the FHF progenitors are mixed in the same cluster as the extra-embryonic mesoderm, but no specific characterization of potential different cell populations included in this cluster was performed to confirm this.

- The authors identified the EEM cluster as a Juxta-cardiac field, without showing the expression of the principal marker Mab21l2 per cluster and/or on UMAPs.

- As the FHF progenitors arise earlier than the Juxta-cardiac field cells, it must be possible to identify an early FHF progenitor population (Nkx2-5+; Mab21l2-) using the time stamp. It would be more accurate to use this FHF cluster as a starting point than the EEM cluster to infer the FHF cardiac differentiation trajectory.

These concerns call into question the overall veracity of the trajectory analysis, and in fact, the discrepancies with prior published heart field trajectories are noted but the authors fail to validate their new interpretation. Because their trajectories are followed for the remainder of the paper, many of the interpretations and claims in the paper may be misleading. For example, these trajectories are used subsequently for annotation of the multiomic data, but any errors in the initial trajectories could result in errors in multiomic annotation, etc, etc.

(4) As mentioned in the discussion, the authors identified the MJH and PSH trajectories as non-overlapping. But, the authors did not discuss major previously published data showing that both FHF and SHF arise from a common transcriptomic progenitor state in the primitive streak (DOI: 10.1126/science.aao4174; DOI: 10.1007/s11886-022-01681-w). The authors should consider and discuss the specifics of why they obtained two completely separate trajectories from the beginning, how these observations conflict with prior published work, and what efforts they have made at validation.

(5) Figures 1D and E are confusing, as it's unclear why the authors selected only cells at E7.0. Also, panels 1D 'Trajectory' and 'Pseudotime' suggest that the CM trajectory moves from the PSH cells to the MJH. This result is confusing, and the authors should explain this observation.

(6) Regarding the PSH trajectory, it's unclear how the authors can obtain a full cardiac differentiation trajectory from the SHF progenitors as the SHF-derived cardiomyocytes are just starting to invade the heart tube at E8.5 (DOI: 10.7554/eLife.30668).

The above notes some of the discrepancies between the author's trajectory analysis and the historical cardiac development literature. Overall, the discrepancies between the author's trajectory analysis and the historical cardiac development literature are glossed over and not adequately validated.

(7) The authors mention analyzing "activated/inhibited genes" from Peng et al. 2019 but didn't specify when Peng's data was collected. Is it temporally relevant to the current study? How can "later stage" pathway enrichment be interpreted in the context of early-stage gene expression?

(8) Motif enrichment: cluster-specific DAEs were analyzed for motifs, but the authors list specific TFs rather than TF families, which is all that motif enrichment can provide. The authors should either list TF families or state clearly that the specific TFs they list were not validated beyond motifs.

(9) The core regulatory network is purely predictive. The authors again should refrain from language implying that the TFs in the CRN have any validated role.

Regarding the in vivo analysis of Hand1 CKO embryos, Figures 6 and 7:

(10) How can the authors explain the presence of a heart tube in the E9.5 Hand1 CKO embryos (Figure 6B) if, following the authors' model, the FHF/Juxta-cardiac field trajectory is disrupted by Hand1 CKO? A more detailed analysis of the cardiac phenotype of Hand1 CKO embryos would help to assess this question.

(11) The cell proportion differences observed between Ctrl and Hand1 CKO in Figure 6D need to be replicated and an appropriate statistical analysis must be performed to definitely conclude the impact of Hand1 CKO on cell proportions.

(12) The in-vitro cell differentiations are unlikely to recapitulate the complexity of the heart fields in-vivo, but they are analyzed and interpreted as if they do.

(13) The schematic summary of Figure 7F is confusing and should be adjusted based on the following considerations:<br /> (a) the 'Wild-type' side presents 3 main trajectories (SHF, Early HT and JCF), but uses a 2-color code and the authors described only two trajectories everywhere else in the article (aka MJH and PSH). It's unclear how the SHF trajectory (blue line) can contribute to the Early HT, when the Early HT is supposed to be FHF-associated only (DOI: 10.7554/eLife.30668). As mentioned previously in Major comment 3., this model suggests a distinction between FHF and JCF trajectories, which is not investigated in the article.<br /> (b) the color code suggests that the MJH (FHF-related) trajectory will give rise to the right ventricle and outflow tract (green line), which is contrary to current knowledge.

Minor comments:

(1) How genes were selected to generate Figure 1F? Is this a list of top differentially expressed genes over each pseudotime and/or between pseudotimes?

(2) Regarding Figure 1G, it's unclear how inhibited signaling can have an increased expression of underlying genes over pseudotimes. Can the authors give more details about this analysis and results?

(3) How do the authors explain the visible Hand1 expression in Hand1 CKO in Figure S7C 'EEM markers'? Is this an expected expression in terms of RNA which is not converted into proteins?

(4) The authors do not address the potential presence of doublets (merged cells) within their newly generated dataset. While they mention using "SCTransform" for normalization and artifact removal, it's unclear if doublet removal was explicitly performed.

Reviewer #2 (Public Review):

Summary of goals:

The aims of the study were to identify new lineage trajectories for the cardiac lineages of the heart, and to use computational and cell and animal studies to identify and validate new gene regulatory mechanisms involved in these trajectories.

Strengths:

The study addresses the long-standing yet still not fully answered questions of what drives the earliest specification mechanisms of the heart lineages. The introduction demonstrates a good understanding of the relevant lineage trajectories that have been previously established, and the significance of the work is well described. The study takes advantage of several recently published data sets and attempts t use these in combination to uncover any new mechanisms underlying early mesoderm/cardiac specification mechanisms. A strength of the study is the use of an in vitro model system (mESCs) to assess the functional relevance of the key players identified in the computational analysis, including innovative technology such as CRISPR-guided enhancer modulations. Lastly, the study generates mesoderm-specific Hand1 LOF embryos and assesses the differentiation trajectories in these animals, which represents a strong complementary approach to the in vitro and computational analysis earlier in the paper. The manuscript is clearly written and the methods section is detailed and comprehensive.

Comments and Weaknesses:

Overall: The computational analysis presented here integrates a large number of published data sets with one new data point (E7.0 single cell ATAC and RNA sequencing). This represents an elegant approach to identifying new information using available data. However, the data presentation at times becomes rather confusing, and relatively strong statements and conclusions are made based on trajectory analysis or other inferred mechanisms while jumping from one data set to another. The cell and in vivo work on Hand1 and Foxf1 is an important part of the study. Some additional experiments in both of these model systems could strongly support the novel aspects that were identified by the computational studies leading into the work.

(1) Definition of MJH and PSH trajectory:<br /> The study uses previously published data sets to identify two main new differentiation trajectories: the MJH and the PSH trajectory (Figure 1). A large majority of subsequent conclusions are based on in-depth analysis of these two trajectories. For this reason, the method used to identify these trajectories (WTO, which seems a highly biased analysis with many manually chosen set points) should be supported by other commonly used methods such as for example RNA velocity analysis. This would inspire some additional confidence that the MJH and PSH trajectories were chosen as unbiased and rigorous as possible and that any follow-up analysis is biologically relevant.

(2) Identification of MJH and PSH trajectory progenitors:<br /> The study defines various mesoderm populations from the published data set (Figure 1A-E), including nascent mesoderm, mixed mesoderm, and extraembryonic mesoderm. It further assigns these mesoderm populations to the newly identified MJH/PSH trajectories. Based on the trajectory definition in Figure 1A it appears that both trajectories include all 3 mesoderm populations, albeit at different proportions and it seems thus challenging to assign these as unique progenitor populations for a distinct trajectory, as is done in the epigenetic study by comparing clusters 8 (MJH) and s (PSH)(Figure 2). Along similar lines, the epigenetic analysis of clusters 2 and 8 did not reveal any distinct differences in H3K4m1, H3K27ac, or H3K4me3 at any of the time points analyzed (Figure 2F). While conceptually very interesting, the data presented do not seem to identify any distinct temporal patterns or differences in clones 2 and 8 (Figure 2H), and thus don't support the conclusion as stated: "the combined transcriptome and chromatin accessibility analysis further supported the early lineage segregation of MJH and the epigenetic priming at gastrulation stage for early cardiac genes".

(3) Function of Hand1 and Foxf1 during early cardiac differentiation:<br /> The study incorporated some functional studies by generating Hand1 and Foxf1 KO mESCs and differentiated them into mesoderm cells for RNA sequencing. These lines would present relevant tools to assess the role of Hand1 and Foxf1 in mesoderm formation, and a number of experiments would further support the conclusions, which are made for the most part on transcriptional analysis. For example, the study would benefit from quantification of mesoderm cells and subsequent cardiomyocytes during differentiation (via IF, or more quantitatively, via flow cytometry analysis). These data would help interpret any of the findings in the bulk RNAseq data, and help to assess the function of Hand1 and Foxf1 in generating the cardiac lineages. Conclusions such as "the analysis indicated that HAND1 and FOXF1 could dually regulate MJH specification through directly activating the MJH specific genes and inhibiting PSH specific genes" seem rather strong given the data currently provided.

(4) Analysis of Hand1 cKO embryos:<br /> Adding a mouse model to support the computational analysis is a strong way to conclude the study. Given the availability of these early embryos, some of the findings could be strengthened by performing a similar analysis to Figure 7B&C and by including some of the specific EEM markers found to be differentially regulated to complement the structural analysis of the embryos.

(5) Current findings in the context of previous findings:<br /> The introduction carefully introduces the concept of lineage specification and different progenitor pools. Given the enormous amount of knowledge already available on Hand1 and Foxf1, and their role in specific lineages of the early heart, some of this information should be added, ideally to the discussion where it can be put into context of what the present findings add to the existing understanding of these transcription factors and their role in early cardiac specification.

Reviewer #3 (Public Review):

(1) In Figure 1A, could the authors justify using E8.5 CMs as the endpoint for the second lineage and better clarify the chamber identities of the E8.5 CMs analysed? Why are the atrial genes in Figure 1C of the PSH trajectory not present in Table S1.1, which lists pseudotime-dependent genes for the MJH/PSH trajectories from Figure 1F?

(2) Could the authors increase the resolution of their trajectory and genomic analyses to distinguish between the FHF (Tbx5+ HCN4+) and the JCF (Mab21l2+/ Hand1+) within the MJH lineage? Also, clarify if the early extraembryonic mesoderm contributes to the FHF.

(3) The authors strongly assume that the juxta-cardiac field (JCF), defined by Mab21l2 expression at E7.5 in the extraembryonic mesoderm, contributes to CMs. Could the authors explain the evidence for this? Could the authors identify Mab21l2 expression in the left ventricle (LV) myocardium and septum transversum at E8.5 (see Saito et al., 2013, Biol Open, 2(8): 779-788)? If such a JCF contribution to CMs exists, the extent to which it influences heart development should be clarified or discussed.

(4) Could the authors distinguish the Hand1+ pericardium from JCF progenitors in their single-cell data and explain why they excluded other cell types, such as the endocardium/endothelium and pericardium, or even the endoderm, as endpoints of their trajectory analysis? At the NM and MM mesoderm stages, how did the authors distinguish the earliest cardiac cells from the surrounding developing mesoderm?

(5) Could the authors contrast their trajectory analysis with those of Lescroart et al. (2018), Zhang et al., Tyser et al., and Krup et al.?

(6) Previous studies suggest that Mesp2 expression starts at E8 in the presomitic mesoderm (Saga et al., 1997). Could the authors provide in situ hybridization or HCR staining to confirm the early E7 Mesp2 expression suggested by the pseudo-time analysis of the second lineage.

(7) Could the authors also confirm the complementary Hand1 and Lefty2 expression patterns at E7 using HCR or in situ hybridization? Hand1 expression in the first lineage is plausible, considering lineage tracing results from Zhang et al.

(8) Could the authors explain why Hand1 and Lefty2+ cells are more likely to be multipotent progenitors, as mentioned in the text?

(9) Could the authors comment on the low Mesp1 expression in the mesodermal cells (MM) of the MJH trajectory at E7 (Figure 1D)? Is Mesp1 transiently expressed early in MJH progenitors and then turned off by E7? Have all FHF/JCF/SHF cells expressed Mesp1?

(10) Could the authors clarify if their analysis at E7 comprises a mixture of embryonic stages or a precisely defined embryonic stage for both the trajectory and epigenetic analyses? How do the authors know that cells of the second lineage are readily present in the E7 mesoderm they analysed (clusters 0, 1, and 2 for the multiomic analysis)?

(11) Could the authors further comment on the active Notch signaling observed in the first and second lineages, considering that Notch's role in the early steps of endocardial lineage commitment, but not of CMs, during gastrulation has been previously described by Lescroart et al. (2018)?

(12) In cluster 8, Figure 2D, it seems that levels of accessibility in cluster 8 are relatively high for genes associated with endothelium/endocardium development in addition to MJH genes. Could the authors comment and/or provide further analysis?

(13) Can the authors clarify why they state that cluster 8 DAEs are primed before the full activation of their target genes, considering that Bmp4 and Hand1 peak activities seem to coincide with their gene expression in Figure 2G?

(14) Did the authors extend the multiomic analysis to Nanog+ epiblast cells at E7 and investigate if cardiac/mesodermal priming exists before mesodermal induction (defined by T/Mesp1 onset of expression)?

(15) In the absence of duplicates, it is impossible to statistically compare the proportions of mesodermal cell populations in Hand1 wild-type and knockout (KO) embryos or to assess for abnormal accumulation of PS, NM, and MM cells. Could the authors analyse the proportions of cells by careful imaging of Hand1 wild-type and KO embryos instead?

(16) Could the authors provide high-resolution images for Figure 7 B-C-D as they are currently hard to interpret?

Reviewer #1 (Public Review):

Summary:

This paper presents a class of small molecule inhibitors of tau aggregation which was discovered through a computational screen. Analogs were generated and tested for their ability to inhibit fibril formation.

Strengths:

A few of the analogs were found to have sub-stoichiometric activity. A comparison of unseeded and seeded aggregation kinetics suggests that these compounds preferentially target early-stage aggregation.

Weaknesses:

The authors state their interest is in finding compounds that target monomeric states of tau, but their only detection method is late-stage fibril formation. In this respect, they have not really defined a mechanism of action. They state their plan to use hydrogen-exchange mass spectrometry, but there are other techniques, such as single-molecule FRET and measurement of intramolecular reconfiguration. Additionally, there is information that can be gleaned from detailed kinetic modeling of the ThT kinetics to include monomer dynamics, formation of oligomers, and secondary nucleation of fibrils.

Reviewer #2 (Public Review):

Summary:

James et al, in this study, build on their previous work investigating tau as a drug target. The authors identify tryptanthrin (TA) and its analogs as powerful inhibitors of tau4RD aggregation, even at low concentrations (nanomolar range). Interestingly, these analogs specifically target the initial stages of aggregation, where tau self-association first begins. This targeted approach effectively explains why such small amounts of tryptanthrin analogs are sufficient for inhibition. The study further shows that slight modifications to the structure of these molecules can significantly impact their effectiveness.

Strengths:

The experiments are well-designed and executed. The reviewer, in particular, appreciates the authors for the simple yet intelligent study design to understand the mechanism of aggregation inhibition by TA analogs.

Weaknesses:

Certain areas in the manuscript need clarifications, revisions, or additional supporting studies to strengthen the outcomes. For example, the authors mostly apply a single approach to assess tau aggregation or aggregation inhibition. Using additional techniques as suggested below will be helpful.

Reviewer #1 (Public Review):

Summary:

The study conducted by the Shouldiner's group advances the understanding of mitochondrial biology through the utilization of their bi-genomic (BiG) split-GFP assay, which they had previously developed and reported. This research endeavors to consolidate the catalog of matrix and inner membrane mitochondrial proteins. In their approach, a genetic framework was employed wherein a GFP fragment (GFP1-10) is encoded within the mitochondrial genome. Subsequently, a collection of strains was created, with each strain expressing a distinct protein tagged with the GFP11 fragment. The reconstitution of GFP fluorescence occurs upon the import of the protein under examination into the mitochondria.

Strengths:

Notably, this assay was executed under six distinct conditions, facilitating the visualization of approximately 400 mitochondrial proteins. Remarkably, 50 proteins were conclusively assigned to mitochondria for the first time through this methodology. The strains developed and the extensive dataset generated in this study serve as a valuable resource for the comprehensive study of mitochondrial biology. Specifically, it provides a list of 50 "eclipsed" proteins whose role in mitochondria remains to be characterized.

Weaknesses:

The work could include some functional studies of at least one of the newly identified 50 proteins.

Reviewer #2 (Public Review):

The authors addressed the question of how mitochondrial proteins that are dually localized or only to a minor fraction localized to mitochondria can be visualized on the whole genome scale. For this, they used an established and previously published method called BiG split-GFP, in which GFP strands 1-10 are encoded in the mitochondrial DNA and fused the GFP11 strand C-terminally to the yeast ORFs using the C-SWAT library. The generated library was imaged under different growth and stress conditions and yielded positive mitochondrial localization for approximately 400 proteins. The strength of this method is the detection of proteins that are dually localized with only a minor fraction within mitochondria, which so far has hampered their visualization due to strong fluorescent signals from other cellular localizations. The weakness of this method is that due to the localization of the GFP1-10 in the mitochondrial matrix, only matrix proteins and IM proteins with their C-termini facing the matrix can be detected. Also, proteins that are assembled into multimeric complexes (which will be the case for probably a high number of matrix and inner membrane-localized proteins) resulting in the C-terminal GFP11 being buried are likely not detected as positive hits in this approach. Taking these limitations into consideration, the authors provide a new library that can help in the identification of eclipsed protein distribution within mitochondria, thus further increasing our knowledge of the complete mitochondrial proteome. The approach of global tagging of the yeast genome is the logical consequence after the successful establishment of the BiG split-GFP for mitochondria. The authors also propose that their approach can be applied to investigate the topology of inner membrane proteins, however, for this, the inherent issue remains that it cannot be excluded that even the small GFP11 tag can impact on protein biogenesis and topology. Thus, the approach will not overcome the need to assess protein topology analysis via biochemical approaches on endogenous untagged proteins.

Reviewer #3 (Public Review):

Summary:

Here, Bykov et al move the bi-genomic split-GFP system they previously established to the genome-wide level in order to obtain a more comprehensive list of mitochondrial matrix and inner membrane proteins. In this very elegant split-GFP system, the longer GFP fragment, GFP1-10, is encoded in the mitochondrial genome and the shorter one, GFP11, is C-terminally attached to every protein encoded in the genome of yeast Saccharomyces cerevisiae. GFP fluorescence can therefore only be reconstituted if the C-terminus of the protein is present in the mitochondrial matrix, either as part of a soluble protein, a peripheral membrane protein, or an integral inner membrane protein. The system, combined with high-throughput fluorescence microscopy of yeast cells grown under six different conditions, enabled the authors to visualize ca. 400 mitochondrial proteins, 50 of which were not visualised before and 8 of which were not shown to be mitochondrial before. The system appears to be particularly well suited for analysis of dually localized proteins and could potentially be used to study sorting pathways of mitochondrial inner membrane proteins.

Strengths:

Many fluorescence-based genome-wide screens were previously performed in yeast and were central to revealing the subcellular location of a large fraction of yeast proteome. Nonetheless, these screens also showed that tagging with full-length fluorescent proteins (FP) can affect both the function and targeting of proteins. The strength of the system used in the current manuscript is that the shorter tag is beneficial for the detection of a number of proteins whose targeting and/or function is affected by tagging with full-length FPs.

Furthermore, the system used here can nicely detect mitochondrial pools of dually localized proteins. It is especially useful when these pools are minor and their signals are therefore easily masked by the strong signals coming from the major, nonmitochondrial pools of the proteins.

Weaknesses:

My only concern is that the biological significance of the screen performed appears limited. The dataset obtained is largely in agreement with several previous proteomic screens but it is, unfortunately, not more comprehensive than them, rather the opposite. For proteins that were identified inside mitochondria for the first time here or were identified in an unexpected location within the organelle, it remains unclear whether these localizations represent some minor, missorted pools of proteins or are indeed functionally important fractions and/or productive translocation intermediates. The authors also allude to several potential applications of the system but do little to explore any of these directions.

Reviewer #1 (Public Review):

Summary:<br /> Overall, this study provides a meticulous comparison of developmental transcriptomes between two sub-species of the annelid Streblospio benedicti. Different lineages of S. benedicti maintain one of two genetically programmed alternative life histories, the ancestral planktotrophic or derived lecithotrophic forms of development. This contrast is also seen at the inter-species level in many marine invertebrate taxa, such as echinoderms and molluscs. The authors report relatively (surprisingly?) modest differences in transcriptomes overall, but also find some genes whose expression is essentially morph-specific (which they term "exclusive").

Strengths:<br /> The study is based on dense and appropriately replicated sampling of early development. The tight clustering of each stage/morph combination in PCA space suggests the specimens were accurately categorized. The similar overall trajectories of the two morphs was surprising to me for two stage: 1) the earliest stage (16-cell), at which we might expect maternal differences due to the several-fold difference in zygote size, and 2) the latest stage (1-week), where there appears to be the most obvious morphological difference. This is why we need to do experiments!

The examination of F1 hybrids was another major strength of the study. It also produced one of the most surprising results: though intermediate in phenotype, F1 embryos have the most distinct transcriptomes, and reveal a range of fixed, compensatory differences in the parental lines. Further, the F1 lack expression of nearly all transcripts identified as morph-specific in the pure parental lines. Since the F1 larvae present intermediate traits combining the features of both morphs, this implies that morph-specific transcripts are not actually necessary for morph-specific traits. This is interesting and somewhat counter to what one might naively expect.

Weaknesses:<br /> Overall I really enjoyed this paper, and in its revised form it addresses some concerns I had in the first version. I still see a few places where it can be tightened and made more insightful.

Reviewer #2 (Public Review):

The manuscript by Harry and Zakas determined the extent to which gene expression differences contribute to developmental divergence by using a model that has two distinct developmental morphs within a single species. Although the authors did collect a valuable dataset and trends in differential expression between the two morphs of S. benedicti were presented, we found limitations about the methods, system, and resources that the authors should address.

We have two major points:

(1) Background information about the biological system needs to be clarified in the introduction of this manuscript. The authors stated that F1 offspring can have intermediate larval traits compared to the parents (Line 81). However, the authors collected F1 offspring at the same time as the mother in the cross. If offspring have intermediate larval traits, their developmental timeline might be different than both parents and necessitate the collection of offspring at different times to obtain the same stages as the parents. Could the authors (1) explain why they collected offspring at the same time as parents given that other literature and Line 81 state these F1 offspring develop at intermediate rates, and (2) add the F1 offspring to Figure 1 to show morphological and timeline differences in development?

Additionally, the authors state (Lines 83-85) that they detail the full-time course of embryogenesis for both the parents and the F1 crosses. However, we do not see where the authors have reported the full-time course for embryogenesis of the F1 offspring. Providing this information would shape the remaining results of the manuscript.

(2) We have several concerns about the S. benedicti genome and steps regarding the read mapping for RNA-seq:

The S. benedicti genome used (Zakas et al. 2022) was generated using the PP morph. The largest scaffolds of this assembly correspond to linkage groups, showing the quality of this genome. The authors should point out in the Methods and/or Results sections that the quality of this genome means that PP-specific gene expression can be quantified well. However, the challenges and limitations of mapping LL-specific expression data to the PP genome should be discussed.

It is possible that the authors did not find exclusive gene expression in the LL morph because they require at least one gene to be turned on in one morph as part of the data-cleaning criteria. Because the authors are comparing all genes to the PP morph, they could be missing true exclusive genes responsible for the biological differences between the two morphs. Did they make the decision to only count genes expressed in one stage of the other morph because the gene models and mapping quality led to too much noise?

The authors state that the mapping rates between the two morphs are comparable (Supplementary Figure 1). However, there is a lot of variation in mapping the LL individuals (~20% to 43%) compared to the PP individuals. What is the level of differentiation within the two morphs in the species (pi and theta)? The statistical tests for this comparison should be added and the associated p-value should be reported. The statistical test used to compare mapping rates between the two morphs may be inappropriate. The authors used Salmon for their RNA alignment and differential expression analysis, but it is possible that a different method would be more appropriate. For example, Salmon has some limitations as compared to Kallisto as others have noted. The chosen statistical test should be explained, as well as how RNA-seq data are processed and interpreted.

What about the read mapping rate and details for the F1 LP and PL individuals? How did the offspring map to the P genome? These details should be included in Supplementary Figure 1. Could the authors also provide information about the number of genes expressed at each stage in the F1 LP and PL samples in S Figure 2? How many genes went into the PCA? Many of these details are necessary to evaluate the F1 RNA-seq analyses.

Generally, the authors need to report the statistics used in data processing more thoroughly. The authors need to report the statistics used to (1) process and evaluate the RNA-seq data and (2) determine the significance between the two morphs (Supplementary Figures 1 and 2).

Reviewer #1 (Public Review):

Summary:

The endocannabinoid system (ECS) components are dysregulated within the lesion microenvironment and systemic circulation of endometriosis patients. Using endometriosis mouse models and genetic loss of function approaches, Lingegowda et al. report that canonical ECS receptors, CNR1 and CNR2, are required for disease initiation, progression, and T-cell dysfunction.

Strengths:

The approach uses genetic approaches to establish in vivo causal relationships between dysregulated ECS and endometriosis pathogenesis. The experimental design incorporates both bulk and single-cell RNAseq approaches, as well as imaging mass spectrometry to characterize the mouse lesions. The identification of immune-related and T-cell-specific changes in the lesion microenvironment of CNR1 and CNR2 knockout (KO) mice represents a significant advance

Weaknesses:

Although the mouse phenotypic analyses involves a detailed molecular characterization of the lesion microenvironment using genomic approaches, detailed measurements of lesion size/burden and histopathology would provide a better understanding of how CNR1 or CNR2 loss contributes to endometriosis initiation and progression. The cell or tissue-specific effects of the CNR1 and CNR2 are not incorporated into the experimental design of the studies. Although this aspect of the approach is recognized as a major limitation, global CNR1 and CNR2 KO may affect normal female reproductive tract function, ovarian steroid hormone levels, decidualization response, or lead to preexisting alterations in host or donor tissues, which could affect lesion establishment and development in the surgically induced, syngeneic mouse model of endometriosis.

Reviewer #2 (Public Review):

Summary:

The endocannabinoid system (ECS) regulates many critical functions, including reproductive function. Recent evidence indicates that dysregulated ECS contributes to endometriosis pathophysiology and microenvironment. Therefore, the authors further examined the dysregulated ECS and its mechanisms in endometriosis lesion establishment and progression using two different endometrial sources of mouse models of endometriosis with CNR1 and CNR2 knockout mice. The authors presented differential gene expressions and altered pathways, especially those related to the adaptive immune response in CNR1 and CNR2 ko lesions. Interstingly, the T-cell population was dramatically reduced in the peritoneal cavity lacking CNR2, and the loss of proliferative activity of CD4+ T helper cells. Imaging mass cytometry analysis provided spatial profiling of cell populations and potential relationships among immune cells and other cell types. This study provided fundamental knowledge of the endocannabinoid system in endometriosis pathophysiology.

Strengths:

Dysregulated ECS and its mechanisms in endometriosis pathogenesis were assessed using two different endometrial sources of mouse models of endometriosis with CNR1 and CNR2 knockout mice. Not only endometriotic lesions but also peritoneal exudate (and splenic) cells were analyzed to understand the specific local disease environment under the dysregulated ECS.

Providing the results of transcriptional profiles and pathways, immune cell profiles, and spatial profiles of cell populations support altered immune cell population and their disrupted functions in endometriosis pathogenesis via dysregulation of ECS.

L386: Role of CNR2 in T cells: Finding nearly absent CD3+ T cells in the peritoneal cavity of CNR2 ko mice is intriguing.

Interpretation of the results is well-described in discussion.

Weaknesses:

The study was terminated and characterized 7 days after EM induction surgery without the details for selecting the time point to perform the experiments.

The authors also mentioned that altered eutopic endometrium contributes to the establishment and progression of endometriosis. This reviewer agrees L324-325. If so, DEGs are likely identified between eutopic endometrium (with/without endometriosis lesion induction) and ectopic lesions. It would be nice to see the data (even though using publicly available data sets).

Figure 7 CDEF. Please add the results of the statistical analyses and analyzed sample numbers. L444-450 cannot be reviewed without them.

This reviewer agrees L498-500. In contrast, retrograded menstrual debris is not decidualized. The section could be modified to avoid misunderstanding.

The authors addressed all my concerns. I do not have any comments.

Reviewer #1 (Public Review):

The authors showed that autophagy-related genes are involved in plant immunity by regulating the protein level of the salicylic acid receptor, NPR1.

The experiments are carefully designed and the data is convincing. The authors did a good job of understanding the relationship between ATG6 and NRP1.

The authors have addressed most of my previous concerns.

Reviewer #2 (Public Review):

The manuscript by Zhang et al. explores the effect of autophagy regulator ATG6 on NPR1-mediated immunity. The authors propose that ATG6 directly interacts with NPR1 in the nucleus to increase its stability and promote NPR1-dependent immune gene expression and pathogen resistance. This novel role of ATG6 is proposed to be independent of its role in autophagy in the cytoplasm. The authors demonstrate through biochemical analysis that ATG6 interacts with NPR1 in yeast and very weakly in vitro. They further demonstrate using overexpression transgenic plants that in the presence of ATG6-mcherry the stability of NPR1-GFP and its nuclear pool is increased.

Comments on revised version:

The authors demonstrate the correlation between overexertion of atg6 and higher stability and activity of npr1. They claim a novel activity of atg6 in the nucleus.<br /> Overall, the experimental scope of the study is solid, however, the over-interpretation of the results substantially reduces the significance and value of this study for the target plant immunity readership.

Reviewer #1 (Public Review):

Summary:

In this well-designed study, the authors of the manuscript have analyzed the impact of individually silencing 90 lipid transfer proteins on the overall lipid composition of a specific cell type. They confirmed some of the evidence obtained by their own and other research groups in the past, and additionally, they identified an unreported role for ORP9-ORP11 in sphingomyelin production at the trans-Golgi. As they delved into the nature of this effect, the authors discovered that ORP9 and ORP11 form a dimer through a helical region positioned between their PH and ORD domains.

Strengths:

This well-designed study presents compelling new evidence regarding the role of lipid transfer proteins in controlling lipid metabolism. The discovery of ORP9 and ORP11's involvement in sphingolipid metabolism invites further investigation into the impact of the membrane environment on sphingomyelin synthase activity.

Weaknesses:

There are a couple of weaknesses evident in this manuscript. Firstly, there's a lack of mechanistic understanding regarding the regulatory role of ORP9-11 in sphingomyelin synthase activity. Secondly, the broader role of hetero-dimerization of LTPs at ER-Golgi membrane contact sites is not thoroughly addressed. The emerging theme of LTP dimerization through coiled domains has been reported for proteins such as CERT, OSBP, ORP9, and ORP10. However, the specific ways in which these LTPs hetero and/or homo-dimerize and how this impacts lipid fluxes at ER-Golgi membrane contact sites remain to be fully understood.

Regardless of the unresolved points mentioned above, this manuscript presents a valuable conceptual advancement in the study of the impact of lipid transfer on overall lipid metabolism. Moreover, it encourages further exploration of the interplay among LTP actions across various cellular organelles.

Reviewer #2 (Public Review):

Summary:

The authors set out to determine which lipid transfer proteins impact the lipids of Golgi apparatus, and they identified a reasonable number of "hits" where the lack of one lipid transfer protein affected a particular Golgi lipid or class of lipids. They then carried out something close to a "proof of concept" for one lipid (sphingomyelin) and two closely related lipid transfer proteins (ORP9/ORP11). They looked into that example in great detail and found a previous unknown relationship between the level of phosphatidylserine in the Golgi (presumably trans-Golgi, trans-Golgi Network) and function of the sphingomyelin synthase enzyme. This was all convincingly done - results support their conclusions - showing that the authors achieved their aims.

Impact:

There are likely to be 2 types of impact:

(I) cell biology: sphoingomyelin synthase, ORP9/11 will be studied in future in more informed ways to understand (a) the role of different Golgi lipids - this work opens that out and produces a to more questions than answers (b) the role of different ORPs: what distinguishes ORP11 from its paralogy ORP10?

(ii) molecular biochemistry: combining knockdown miniscreen with organelle lipidomics must be time-consuming, but here it is shown to be quite a powerful way to discover new aspects of lipid-based regulation of protein function. This will be useful to others as an example, and if this kind of workflow could be automated, then the possible power of the method could be widely applied.

Strengths:

Nicely controlled data;

Wide-ranging lipidomics dataset with repeats and SDs - all data easily viewed.

Simple take home message that PS traffic to the TGN by ORP9/11 is required for some aspect of SMS1 function.

Weaknesses:

Model and Discussion:

Despite the authors saying that this has been addressed in their rebuttal, I still struggle to find any ideas about the aspect of SMS1 function that is being affected.

As I mentioned before, even if no further experiments were carried out the authors could discuss possibilities. one might speculate what the PS is being used for. For example, is it a co-factor for integral membrane proteins, such as flippases? Is it a co-factor for peripheral membrane proteins, such as yet more LTPs? The model could include the work of Peretti et al (2008), which linked Nir2 activity exchanging PI:PA (Yadav et al, 2015) to the eventual function of CERT. Could the PS have a role in removing/reducing DAG produced by CERT?

Reviewer #2 (Public Review):

Summary:

In this work, Mohamed Y. El-Naggar and co-workers present a detailed electronic characterization of cable bacteria from Southern California freshwater sediments. The cable bacteria could be reliably enriched in laboratory incubations, and subsequent TEM characterization and 16S rRNA gene phylogeny demonstrated their belonging to the genus Candidatus Electronema. Atomic force microscopy and two-point probe resistance measurements were then used to map out the characteristics of the conductive nature, followed by microelectrode four-probe measurements to quantify the conductivity.

Interestingly, the authors observe that some freshwater cable bacteria filaments displayed a higher degree of robustness upon oxygen exposure than what was previously reported for marine cable bacteria. Finally, a single nanofiber conductivity on the order of 0.1 S/cm is calculated, which matches the expected electron current densities linking electrogenic sulphur oxidation to oxygen reduction in sediment and is consistent with hopping transport.

Strengths and weaknesses:

A comprehensive study is applied to characterise the conductive properties of the sampled freshwater cable bacteria. Electrostatic force microscopy and conductive atomic force microscopy provide direct evidence of the location of conductive structures. Four-probe microelectrode devices are used to quantify the filament resistance, which presents a significant advantage over commonly used two-probe measurements that include contributions from contact resistances. While the methodology is convincing, I find that some of the conclusions seem to be drawn on very limited sample sizes, which display widely different behaviour. In particular:

The authors observe that the conductivity of freshwater filaments may be less sensitive to oxygen exposure than previously observed for marine filaments. This is indeed the case for an interdigitated array microelectrode experiment (presented in Figure 5) and for a conductive atomic force microscopy experiment (described in line 391), but the opposite is observed in another experiment (Figure S1). It is therefore difficult to assess the validity of the conclusion until sufficient experimental replications are presented.

The calculation of a single nanofiber conductivity is based on experiment and calculation with significant uncertainty. E.g. for the number of nanofibres in a single filament that varies depending on the filament size (Frontiers in microbiology, 2018, 9: 3044.), and the measured CB resistance, which does not scale well with inner probe separation (Figure 5). A more rigorous consideration of these uncertainties is required.

Comments on revised version:

The authors address all of the comments carefully.

Reviewer #1 (Public Review):

Little is known about the local circuit mechanisms in the preoptic area (POA) that regulate body temperature. This carefully executed study investigates the role of GABAergic interneurons in the POA that express neurotensin (NTS). The principal finding is that GABA-release from these cells inhibits neighboring neurons, including warm-activated PACAP neurons, thereby promoting hyperthermia, whereas NTS released from these cells has the opposite effect, causing a delayed activation and hypothermia. This is shown through an elegant series of experiments that include slice recordings alongside matched in vivo functional manipulations. The roles of the two neurotransmitters are distinguished using a cell-type-specific knockout of Vgat as well as pharmacology to block GABA and NTS receptors. Overall, this is an excellent study that is noteworthy for revealing local circuit mechanisms in the POA that control body temperature and also for highlighting how amino acid neurotransmitters and neuropeptides released from the same cell can have opposing physiologic effects.

Reviewer #1 (Public Review):

Summary:

The authors aim to assess the effect of salt stress on root:shoot ratio, identify the underlying genetic mechanisms, and evaluate their contribution to salt tolerance. To this end, the authors systematically quantified natural variations in salt-induced changes in root:shoot ratio. This innovative approach considers the coordination of root and shoot growth rather than exploring biomass and the development of each organ separately. Using this approach, the authors identified a gene cluster encoding eight paralog genes with a domain-of-unknown-function 247 (DUF247), with the majority of SNPs clustering into SR3G (At3g50160). In the manuscript, the authors utilized an integrative approach that includes genomic, genetic, evolutionary, histological, and physiological assays to functionally assess the contribution of their genes of interest to salt tolerance and root development.

Strengths:

The holistic approach and integrative methodologies presented in the manuscript are essential for gaining a mechanistic understanding of a complex trait such as salt tolerance. The authors focused on At3g50160 but included in their analyses additional DUF247 paralogs, which further contributes to the strength of their approach. In addition, the authors considered the developmental stage (young seedlings, early or late vegetative stages) and growth conditions of the plants (agar plates or soil) when investigating the role of SR3G in salt tolerance and root or shoot development.

Weaknesses:

The authors' claims and interpretation of the results are not fully supported by the data and analyses. In several cases, the authors report differences that are not statistically significant (e.g., Figures 4A, 7C, 8B, S14, S16B, S17C), use inappropriate statistical tests (e.g., t-test instead of Dunnett Test/ANOVA as in Figures 10B-C, S19-23), present standard errors that do not seem to be consistent with the post-hoc Tukey HSD Test (e.g., Figures 4, 9B-C, S16B), or lack controls (e.g., Figure 5C-E, staining of the truncated versions with FM4-64 is missing).

In other cases, traits of root system architecture and expression patterns are inconsistent between different assays despite similar growth conditions (e.g., Figures S17A-B vs. 10A-C vs. 6A, and Figures S16B vs. 4A/9B), or T-DNA insertion alleles of WRKY75 that are claimed to be loss-of-function show comparable expression of WRKY75 as WT plants. Additionally, several supplemental figures are mislabeled (Figures S6-9), and some figure panels are missing (e.g., Figures S16C and S17E).

Consequently, the authors' decisions regarding subsequent functional assays, as well as major conclusions about gene function, including SR3G function in root system architecture, involvement in root suberization, and regulation of cellular damage are incomplete.

Reviewer #2 (Public Review):

Salt stress is a significant and growing concern for agriculture in some parts of the world. While the effects of sodium excess have been studied in Arabidopsis and (many) crop species, most studies have focused on Na uptake, toxicity, and overall effects on yield, rather than on developmental responses to excess Na, per se. The work by Ishka and colleagues aims to fill this gap.

Working from an existing dataset that exposed a diverse panel of A. thaliana accessions to control, moderate, and severe salt stress, the authors identify candidate loci associated with altering the root:shoot ratio under salt stress. Following a series of molecular assays, they characterize a DUF247 protein which they dub SR3G, which appears to be a negative regulator of root growth under salt stress.

Overall, this is a well-executed study that demonstrates the functional role played by a single gene in plant response to salt stress in Arabidopsis.

The abstract and beginning of the Discussion section highlight the "new tool" developed here for measuring biomass accumulation. I feel that this distracts from the central aims of the study, which is really about the role of a specific gene in root development under salt stress. I would suggest moving the tool description to less prominent parts of the manuscript.

Reviewer #1 (Public Review):

Summary:

Assessment of cardiac LEC transcriptomes post-MI may yield new targets to improve lymphatic function. scRNAseq is a valid approach as cardiac LECs are rare compared to blood vessel endothelial cells.

Strengths:

Extensive bioinformatics approaches employed by the group.

Weaknesses:

Too few cells are included in scRNAseq data set and the spatial transcriptomics data that was exploited has little relevance, or rather specificity, for cardiac lymphatics. This study seems more like a collection of preliminary transcriptomic data than a conclusive scientific report to help advance the field.

Reviewer #2 (Public Review):

Summary:

This study integrated single-cell sequencing and spatial transcriptome data from mouse heart tissue at different time points post-MI. They identified four transcriptionally distinct subtypes of lymphatic endothelial cells and localized them in space. They observed that LECs subgroups are localized in different zones of infarcted heart with functions. Specifically, they demonstrated that LEC ca III may be involved in directly regulating myocardial injuries in the infarcted zone concerning metabolic stress, while LEC ca II may be related to the rapid immune inflammatory responses of the border zone in the early stage of MI. LEC ca I and LEC collection mainly participate in regulating myocardial tissue edema resolution in the middle and late stages post-MI. Finally, cell trajectory and Cell-Chat analyses further identified that LECs may regulate myocardial edema through Aqp1, and likely affect macrophage infiltration through the galectin9-CD44 pathway. The authors concluded that their study revealed the dynamic transcriptional heterogeneity distribution of LECs in different regions of the infarcted heart and that LECs formed different functional subgroups that may exert different bioeffects in myocardial tissue post-MI.

Strengths:

The study addresses a significant clinical challenge, and the results are of great translational value. All experiments were carefully performed, and their data support the conclusion.

Weaknesses:

(1) Language expression must be improved. Many incomplete sentences exist throughout the manuscript. A few examples: Lines 70-71: In order to further elucidate the effects and regulatory mechanisms of the lymphatic vessels in the repair process of myocardial injury following MI. Lines 71-73: This study, integrated single-cell sequencing and spatial transcriptome data from mouse heart tissue at different time points after MI from publicly available data (E-MTAB-7895, GSE214611) in the ArrayExpress and gene expression omnibus (GEO) databases. Line 88-89: Since the membrane protein LYVE1 can present lymphatic vessel morphology more clearly than PROX1.

(2) The type of animal models (i.e., permeant MI or MI plus reperfusion) included in ArrayExpress and gene expression omnibus (GEO) databases must be clearly defined as these two models may have completely different effects on lymphatic vessel development during post-MI remodeling.

(3) Lines 119-120: Caution must be taken regarding Cav1 as a lymphocyte marker because Cav1 is expressed in all endothelial cells, not limited to LEC.

(4) Figure 1 legend needs to be improved. RZ, BZ, and IZ need to be labeled in all IF images. Day 0 images suggest that RZ is the tissue section from the right ventricle. Was RZ for all other time points sampled from the right ventricular tissue section?

(5) The discussion section needs to be improved and better focused on the findings from the current study.

Reviewer #3 (Public Review):

Summary:

It has been demonstrated that cardiac lymphatics are essential for cardiac health and function. Moreover, post-myocardial infarction, targeting lymphatics by stimulating lymphangiogenesis has been shown to improve cardiac inflammation, fibrosis, and function. Then, the aim of this study was to evaluate the transcriptomic changes of cardiac lymphatic endothelial cells (LECs) after a myocardial infarction, which could reveal new therapeutic targets targeting lymphatic function. Moreover, investigating the cell-cell communication between lymphatic and immune cells would give critical information for a better understanding of the disease.

Strengths:

The use of scRNAseq data to evaluate LECs is an effective strategy considering the small proportion of LECs compared to blood endothelial cells. The extensive bioinformatic analysis used by the authors for three different data sets.

Weaknesses:

Among a total of 44,860 cells, only 242 LECs and 5,688 endothelial cells were identified. This small number of LECs is not representative and is insufficient to reliably distinguish four different clusters. The bioinformatic analysis is not supported by significant results in their in vivo and in vitro experiments.

Reviewer #1 (Public Review):

Summary:

In this study, the authors developed three case studies: (1) transcriptome profiling of two human cell cultures (HEK293 and HeLa), (2) identification of experimentally enriched transcripts in cell culture (RiboMinus and RiboPlus treatments), and (3) identification of experimentally manipulated genes in yeast strains (gene knockouts or strains transformed with plasmids containing the deleted gene for overexpression). Sequencing was performed using the Oxford Nanopore Technologies (ONT), the only technology that allows for real-time analysis. The real-time transcriptomic analysis was performed using NanopoReaTA, a recent toolbox for comparative transcriptional analyses of Nanopore-seq data, developed by the group (Wierczeiko and Pastore et al. 2023). The authors aimed to show the use of the tool developed by them in data generated by ONT, evidencing the versatility of the tool and the possibility of cost reduction since the sequencing by ONT can be stopped at any time since enough data were collected.

Strengths:

Given that Oxford Nanopore Technologies offers real-time sequencing, it is extremely useful to develop tools that allow real-time data analysis in parallel with data generation. The authors demonstrated that this strategy is possible for both human cell lines and yeasts in the case studies presented. It is a useful strategy for the scientific community and it has the potential to be integrated into clinical applications for rapid and cost-effective quality checks in specific experiments such as overexpression of genes.

Weaknesses:

In relation to the RNA-Seq analyses, for a proper statistical analysis, a greater number of replicates should have been performed. The experiments were conducted with a minimal number of replicates (2 replicates for case study 1 and 2 and 3 replicates for case study 3).

Regarding the experimental part, some problems were observed in the conversion to double-stranded and loading for Nanopore-Seq, which were detailed in Supplementary Material 2. This fact is probably reflected in the results where a reduction in the overall sequencing throughput and detected gene number for HEK293 compared to HeLa were observed (data presented in Supplementary Figure 2). It is necessary to use similar quantities of RNA/cDNA since the sequencing occurs in real-time. The authors should have standardized the experimental conditions to proceed with the sequencing and perform the analyses.

Reviewer #2 (Public Review):

Summary:

Transcriptomics technologies play important roles in biological studies. Technologies based on second-generation sequencing, such as mRNA-seq, face some serious obstacles, including isoform analysis, due to short read length. Third-generation sequencing technologies perfectly solve these problems by having long reads, but they are much more expensive. The authors presented a useful real-time strategy to minimize the cost of sequencing with Oxford Nanopore Technologies (ONT). The authors performed three sets of experiments to illustrate the utility of the real-time strategy. However, due to the problems in experimental design and analysis, their aims are not completely achieved. If the authors can significantly improve the experiments and analysis, the strategy they proposed will guide biologists to conduct transcriptomics studies with ONT in a fast and cost-effective way and help studies in both basic research and clinical applications.

Strengths:

The authors have recently developed a computational tool called NanopoReaTA to perform real-time analysis when cDNA/RNA samples are sequenced with ONT (Wierczeiko et al., 2023). The advantage of real-time analysis is that the sequencing can be stopped once enough data is collected to save cost. Here, they described three sets of experiments: a comparison between two human cell lines, a comparison among RNA preparation procedures, and a comparison between genetically modified yeasts. Their results show that the real-time strategy works for different species and different RNA preparation methods.

Weaknesses:

However, especially considering that the computational tool NanopoReaTA is their previous work, the authors should present more helpful guidelines to perform real-time ONT analysis and more advanced analysis methods. There are four major weaknesses:

(1) For all three sets of experiments, the authors focused on sample clustering and gene-level differential expression analysis (DEA), and only did little analysis on isoform level and even nothing in any figures in the main text. Sample clustering and gene-level DEA can be easily and well done using mRNA-seq at a much cheaper cost. Even for initial data quality checking, mRNA-seq can be first done in Illumina MiSeq/NextSeq which is quick, before deep sequencing in HiSeq/NovaSeq. The real power of third-generation RNA sequencing is the isoform analysis due to the long read length. At least for now, PacBio Iso-seq is very expensive and one cannot analyze the data in real-time. Thus, the authors should focus on the real-time isoform analysis of ONT to show the advantages.

(2) The sample sizes are too small in all three sets of experiments: only two for sets 1 and 2, and three for set 3. For DEA, three is the minimal number for proper statistics. But a sample size of three always leads to very poor power. Nowadays, a proper transcriptomics study usually has a larger sample size. Besides the power issue, biological samples always contain many outliers due to many reasons. It is crucial to show whether the real-time analysis also works for larger sample sizes, such as 10, i.e., 20 samples in total. Will the performance still hold when the sample number is increasing? What is the maximum sample number for an ONT run? If the samples need to be split into multiple runs, how the real-time analysis will be adjusted? These questions are quite useful for researchers who plan to use ONT.

(3) According to the manuscript, real-time analysis checks the sequencing data in a few time points, this is usually called sequential analysis or interim analysis in statistics which is usually performed in clinical trials to save cost. Care must be taken while performing these analyses, as repeated checks on the data can inflate the type I error rate. Thus, the authors should develop a sequential analysis procedure for real-time RNA sequencing.

(4) The experimental set 1 (comparison between two completely different human cell lines) and experimental set 2 (comparison among RNA preparation procedures) are not quite biologically meaningful. If it is possible, it is better for the authors to perform an experiment more similar to a real situation for biological discovery. Then the manuscript can attract more researchers to follow its guidelines.

Reviewer #2 (Public Review):

Assessment

This study develops a potentially useful metric for quantifying codon usage adaptation – the Codon Adaptation Index of Species (CAIS) – that is intended to allow for more direct comparisons of the strength of selection at the molecular level across species by controlling for interspecies variation in amino acid usage and GC content. As evidence to support there claim CAIS better controls for GC content and amino acid usage across species, they note that CAIS has only a weak positive correlation with GC% (that does not stand up to multiple hypothesis testing correction) while CAI has a clear negative correlation with GC%. Using CAIS, they find better adapted species have more disordered protein domains; however, excitement about these findings is dampened due to (1) this result is also observed using the effective number of codons (ENC) and

(2) concerns over the interpretation of CAIS as a proxy for the effectiveness of selection.

Public Review

Summary

The goal of the authors in this study is to develop a more reliable approach for quantifying codon usage such that it is more comparable across species. Specifically, the authors wish to estimate the degree of adaptive codon usage, which is potentially a general proxy for the strength of selection at the molecular level. To this end, the authors created the Codon Adaptation Index for Species (CAIS) that attempts to control for differences in amino acid usage and GC% across species. Using their new metric, the authors observe a positive relationship between CAIS and the overall “disorderedness” of a species protein domains. I think CAIS has the potential to be a valuable tool for those interested in comparing codon adaptation across species in certain situations. However, I have certain theoretical concerns about CAIS as a direct proxy for the efficiency of selection sNe when mutation bias changes across species.

Strengths

(1) I appreciate that the authors recognize the potential issues of comparing CAI when amino acid usage varies and correct for this in CAIS. I think this is sometimes an under-appreciated point in the codon usage literature, as CAI is a relative measure of codon usage bias (i.e. only considers synonyms). However, the strength of natural selection on codon usage can potentially vary across amino acids, such that comparing mean CAI between protein regions with different amino acid biases may result in spurious signals of statistical significance.

(2) The CAIS metric presented here is generally applicable to any species that has an annotated genome with protein-coding sequences. A significant improvement over the previous version is the implementation of software tool for applying this method.

(3) The authors do a better job of putting their results in the context of the underlying theory of CAIS compared to the previous version.

(4) The paper is generally well-written.

Weaknesses

(1) The previously observed correlation between CAIS and body size was due to a bug when calculating phylogenetic independent contrasts. I commend the authors for acknowledging this mistake and updating the manuscript accordingly. I feel that the unobserved correlation between CAIS and body size should remain in the final version of the manuscript. Although it is disappointing that it is not statistically significant, the corrected results are consistent with previous findings (Kessler and Dean 2014).

(2) I appreciate the authors for providing a more detailed explanation of the theoretical basis model. However, I remain skeptical that shifts in CAIS across species indicates shifts in the strength of selection. I am leaving the math from my previous review here for completeness.

As in my previous review, let’s take a closer look at the ratio of observed codon frequencies vs. expected codon frequencies under mutation alone, which was previously notated as RSCUS in the original formulation. In this review, I will keep using the RSCUS notation, even though it has been dropped from the updated version. The key point is this is the ratio of observed and expected codon frequencies. If this ratio is 1 for all codons, then CAIS would be 0 based on equation 7 in the manuscript – consistent with the complete absence of selection on codon usage. From here on out, subscripts will only be used to denote the codon and it will be assumed that we are only considering the case of r = genome for some species s.

I think what the authors are attempting to do is “divide out” the effects of mutation bias (as given by Ei), such that only the effects of natural selection remain, i.e. deviations from the expected frequency based on mutation bias alone represents adaptive codon usage. Consider Gilchrist et al. GBE 2015, which says that the expected frequency of codon i at selection-mutation-drift equilibrium in gene g for an amino acid with Na synonymous codons is

where ∆M is the mutation bias, ∆η is the strength of selection scaled by the strength of drift, and φg is the gene expression level of gene g. In this case, ∆M and ∆η reflect the strength and direction of mutation bias and natural selection relative to a reference codon, for which ∆M,∆η = 0. Assuming the selection-mutation-drift equilibrium model is generally adequate to model of the true codon usage patterns in a genome (as I do and I think the authors do, too), the Ei,g could be considered the expected observed frequency codon i in gene g

E[Oi,g].

Let’s re-write the  in the form of Gilchrist et al., such that it is a function of mutation bias ∆M. For simplicity we will consider just the two codon case and assume the amino acid sequence is fixed. Assuming GC% is at equilibrium, the term gr and 1 − gr can be written as

where µx→y is the mutation rate from nucleotides x to y. As described in Gilchrist et al. MBE 2015 and Shah and Gilchrist PNAS 2011, the mutation bias . This can be expressed in terms of the equilibrium GC content by recognizing that

As we are assuming the amino acid sequence is fixed, the probability of observing a synonymous codon i at an amino acid becomes just a Bernoulli process.

If we do this, then

Recall that in the Gilchrist et al. framework, the reference codon has ∆MNNG,NNG \= 0 =⇒ e−∆MNNG,NNG \=

(1) Thus, we have recovered the Gilchrist et al. model from the formulation of Ei under the assumption that natural selection has no impact on codon usage and codon NNG is the pre-defined reference codon. To see this, plug in 0 for ∆η in equation (1).

We can then calculate the expected RSCUS using equation (1) (using notation E[Oi]) and equation (6) for the two codon case. For simplicity assume, we are only considering a gene of average expression (defined as ). Assume in this case that NNG is the reference codon (∆MNNG,∆ηNNG \= 0).

This shows that the expected value of RSCUS for a two codon amino acid is expected to increase as the strength of selection ∆η increases, which is desired. Note that ∆η in Gilchrist et al. is formulated in terms of selection against a codon relative to the reference, such that a negative value represents that a codon is favored relative to the reference. If ∆η = 0 (i.e. selection does not favor either codon), then E[RSCUS] = 1. Also note that the expected RSCUS does not remain independent of the mutation bias. This means that even if sNe (i.e. the strength of natural selection) does not change between species, changes to the strength and direction of mutation bias across species could impact RSCUS. Assuming my math is right, I think one needs to be cautious when interpreting CAIS as representative of the differences in the efficiency of selection across species except under very particular circumstances.

Consider our 2-codon amino acid scenario. You can see how changing GC content without changing selection can alter the CAIS values calculated from these two codons. Particularly problematic appears to be cases of extreme mutation biases, where CAIS tends toward 0 even for higher absolute values of the selection parameter. Codon usage for the majority of the genome will be primarily determined by mutation biases,

with selection being generally strongest in a relatively few highly-expressed genes. Strong enough mutation biases ultimately can overwhelm selection, even in highly-expressed genes, reducing the fraction of sites subject to codon adaptation.

Peer review image 1.

Peer review image 2.

CAIS (Low Expression)

Peer review image 3.

CAIS (Average Expression)

Peer review image 4.

CAIS (High Expression)

If we treat the expected codon frequencies as genome-wide frequencies, then we are basically assuming this genome made up entirely of a single 2-codon amino acid with selection on codon usage being uniform across all genes. This is obviously not true, but I think it shows some of the potential limitations of the CAIS approach. Based on these simulations, CAIS seems best employed under specific scenarios. One such case could be when it is known that mutation bias varies little across the species of interest. Looking at the species used in this manuscript, most of them have a GC content around 0.41, so I suspect their results are okay (assuming things like GC-biased gene conversion are not an issue). Outliers in GC content probably are best excluded from the analysis.

Although I have not done so, I am sure this could be extended to the 4 and 6 codon amino acids. One potential challenge to CAIS is the non-monotonic changes in codon frequencies observed in some species (again, see Shah and Gilchrist 2011 and Gilchrist et al. 2015).

Reviewer #1 (Public Review):

In this work, the authors provide a valuable transcriptomic resource for the intermediate free-living transmission stage (miracidium larva) of the blood fluke. The single-cell transcriptome inventory is beautifully supplemented with in situ hybridization, providing spatial information and absolute cell numbers for many of the recovered transcriptomic states. The identification of sex-specific transcriptomic states within the populations of stem cells was particularly unexpected. The work comprises a rich resource to complement the biology of this complex system.

Comments on revised version:

I have read through the responses and the revised manuscript. I think together this results in an improved version.

Reviewer #2 (Public Review):

Summary:

In this manuscript the authors have generated a single-cell atlas of the miracidium, the first free-living stage of an important human parasite, Schistosoma mansoni. Miracidia develop from eggs produced in the mammalian (human) host and are released into freshwater, where they can infect the parasite's intermediate snail host to continue the life cycle. This study adds to the growing single-cell resources that have already been generated for other life-cycle stages and, thus, provides a useful resource for the field.

Strengths:

Beyond generating lists of genes that are differentially expressed in different cell types, the authors validated many of the cluster-defining genes using in situ hybridization chain reaction. In addition to providing the field with markers for many of the cell types in the parasite at this stage, the authors use these markers to count the total number of various cell types in the organism. Because the authors realized that their cell isolation protocols were biasing the cell types they were sequencing, they applied a second method to help them recover additional cell types.

Schistosomes have ZW sex chromosomes and the authors make the interesting observation that the stem cells at this stage are already expressing sex (i.e. W)-specific genes.

Comments on revised version:

The manuscript has been improved after revisions. The methods, data and analyses broadly support the claims with only minor weaknesses.

Reviewer #1 (Public Review):

This study of mixed glutamate/GABA transmission from axons of the supramammillary nucleus to dentate gyrus seeks to sort out whether the two transmitters are released from the same or different synaptic vesicles. This conundrum has been examined in other dual-transmission cases and even in this particular pathway, there are different views. The authors use a variety of electrophysiological and immunohistochemical methods to reach the surprising (to me) conclusion that glutamate and GABA-filled vesicles are distinct yet released from the same nerve terminals. The strength of the conclusion rests on the abundance of data (approaches) rather than the decisiveness of any one approach, and I came away believing that the boutons may indeed produce and release distinct types of vesicles, but have reservations. Accepting the conclusion, one is now left with another conundrum, not addressed even in the discussion: how can a single bouton sort out VGLUTs and VIAATs to different vesicles, position them in distinct locations with nm precision, and recycle them without mixing? And why do it this way instead of with single vesicles having mixed chemical content? For example, could a quantitative argument be made that separate vesicles allow for higher transmitter concentrations? I feel the paper needs to address these problems with some coherent discussion, at minimum.

Major concerns:

(1) Throughout the paper, the authors use repetitive optogenetic stimulation to activate SuM fibers and co-release glutamate and GABA. There are several issues here: first, can the authors definitively assure the reader that all the short-term plasticity is presynaptic and not due to ChR2 desensitization? This has not been addressed. Second, can the authors also say that all the activated fibers release both transmitters? If for example 20% of the fibers retained a one-transmitter identity and had distinct physiological properties, could that account for some of the physiological findings?

(2) PPR differences in Figures 1F-I are statistically significant but still quite small. You could say they are more similar than different in fact, and residual differences are accounted for by secondary factors like differential receptor saturation.

(3) The logic of the GPCR experiments needs a better setup. I could imagine different fibers released different transmitters and had different numbers of mGluRs, so that one would get different modulations. On the assumption that all the release is from a single population of boutons, then either the mGluRs are differentially segregated within the bouton, or the vesicles have differential responsiveness to the same modulatory signal (presumably a reduced Ca current). This is not developed in the paper.

(4) The biphasic events of Figures 3 and S3: I find these (unaveraged) events a bit ambiguous. Another way to look at them is that they are not biphasic per se but rather are not categorizable. Moreover, these events are really tiny, perhaps generated by only a few receptors whose open probability is variable, thus introducing noise into the small currents.

(5) Figure 4 indicates that the immunohistochemical analysis is done on SuM terminals, but I do not see how the authors know that these terminals come from SuM vs other inputs that converge in DG.

(6) Figure 4E also shows many GluN1 terminals not associated with anything, not even Vglut, and the apparent numbers do not mesh with the statistics. Why?

(7) Do the conclusions based on the fluorescence immuno mesh with the apparent dimensions of the EM active zones and the apparent intermixing of labeled vesicles in immuno EM?

(8) Figure 6 is not so interesting to me and could be removed. It seems to test the obvious: EPSPs promote firing and IPSPs oppose it.

Reviewer #2 (Public Review):

Summary:

In this study, the authors investigated the release properties of glutamate/GABA co-transmission at the supramammillary nucleus (SuM)-granule cell (GC) synapses using in vitro electrophysiology and anatomical approaches at the light and electron microscopy level. They found that SuM to dentate granule cell synapses, which co-release glutamate and GABA, exhibit distinct differences in paired-pulse ratio, Ca2+ sensitivity, presynaptic receptor modulation, and Ca2+ channel-vesicle coupling configuration for each neurotransmitter. The study shows that glutamate/GABA co-release produces independent glutamatergic and GABAergic synaptic responses, with postsynaptic targets segregated. They show that most SuM boutons form distinct glutamatergic and GABAergic synapses in close proximity, characterized by GluN1 and GABAAα1 receptor labeling, respectively. Furthermore, they demonstrate that glutamate/GABA co-transmission exhibits distinct short-term plasticity, with glutamate showing frequency-dependent depression and GABA showing frequency-independent stable depression.

Their findings suggest that these distinct modes of glutamate/GABA co-release by SuM terminals serve as frequency-dependent filters of SuM inputs.

Strengths:

The conclusions of this paper are mostly well supported by the data.

Weaknesses:

Some aspects of Supplementary Figure 1A and the table need clarification. Specifically, the claim that the authors have stimulated an axon fiber rather than axon terminals is not convincingly supported by the diagram of the experimental setup. Additionally, the antibody listed in the primary antibodies section recognizes the gamma2 subunit of the GABAA receptor, not the alpha1 subunit mentioned in the results and Figure 4.

Reviewer #3 (Public Review):

Summary:

In this manuscript, Hirai et al investigated the release properties of glutamate/GABA co-transmission at SuM-GC synapses and reported that glutamate/GABA co-transmission exhibits distinct short-term plasticity with segregated postsynaptic targets. Using optogenetics, whole-cell patch-clamp recordings, and immunohistochemistry, the authors reveal distinct transmission modes of glutamate/GABA co-release as frequency-dependent filters of incoming SuM inputs.

Strengths:

Overall, this study is well-designed and executed; conclusions are supported by the results. This study addressed a long-standing question of whether GABA and glutamate are packaged in the same vesicles and co-released in response to the same stimuli in the SuM-GC synapses (Pedersen et al., 2017; Hashimotodani et al., 2018; Billwiller et al., 2020; Chen et al., 2020; Li et al., 2020; Ajibola et al., 2021). Knowledge gained from this study advances our understanding of neurotransmitter co-release mechanisms and their functional roles in the hippocampal circuits.

Weaknesses:

No major issues are noted. Some minor issues related to data presentation and experimental details are listed below.

Reviewer #2 (Public Review):

Summary:

Previous research shows that humans tend to adjust learning in environments where stimulus-outcome contingencies become more volatile. This learning rate adaptation is impaired in some psychiatric disorders, such as depression and anxiety. In this tudy the authors reanalyze previously published data on a reversal learning task with two volatility levels. Through a new model they provide some evidence for an alternative explanation whereby the learning rate adaptation is driven by different decision-making strategies and not learning deficits. In particular, they propose that adjusting of learning can be explained by deviations from the optimal decision-making strategy (based on maximizing expected utility) due to response stickiness or focus on reward magnitude. Furthermore, a factor related to general psychopathology of individuals with anxiety and depression negatively correlated with the weight on the optimal strategy and response stickiness, while it correlated positively with the magnitude strategy (a strategy that ignores the probability of outcome).

The main strength of the study is a novel and interesting explanation of an otherwise well-established finding in human reinforcement learning. This proposal is supported by rigorously conducted parameter retrieval and the comparison of the novel model to a wide range of previously published models. The authors explore from many angles, if and why the predictions from the new proposed model are superior to previously applied models.

My previous concerns were addressed in the revised version of the manuscript. I believe that the article now provides a new perspective on a well-established learning effect and offer a novel set of interesting response models that can be applied to a wide array of decision-making problems.

I see two limitations of the study not mentioned in the discussion of the manuscript. First, the task features binary inputs and responses, therefore unexpected uncertainty (volatility) is impossible to differentiate from the uncertainty about outcomes, and exploration is inseparable from random choices. Future work could validate these findings in task designs that allow to distinguish these processes. Second, clinical results are based on a small sample of patients and should be interpreted with this in mind.

Reviewer #3 (Public Review):

Summary:

This paper presents a new formulation of a computational model of adaptive learning amid environmental volatility. Using a behavioral paradigm and data set made available by the authors of an earlier publication (Gagne et al., 2020), the new model is found to fit the data well. The model's structure consists of three weighted controllers that influence decisions on the basis of (1) expected utility, (2) potential outcome magnitude, and (3) habit. The model offers an interpretation of psychopathology-related individual differences in decision-making behavior in terms of differences in the relative weighting of the three controllers.

Strengths:

The newly proposed "mixture of strategies" (MOS) model is evaluated relative to the model presented in the original paper by Gagne et al., 2020 (here called the "flexible learning rate" or FLR model) and two other models. Appropriate and sophisticated methods are used for developing, parameterizing, fitting, and assessing the MOS model, and the MOS model performs well on multiple goodness-of-fit indices. Parameters of the model show decent recoverability and offer a novel interpretation for psychopathology-related individual differences. Most remarkably, the model seems to be able to account for apparent differences in behavioral learning rates between high-volatility and low-volatility conditions even with no true condition-dependent change in the parameters of its learning/decision processes. This finding calls into question a class of existing models that attribute behavioral adaptation to adaptive learning rates.

Weaknesses:

The authors have responded to the weaknesses noted previously.

Reviewer #1 (Public Review):

Summary:

Das and Menon describe an analysis of a large open-source iEEG dataset (UPENN-RAM). From encoding and recall phases of memory tasks, they analyzed power and phase-transfer entropy as a measure of directed information flow in regions across a hypothesized tripartite network system. The anterior insula (AI) was found to have heightened high gamma power during encoding and retrieval, which corresponded to suppression of high gamma power in the posterior cingulate cortex (PCC) during encoding but not recall. In contrast, directed information flow from (but not to) AI to mPFC/PCC and dorsal posterior parietal/middle frontal cortex is high during both time periods when PTE is analyzed with broadband but not narrowband activity. They claim that these findings significantly advance an understanding of how network communication facilitates cognitive operations such as control over memory and that the AI of the salience network (SN) is responsible for governing the switch between the frontoparietal network (FPN) and default-mode network (DMN) when shifting between externally- and internally-driven processing.

I find this question interesting and important and agree with the authors that iEEG presents a unique opportunity to investigate the temporal dynamics within network nodes. However, I am not convinced that their claims are supported by the results currently presented. In particular, the fact that network-level communication is not modulated significantly compared to rest and does not relate to behavior suggests that PTE analyses may not be tapping into task-relevant communication. Moreover, dissociation of network effects - present during both encoding and recall - from local power suppression effects - present only during encoding - suggests that these sets of results may index separate and not unitary task processes.

Strengths:

- The authors present results from an impressively sized iEEG sample. For reader context, this type of invasive human data is difficult and time-consuming to collect and many similar studies in high-level journals include 5-20 participants, typically not all of whom have electrodes in all regions of interest. It is excellent that they have been able to leverage open-source data in this way.

- Preprocessing of iEEG data also seems sensible and appropriate based on field standards.

- The authors tackle the replication issues inherent in much of the literature by replicating findings across task contexts, demonstrating that the principles of network communication evidenced by their results generalize in multiple task memory contexts. Again, the number of iEEG patients who have multiple tasks' worth of data is impressive.

Weaknesses:

• The motivation for investigating the tripartite network during memory tasks is not currently well-elaborated. Though the authors mention, for example, that "the formation of episodic memories relies on the intricate interplay between large-scale brain networks (p. 4)", there are no citations provided for this statement, and the reader is unable to evaluate whether the nodes and networks evidenced to support these processes are the same as networks measured here.

• In addition, though the tripartite network has been proposed to support cognitive control processes, and the neural basis of cognitive control is the framed focus of this work, the authors do not demonstrate that they have measured cognitive control in addition to simple memory encoding and retrieval processes. Tasks that have investigated cognitive control over memory (such as those cited on p. 13 - Badre et al., 2005; Badre & Wagner, 2007; Wagner et al., 2001; Wagner et al., 2005) generally do not simply include encoding, delay, and recall (as the tasks used here), but tend to include some manipulation that requires participants to engage control processes over memory retrieval, such as task rules governing what choice should be made at recall (e.g., from Badre et al., 2005 Fig. 1: congruency of match, associative strength, number of choices, semantic similarity). Moreover, though there are task-responsive signatures in the nodes of the tripartite networks, concluding that cognitive control is present because cognitive control networks are active would be a reverse inference.

• It is currently unclear if the directed information flow from AI to DMN and FPN nodes truly arises from task-related processes such as cognitive control or if it is a function of static brain network characteristics constrained by anatomy (such as white matter connection patterns, etc.). This is a concern because the authors did not find that influences of AI on DMN or FPN are increased relative to a resting baseline (collected during the task) or that directed information flow differs in successful compared to unsuccessful retrieval. I doubt that this AI influence is 1) supporting a switch between the DMN and FPN via the SN or 2) relevant for behavior if it doesn't differ from baseline-active task or across accuracy conditions. An additional comparison that may help investigate whether this is reflective of static connectivity characteristics would be a baseline comparison during non-task rest or sleep periods.

• Related to the above concern, it is also questionable how directed information flow from AI facilitates switching between FPN and DMN during both encoding and recall if high gamma activity does not significantly differ in AI versus PCC or mPFC during recall as it does during encoding. It seems erroneous to conclude that the network-level communication is happening or happening with the same effect during both task time points when these effects are decoupled in such a way from the power findings.

• Missing information about the methods used for time-frequency conversion for power calculation and the power normalization/baseline-correction procedure bars a thorough evaluation of power calculation methods and results.

If revisions to the manuscript can address concerns about directed information flow possibly being due to anatomical constraints - such as by indicating that directed information flow is not present during non-task rest or sleep - this work may convey important information about the structure and order of communication between these networks during attention to tasks in general. However, the ability of the findings to address cognitive control-specific communication and the nature of neurophysiological mechanisms of this communication - as opposed to the temporal order and structure of recruited networks - may be limited.

Because phase-transfer entropy is presented as a "causal" analysis in this investigation (PTE), I also believe it is important to highlight for readers recent discussions surrounding the description of "causal mechanisms" in neuroscience (see "Confusion about causation" section from Ross and Bassett, 2024, Nature Neuroscience). A large proportion of neuroscientists (admittedly, myself included) use "causal" only to refer to a mechanism whose modulation or removal (with direct manipulation, such as by lesion or stimulation) is known to change or control a given outcome (such as a successful behavior). As Ross and Bassett highlight, it is debatable whether such mechanistic causality is captured by Granger "causality" (a.k.a. Granger prediction) or the parametric PTE, and the imprecise use of "causation" may be confusing. The authors could consider amending language regarding this analysis if they are concerned about bridging these definitions of causality across a wide audience.

Reviewer #2 (Public Review):

In this study, the authors leverage a large public dataset of intracranial EEG (the University of Pennsylvania RAM repository) to examine electrophysiologic network dynamics involving the participation of salience, frontoparietal, and default mode networks in the completion of several episodic memory tasks. They do this through a focus on the anterior insula (AI; salience network), which they hypothesize may help switch engagement between the DMN and FPN in concert with task demands. By analyzing high-gamma spectral power and phase transfer entropy (PTE; a putative measure of information "flow"), they show that the AI shows higher directed PTE towards nodes of both the DMN and FPN, during encoding and recall, across multiple tasks. They further demonstrate that high-gamma power in the PCC/precuneus is decreased relative to the AI during memory encoding. They interpret these results as evidence of "triple-network" control processes in memory tasks, governed by a key role of the AI.

I commend the authors on leveraging this large public dataset to help contextualize network models of brain function with electrophysiological mechanisms - a key problem in much of the fMRI literature. I also appreciate that the authors emphasized replicability across multiple memory tasks, in an effort to demonstrate conserved or fundamental mechanisms that support a diversity of cognitive processes. However, I believe that their strong claims regarding causal influences within circumscribed brain networks cannot be supported by the evidence as presented. In my efforts to clearly communicate these inadequacies, I will suggest several potential analyses for the authors to consider that might better link the data to their central hypotheses.

(1) As a general principle, the effects that the authors show - both in regards to their high-gamma power analysis and PTE analysis - do not offer sufficient specificity for a reader to understand whether these are general effects that may be repeated throughout the brain, or whether they reflect unique activity to the networks/regions that are laid out in the Introduction's hypothesis. This lack of specificity manifests in several ways, and is best communicated through examples of control analyses.

First, the PTE analysis is focused solely on the AI's interactions with nodes of the DMN and FPN; while it makes sense to focus on this putative "switch" region, the fact that the authors report significant PTE from the AI to nodes of both networks, in encoding and retrieval, across all tasks and (crucially) also at baseline, raises questions about the meaningfulness of this statistic. One way to address this concern would be to select a control region that would be expected to have little/no directed causal influence on these networks and repeat the analysis. Alternatively (or additionally), the authors could examine the time course of PTE as it evolves throughout an encoding/retrieval interval, and relate that to the timing of behavioral events or changes in high-gamma power. This would directly address an important idea raised in their own Discussion, "the AI is well-positioned to dynamically engage and disengage with other brain areas."

Second, the authors state that high-gamma suppression in the PCC/precuneus relative to the AI is an anatomically specific signature that is not present in the FPN. This claim does not seem to be supported by their own evidence as presented in the Supplemental Data (Figures S2 and S3), which to my eye show clear evidence of relative suppression in the MFG and dPPC (e.g. S2a and S3a, most notably) which are notated as "significant" with green bars. I appreciate that the magnitude of this effect may be greater in the PCC/precuneus, but if this is the claim it should be supported by appropriate statistics and interpretation.

(2) I commend the authors on emphasizing replicability, but I found their Bayes Factor (BF) analysis to be difficult to interpret and qualitatively inconsistent with the results that they show. For example, the authors state that BF analysis demonstrates "high replicability" of the gamma suppression effect in Figure 3a with that of 3c and 3d. While it does appear that significant effects exist across all three tasks, the temporal structure of high gamma signals appears markedly different between the two in ways that may be biologically meaningful. Moreover, it appears that the BF analysis did not support replicability between VFR and CATVFR, which is very surprising; these are essentially the same tasks (merely differing in the presence of word categories) and would be expected to have the highest degree of concordance, not the lowest. I would suggest the authors try to analytically or conceptually reconcile this surprising finding.

To aid in interpretability, it would be extremely helpful for the authors to assess across-task similarity in high-gamma power on a within-subject basis, which they are well-powered to do. For example, could they report the correlation coefficient between HGP timecourses in paired-associates versus free-recall tasks, to better establish whether these effects are consistent on a within-subject basis? This idea could similarly be extended to the PTE analysis. Across-subject correlations would also be a welcome analysis that may provide readers with better-contextualized effect sizes than the output of a Bayes Factor analysis.

Reviewer #1 (Public Review):

Summary:

The investigation delves into allosteric modulation within the glycosylated SARS-CoV-2 spike protein, focusing on the fatty acid binding site. This study uncovers intricate networks connecting the fatty acid site to crucial functional regions, potentially paving the way for developing innovative therapeutic strategies.

Strengths:

This article's key strength lies in its rigorous use of dynamic nonequilibrium molecular dynamics (D-NEMD) simulations. This approach provides a dynamic perspective on how the fatty acid binding site influences various functional regions of the spike. A comprehensive understanding of these interactions is crucial in deciphering the virus's behavior and identifying potential targets for therapeutic intervention.

Weaknesses:

The presented evidence is compelling but could be better if this study is supported with sequence analysis to facilitate a complete view of the allosteric networks. The thorough analysis of the simulation results is partially aligned with the discussion because observed in the replicates and the monomers an asymmetry in the perturbations generated by D-NEMD, even when we're using 210 nonequilibrium MD of 10 ns. While the authors claim that the strategy used in this article has been previously validated, the complexity of the spike and the interactions analyzed have required a robust statistical analysis, which is not shown quantitatively. The investigation examines the allosteric modulation within the glycosylated SARS-CoV-2 spike protein, emphasizing the significance of the fatty acid binding site in influencing the structural dynamics and communication pathways essential for viral function, potentially facilitating the development of novel therapeutic strategies. The presented evidence is compelling but needs to be supported by sequence analysis, which will facilitate understanding of the scientific community.

Minor considerations:

Figure S3 shows a discrepancy in the presentation of residue values S325 in the plots of Chains A, B, and C. While chain A shows a value near 0.1, chains B and C plots do not have any value.

Please explain why the plots of figures S6, S7, and S8 show significant changes in several regions, such as RBM and Furin Site. Can these changes be explained?

The flow of the allosteric interaction is complex to visualize just by looking at structures. Could you please include a diagram showing the flow of allosteric interactions (in a sequence diagram or using the structure of the protein)? Or could you include a vector showing how the perturbation done in the FA Active site takes contact with other relevant regions of the Spike protein?

Reviewer #3 (Public Review):

Summary:

In a previous study, the authors analyzed the dynamics of the SARS-CoV2 spike protein through lengthy MD simulations and an out-of-equilibrium sampling scheme. They identified an allosteric interaction network linking a lipid-binding site to other structurally important regions of the spike. However, this study was conducted without considering the impact of glycans. It is now known that glycans play a crucial role in modulating spike dynamics. This new manuscript investigates how the presence of glycans affects the allosteric network connecting the lipid binding site to the rest of the spike. The authors conducted atomistic equilibrium and out-of-equilibrium MD simulations and found that while the presence of glycans influences the structural responses, it does not fundamentally alter the connectivity between the fatty acid site and the rest of the spike.

Strengths:

The manuscript's findings are based on an impressive amount of sampling. The methods and results are clearly outlined, and the analysis is conducted meticulously.

Weaknesses:

The study does not clearly show any new findings. The authors themselves acknowledge that the manuscript mainly presents negative results-indicating that glycans do not significantly impact the allosteric network previously reported in other publications. All the results in the paper are based on a single methodology, and additional independent approaches would be needed to confirm the robustness of these findings. Allosteric networks arise from subtle correlations in protein structural dynamics, and it's uncertain whether the results discussed in this manuscript stem exclusively from the chosen force field and other modeling and analysis decisions, or if they indeed reflect something real.

Reviewer #2 (Public Review):

This is a nice paper illustrating the use of equilibrium/non-equilibrium MD simulations to explore allosteric communication in the Spike protein. The results are described in detail and suggest a complex network of signal transmission patterns. The topic is not completely novel as it has been studied before by the same authors and the impact of glycosylation is moderated and localized at the furin site, so not many new conclusions emerge here. It is suggested that mutations are commonly found in the communication pathway which is interesting, but the authors fail to provide evidence that this is related to a positive selection and not simply to a random effect related to mutations at points that are not crucial for stability or function. One interesting point is the connection of the FA site with an additional site binding heme group. It will be interesting to see reversibility, i.e. removal of the ligand at this site is producing perturbation at the FA site?, does it produce other effects suggesting a cascade of allosteric effects? Finally, the paper lacks details to help reproducibility, in particular, I do not see details on D-NEMD calculations. One interesting point is the connection of the FA site with an additional site binding heme group.

Reviewer #1 (Public Review):

The authors effectively delineate the differential distribution and behaviour of MNPs within the heart, noting that these cells can be characterised by their expression levels of csf1ra and mpeg1.1. Key findings include the identification of distinct origins for larval macrophage populations and the sustained presence of csf1ra-expressing cells on the surface of the adult heart. The study examines the embryonic development of these MNPs, revealing that csf1ra+ cells begin populating the heart from embryonic day 3, while mpeg1.1+ cells colonise the heart around day 10, with a significant increase by day 17. Given that the emergence of mpeg1.1+ cells coincides with the reported timing for the onset of haematopoietic stem cell-derived haematopoiesis, the authors combined kaede-lineage tracing experiments and mutant backgrounds to conclude that the earliest tissue-resident macrophages in the heart are derived from primitive haematopoiesis.

The authors also note that the spatial distribution of MNPs varies, with csf1ra+ cells found on the atrium and ventricle surfaces, while mpeg1.1+ cells are initially located on the surface but later distributed throughout the cardiac tissue. Notably, the study demonstrates that tissue-resident macrophages proliferate rapidly following cardiac injury. The authors observe an increased number of proliferating csf1ra+ cells, especially in csf1ra mutant zebrafish, which likely correspond to primitive-derived tissue-resident macrophages that rapidly respond to injury and contribute to the reduced scarring observed in these mutants.

This manuscript makes an important contribution to the field by enhancing our understanding of the ontogeny of tissue-resident macrophages in the heart and their cellular behaviour in a vertebrate model capable of heart regeneration.

Strengths:

This work presents a landmark study on the ontogeny and cellular behaviour of macrophages in the zebrafish heart as it comprehensively examines their development and distribution in both embryonic and adult stages.

One of the key strengths of this study is its thorough cellular description using a range of available genetic tools. By employing transgenic lines to differentiate between a few MNP subtypes, the authors provide a detailed and nuanced understanding of these cells' origins, distribution, and behaviour. This approach allows for high-resolution characterisation of MNP populations, revealing significant insights into their potential role in cardiac homeostasis and regeneration.

Furthermore, the study's findings are significant as they parallel those observed in mouse models, thereby reinforcing the validity and relevance of the zebrafish as a model organism for studying macrophage function in the context of cardiac injury. This comparative aspect underscores the evolutionary conservation of these cellular processes and enhances the study's impact.

Another notable strength is the use of ex vivo imaging techniques, which enable the authors to observe and study the dynamic behaviour of MNPs in heart tissue in real-time. This live imaging capability is crucial for understanding how these cells interact with their environment, particularly in response to cardiac injury. The ability to visualise MNP proliferation and movement provides valuable insights into the mechanisms underlying tissue repair and regeneration.

Weaknesses:

While the manuscript offers significant insights into the ontogeny and behaviour of MNPs in the zebrafish heart, a few limitations described below should be considered:

One potential issue lies in the lineage tracing experiments using the photoconversion Tg(csf1ra:Gal4); Tg(UAS:kaede) line. The authors photoconverted all cardiac tissue macrophages present at 2 days post-fertilisation (dpf) and examined the hearts of these fish at 21 dpf. Although photoconverted macrophages were still observed at 21 dpf, the majority of cells present in the heart at that time were non-photoconverted (cyan) csf1ra+ cells. While this suggests that early-seeded embryonic csf1ra+ macrophages are retained during late larval stages, the contribution of macrophages derived from haematopoietic stem cells (HSCs) might be overestimated. An important concern is that the kaede-converted cells could have proliferated during the embryonic timeframe analysed, thereby diluting and extinguishing the converted kaede protein. This dilution effect could lead to an underestimation of the contribution of primitive embryonic macrophages relative to the HSC-derived cells, resulting in an inaccurate assessment of the proportion of embryonic-derived tissue-resident macrophages over time.

Moreover, the study reports no significant difference in immune cell numbers in the hearts of cmyb-/- mutants, which have normal primitive haematopoiesis but lack HSCs, at 5 dpf. Given the authors' suggestion that mpeg+ cells originate from the HSC wave, it is essential to assess the number of mpeg+ cells in these mutants at later stages. This assessment would clarify whether mpeg+ cells are indeed HSC-derived or if csf1ra+ cells later switch on mpeg expression. Without this additional data, conclusions about the origins of mpeg+ cells remain speculative.

The study's reliance on available genetic tools, while a strength, also introduces limitations. The use of only a few transgenic lines will not fully capture the complexity and diversity of MNP populations, leading to an incomplete understanding of their roles and dynamics.

Furthermore, while the use of ex vivo imaging provides dynamic insights into cell behaviour, it may not fully capture the complexity of in vivo conditions, possibly overlooking interactions and influences present in the living organism.

The manuscript would benefit from increasing the sample sizes to ensure the robustness of the findings. The use of Phalloidin staining to delineate single cells more accurately would also enhance the precision of cell counting and improve the overall data quality.

The study could also benefit from a more in-depth exploration of the functional consequences of MNP heterogeneity in the heart. While the cellular characterisations are thorough, the molecular and regulatory insights provided by the study are limited to a couple of RT-PCRs for some known genes.

Overall, the manuscript by Moyse and colleagues significantly advances our understanding of the ontogeny and behaviour of macrophages in the zebrafish heart, revealing important parallels with mammalian models. However, the points above should be carefully considered when interpreting the results presented in this study.

Reviewer #2 (Public Review):

In this manuscript, Moyse et. al. investigated the origins and potential functions of distinct populations of mononuclear phagocytes (MNPS) in the heart of developing and adult zebrafish. First, the authors demonstrate that the embryonic zebrafish heart contains macrophages early in development and that mpeg1.1 and csf1ra expressing macrophages vary across time and location and present that cardiac tissue macrophages (cTMs) in the juvenile heart are derived by primitive hematopoiesis. By combining the two transgenes, the authors demonstrate that there are 3 distinct (later determined to be 4) subpopulations of MNPs in adult hearts and that the distribution of these subtypes is distinct within the heart consistent with differing distributions of primitive and definitive macrophages in mammalian hearts. Further analysis of these populations demonstrates distinct morphologies of the subpopulations and analysis of markers conserved in mammals demonstrates distinct expression profiles as well. The authors go on to demonstrate that these subpopulations also demonstrate distinct behaviors via ex-vivo imaging. Lastly, the authors investigated the roles of these subpopulations in a model of cardiac injury in adult zebrafish and demonstrated that primitive-derived cTMs proliferate after injury consistent with mammalian models and that the proliferation of these macrophages likely results in reduced scarring in csf1ra mutants which have reduced recruitment of pro-inflammatory definitive macrophages. The data presented in this manuscript provides solid evidence that zebrafish MNPs behave consistently with those in mammals and further solidifies the use of zebrafish models as a useful tool in studying the role of these cells in cardiac repair and regeneration.

The data presented in this manuscript strongly supports the conclusions made by the authors and utilizes novel techniques. The authors appear to have achieved the goals they set out to investigate. The use of ex-vivo imaging to visualize the movement of these macrophage populations within the heart is especially compelling. The combined use of commonly used transgenic reporters for zebrafish macrophages is a very nice use of existing tools to address new questions and highlight the distinct populations of macrophages. While the overall manuscript is very strong and is likely to have a great impact on the field, there are a few weaknesses that should be addressed prior to acceptance:

(1) The reasoning for N used in many of these experiments is not addressed, nor is the question of the number of times experiments were performed. For purposes of rigor and reproducibility, these questions should be addressed in the methods.

(2) In investigating homologs of zebrafish and mammalian genes, the inclusion of additional classical markers and novel markers of subpopulations highlighted in numerous recent studies using single-cell RNA sequencing would greatly add to the impact.

(3) The description of the RT-PCR experiment is not included in the methods. Detailed methods should be provided including probe sequences. Additionally, a quantitative method of presenting this data would strengthen the conclusions presented here as well as the inclusion of additional markers as discussed previously.

Reviewer #3 (Public Review):

In this manuscript, Moyse et al. build on previously published data and investigate several subtypes of mononuclear phagocytes within the larval, juvenile, and adult zebrafish heart. Through the use of mpeg1.1 and csfr1a transgenic lines, the authors characterize the seeding of macrophages in the embryonic and larval heart and describe localization, proportions, morphology, and behavior of several subtypes of mpeg1.1 and csfr1a macrophages in the adult uninjured heart. The authors further provide an analysis of marker gene expression in the differing macrophage subtypes in the uninjured adult heart. Lastly, the authors perform analyses of how these populations respond to cardiac injury and show that csfr1a is important for the proportion and proliferation of these different subtypes of macrophages in the heart.

While the presence of cardiac resident macrophages and their importance in heart regeneration and cardiac disease have been extensively studied in the mouse, the same attention has only recently been given to macrophages in the adult zebrafish heart. This study provides insight into many parallels that exist between resident macrophages in the mouse and zebrafish heart, and while not especially novel, this concept is important for the zebrafish cardiac field. Overall, the conclusions of this study are mostly well supported by the data, but further analysis of marker gene expression in the various macrophage subtypes described would be an important and useful addition for zebrafish researchers studying macrophages in heart regeneration. For example, how are markers of cardiac resident macrophages (described in Wei et al, doi: 10.7554/eLife.84679) expressed in the different mpeg1.1 and csfr1a populations?

Reviewer #1 (Public Review):

Summary:

The authors aimed to investigate the contribution of antigenic drift in the HA and NA genes of seasonal influenza A(H3N2) virus to their epidemic dynamics. Analyzing 22 influenza seasons before the COVID-19 pandemic, the study explored various antigenic and genetic markers, comparing them against indicators characterizing the epidemiology of annual outbreaks. The central findings highlight the significant influence of genetic distance on A(H3N2) virus epidemiology and emphasize the role of A(H1N1) virus incidence in shaping A(H3N2) epidemics, suggesting subtype interference as a key factor.

Major Strengths:

The paper is well-organized, written with clarity, and presents a comprehensive analysis. The study design, incorporating a span of 22 seasons, provides a robust foundation for understanding influenza dynamics. The inclusion of diverse antigenic and genetic markers enhances the depth of the investigation, and the exploration of subtype interference adds valuable insights.

Major Weaknesses:

While the analysis is thorough, some aspects require deeper interpretation, particularly in the discussion of certain results. Clarity and depth could be improved in the presentation of findings, and minor adjustments are suggested. Furthermore, the evolving dynamics of H3N2 predominance post-2009 need better elucidation.

Comments on revised version:

The authors have addressed each of the comments well. I have no further comments.

Reviewer #1 (Public Review):

Summary:

In this study, Maestri et al. use an integrative framework to study the evolutionary history of coronaviruses. They find that coronaviruses arose recently rather than having undergone ancient codivergences with their mammalian hosts. Furthermore, recent host switching has occurred extensively, but typically between closely related species. Humans have acted as an intermediate host, especially between bats and other mammal species.

Strengths:

The study draws on a range of data sources to reconstruct the history of virus-host codivergence and host switching. The analyses include various tests of robustness and evaluations through simulation.

Weaknesses:

The analyses are limited to a single genetic marker (RdRp) from coronaviruses, but using other sections of the genome might lead to different conclusions. The genetic marker also lacks resolution for recent divergences, which precludes the detailed examination of recent host switches. Careful and detailed reconstruction of the timescale would be helpful for clarifying the evolutionary history of coronaviruses alongside their hosts.

Reviewer #2 (Public Review):

Summary:

In their study titled "Recent evolutionary origin and localized diversity hotspots of mammalian coronaviruses," authors Benoît Perez-Lamarque, Renan Maestri, Anna Zhukova, and Hélène Morlon investigate the complex evolutionary history of coronaviruses, particularly those affecting mammals, including humans. The study focuses on unraveling the evolutionary trajectory of these viruses, which have shown a high propensity for causing pandemics, as evidenced by the SARS-CoV2 outbreak.<br /> The research addresses a significant gap in our understanding of the evolutionary dynamics of coronaviruses, particularly their history, patterns of host-to-host transmission, and geographical spread. These aspects are important for predicting and managing future pandemic scenarios.

Historically, studies have employed cophylogenetic tests to explore virus-host relationships within the Coronaviridae family, often suggesting a long history of virus-host codiversification spanning millions of years. However, the team led by Perez-Lamarque proposes a novel phylogenetic framework that contrasts this traditional view. Their approach, which involves adapting gene tree-species tree reconciliation, is designed to robustly test the validity of two competing scenarios: an ancient origination and codiversification versus a more recent emergence and diversification through host switching.

Upon applying this innovative framework to the study of coronaviruses and their mammalian hosts, the authors' findings challenge the prevailing notion of a deep evolutionary history. Instead, their results strongly support a scenario where coronaviruses have a more recent origin, likely in bat populations, followed by diversification predominantly through host-switching events. This diversification, interestingly, seems to occur preferentially within mammalian orders.

A critical aspect of their findings is the identification of hotspots of coronavirus diversity, particularly in East Asia and Europe. These regions align with the proposed scenario of a relatively recent origin and subsequent localized host-switching events. The study also highlights the rarity of spillovers from bats to other species, yet underscores the relatively higher likelihood of such spillovers occurring towards humans, suggesting a significant role for humans as an intermediate host in the evolutionary journey of these viruses.

The research also points out the high rates of host-switching within mammalian orders, including between humans, domesticated animals, and non-flying wild mammals.<br /> In conclusion, the study by Perez-Lamarque and colleagues presents an important quantitative advance in our understanding of the evolutionary history of mammalian coronaviruses. It suggests that the long-held belief in extensive virus-host codiversification may have been substantially overestimated, paving the way for a reevaluation of how we understand, predict, and potentially control the spread of these viruses.

Strengths:

The study is conceptually robust, and its conclusions are convincing.

Weaknesses:

The authors could only use the "undated" model in ALE, with the dated method (which only allows time-consistent transfers) failing on their dataset. The authors did attempt to address this issue in the revision, albeit with limited success.

Reviewer #1 (Public Review):

Summary:

This study, titled "Enhancing Bone Regeneration and Osseointegration using rhPTH(1-34) and Dimeric R25CPTH(1-34) in an Osteoporotic Beagle Model," provides valuable insights into the therapeutic effects of two parathyroid hormone (PTH) analogs on bone regeneration and osseointegration. The research is methodologically sound, employing a robust animal model and a comprehensive array of analytical techniques, including micro-CT, histological/histomorphometric analyses, and serum biochemical analysis.

Strengths:

The use of a large animal model, which closely mimics postmenopausal osteoporosis in humans, enhances the study's relevance to clinical applications. The study is well-structured, with clear objectives, detailed methods, and a logical flow from introduction to conclusion. The findings are significant, demonstrating the potential of rhPTH(1-34) and dimeric R25CPTH(1-34) in enhancing bone regeneration, particularly in the context of osteoporosis.

Weaknesses: There are no major weaknesses.

Reviewer #2 (Public Review):

Summary:

This article explores the regenerative effects of recombinant PTH analogues on osteogenesis.

Strengths:

Although PTH has known to induce the activity of osteoclasts, accelerating bone resorption, paradoxically its intermittent use has become a common treat for osteoporosis. Previous studies successfully demonstrated this phenomenon in vivo, but most of them used rodent animal models, inevitably having a limitation. In this article, the authors tried to address this, using a beagle model, and assessed the osseointegrative effect of recombinant PTH analogues. As a result, the authors clearly observed the regenerative effects of PTH analogues, and compared the efficacy, using histologic, biochemical, and radiologic measurement for surgical-endocrinal combined large animal models. The data seem to be solid, and has potential clinical implications.

Weaknesses:

All the issues that I raised have been resolved in the revision process.

Overall, this paper is well-written and has clarity and consistency for a broader readership.

Reviewer #3 (Public Review):

Summary:

The work submitted by Dr. Jeong-Oh Shin and co-workers aims to investigate the therapeutic efficacy of rhPTH(1-34) and R25CPTH(1-34) on bone regeneration and osseointegration of titanium implants using a postmenopausal osteoporosis animal model.

In my opinion the findings presented are not strongly supported by the provided data since the methods utilized do not allow to significantly support the primary claims.

Strengths:

Strengths include certain good technologies utilized to perform histological sections (i.e. the EXAKT system).

Weaknesses:

Certain weaknesses significantly lower the enthusiasm for this work. Most important: the limited number of samples/group. In fact, as presented, the work has an n=4 for each treatment group. This limited number of samples/group significantly impairs the statistical power of the study. In addition, the implants were surgically inserted following a "conventional implant surgery", implying that no precise/guided insertion was utilized. This weakness is, in my opinion, particularly significant since the amount of bone osteointegration may greatly depend on the bucco-lingual positioning of each implant at the time of the surgical insertion (which should, therefore, be precisely standardized across all animals and for all surgical procedures).

Comments on current version:

As mentioned in my first review, this work is significantly underpowered for the following reasons: 1) n=4 for each treatment group.; 2) no randomization of the surgical sites receiving treatments; 3) implants surgically inserted without precision/guided surgery. The authors have not addressed these concerns.

On a minor note: not sure why the authors present a methodology to evaluate the dynamic bone formation (line 272) but do not present results (i.e. by means of histomorphometrical analyses) utilizing this methodology.

Reviewer #1 (Public Review):

This paper by Ionescu et al. applies novel brain connectivity measures based on fMRI and serotonin PET both at baseline and following ecstasy use in rats. There are multiple strengths to this manuscript. First, the use of connectivity measures using temporal correlations of 11C-DASB PET, especially when combined with resting state fMRI, is highly novel and powerful. The effects of ecstasy on molecular connectivity of the serotonin network and salience network are also quite intriguing.

I would like the authors to discuss and justify their use of high-dose (1.3%) isolfurane. A recent consensus paper on rat fMRI (Grandjean et al., "A Consensus Protocol for Functional Connectivity Analysis in the Rat Brain.") found that medetomidine combined with low dose isoflurane provided optimal control of physiology and fMRI signal. To overcome any doubts about the effects of the high-dose anaesthetic I'd encourage the authors to show the results of their functional connectivity specificity using the same or similar image processing protocol as described in that consensus paper. This is especially true since the fMRI ICs in Figure 2A appear fairly restricted.

I'd also be interested to read more about why the cerebellum was chosen as a reference region, given that serotonin is highly expressed in the cerebellum, and what effects the choice of reference region has on their quantification.

The PET ICs appear less bilateral than the fMRI ICs. Is that simply a thresholding artefact or is it a real signal?

"The data will be made available upon reasonable request" is not sufficient - please deposit the data in an open repository and link to its location.

Reviewer #2 (Public Review):

Summary:

The article aims to describe a novel methodology for the study of brain organization, in comparison to fMRI functional connectivity, under rest vs. controlled pharmacological stimulation.

Strengths:

Solid study design with pharmacological stimulation applied to assess the biological significance of functional and (novel) molecular connectivity estimates.

Provides relevant information on the multivariate organization of serotoninergic system in the brain.

Provides relevant information on the sensitivity of traditional (univariate PET analysis, fMRI functional connectivity) and novel (molecular connectivity) methods in measuring pharmacological effects on brain function.

Weaknesses:

While the study protocol is referenced in the paper, it would be useful to at least report whether the study uses bolus, constant infusion, or a combination of the two and the duration of the frames chosen for reconstruction. Minimal details on anesthesia should also be reported, clarifying whether an interaction between the pharmacological agent for anesthesia and MDMA can be expected (whole-brain or in specific regions).

Some terminology is used in a bit unclear way. E.g. "seed-based" usually refers to seed-to-voxel and not ROI-to-ROI analysis, or e.g. it is a bit confusing to have IC1 called SERT network when in fact all ICs derived from DASB data are SERT networks. Perhaps a different wording could be used (IC1 = SERT xxxxx network; IC2= SERT salience network) .

The limited sample size for the rats undergoing pharmacological stimulation which might make the study (potentially) not particularly powerful. This could not be a problem if the MDMA effect observed is particularly consistent across rats. Information on inter-individual variability of FC, MC, and BPND could be provided in this regard.

Reviewer #1 (Public Review):

Summary:

The experiment is interesting and well executed and describes in high detail fish behaviour in thermally stratified waters. The evidence is strong but the experimental design cannot distinguish between temperature and vertical position of the treatments.

Strengths:

High statistical power, solid quantification of behaviour.

Weaknesses:

A major issue with the experimental design is the vertical component of the experiment. Many thermal preference and avoidance experiments are run using horizontal division in shuttlebox systems or in annular choice flumes. These remove the vertical stratification component so that hot and cold can be compared equally, without the vertical layering as a confounding factor. The method chosen, with its vertical stratification, is inherently unable to control for this effect because warm water is always above, and cold water is always below. This complicates the interpretations and makes firm conclusions about thermal behaviour difficult.

Reviewer #2 (Public Review):

This paper investigates an interesting question: how do fish react to and avoid thermal disturbances from the optimum that occur on fast timescales? Previous work has identified potential strategies for warm avoidance in fish on short timescales while strategies for cold avoidance are far more elusive. The work combines a clever experimental paradigm with careful analysis to show that trout parr avoid cold water by limiting excursions across a warm-cold thermal interface. While I found the paper interesting and convincing overall, there are a few omissions and choices in the presentation that limit interpretability and clarity.

A main question concerns the thermal interface itself. The authors track this interface using a blue dye that is mixed in with either colder or warmer water before a gate is opened that leads to gravitational flow overlaying the two water temperatures. The dye likely allows to identify convective currents which could lead to rapid mixing of water temperatures. However, it is less clear whether it accurately reflects thermal diffusion. This is problematic as the authors identify upward turning behavior around the interface which appears to be the behavioral strategy for avoiding cold water but not warm water. Without knowing the extent of the gradient across the interface, it is hard to know what the fish are sensing. The authors appear to treat the interface as essentially static, leading them to the conclusion that turning away before the interface is reached is likely related to associative learning. However, thermal diffusion could very likely create a gradient across centimeters which is used as a cue by the fish to initiate the turn. In an ideal world, the authors would use a thermal camera to track the relationship between temperature and the dye interface. Absent that, the simulation that is mentioned in passing in the methods section should be discussed in detail in the main text, and results should be displayed in Figure 1. Error metrics on the parameters used in the simulation could then be used to identify turns in subsequent figures that likely are or aren't affected by a gradient formed across the interface.

The authors assume that the thermal interface triggers the upward-turning behavior. However, an alternative explanation, which should be discussed, is that cold water increases the tendency for upward turns. This could be an adaptive strategy since for temperatures > 4C turning swimming upwards is likely a good strategy to reach warmer water.

The paper currently also suffers from a lack of clarity which is largely created by figure organization. Four main and 38 supplemental figures are very unusual. I give some specific recommendations below but the authors should decide which data is truly supplemental, versus supporting important points made in the paper itself. There also appear to be supplemental figures that are never referenced in the text which makes traversing the supplements unnecessarily tedious.<br /> The N that was used as the basis for statistical tests and plots should be identified in the figures to improve interpretability. To improve rigor, the experimental procedures should be expanded. Specifically, the paper uses two thermal models which are not detailed at all in the methods section.

Reviewer #3 (Public Review):

In this study, the authors measured the behavioural responses of brown trout to the sudden availability of a choice between thermal environments. The data clearly show that these fish avoid colder temperatures than the acclimation condition, but generally have no preference between the acclimation condition or warmer water (though I think the speculation that the fish are slowly warming up is interesting). Further, the evidence is compelling that avoidance of cold water is a combination of thermotaxis and thermokinesis. This is a clever experimental approach and the results are novel, interesting, and have clear biological implications as the authors discuss. I also commend the team for an extremely robust, transparent, and clear explanation of the experimental design and analytical decisions. The supplemental material is very helpful for understanding many of the methodological nuances, though I admit that I found it overwhelming at times and wonder if it could be pruned slightly to increase readability. Overall, I think the conclusions are generally well-supported by the data, and I have no major concerns.

Reviewer #1 (Public Review):

Allodynia is commonly measured in the pain field using von Frey filaments, which are applied to a body region (usually hindpaw if studying rodents) by a human. While humans perceive themselves as being objective, as the authors noted, humans are far from consistent when applying these filaments. Not to mention, odors from humans, including those of different sexes, can influence animal behavior. There is thus a major unmet need for a way to automate this tedious von Frey testing process and to remove humans from the experiment. I have no major scientific concerns with the study, as the authors did an outstanding job of comparing this automated system to human experimenters in a rigorous and quantitative manner. They even demonstrated that their automated system can be used in conjunction with in vivo imaging techniques.

While it is somewhat unclear how easy and inexpensive this device will be, I anticipate everyone in the pain field will be clamoring to get their hands on a system like this. And given the mechanical nature of the device and the propensity for mice to urinate on things, I also wonder how frequently the device breaks/needs to be repaired. Perhaps some details regarding the cost and reliability of the device would be helpful to include, as these are the two things that could make researchers hesitant to adopt immediately.

The only major technical concern, which is easy to address, is whether the device generates ultrasonic sounds that rodents can hear when idle or operational, across the ultrasonic frequencies that are of biological relevance (20-110 kHz). These sounds are generally alarm vocalizations and can create stress in animals, and/or serve as cues of an impending stimulus (if indeed they are produced by the device).

Reviewer #2 (Public Review):

Summary:

Burdge, Juhmka, et al describe the development and validation of a new automated system for applying plantar stimuli in rodent somatosensory behavior tasks. This platform allows the users to run behavior experiments remotely, removing experimenter effects on animals and reducing variability in the manual application of stimuli. The system integrates well with other automated analysis programs that the lab has developed, providing a complete package for standardizing behavior data collection and analysis. The authors present extensive validations of the system against manual stimulus application. Some proof of concept studies also show how the system can be used to better understand the effect of experimenters on behavior and the effects of how stimuli are presented on the micro features of the animal withdrawal response.

Strengths:

If widely adopted, ARM has the potential to reduce variability in plantar behavior studies across and within labs and provide a means to standardize results. The system is well-validated and results clearly and convincingly presented. Most claims are well supported by experimental evidence.

Weaknesses:

ARM seems like a fantastic system that could be widely adopted, but no details are given on how a lab could build ARM, thus its usefulness is limited.

The ARM system appears to stop short of hitting the desired forces that von Frey filaments are calibrated toward (Figure 2). This may affect the interpretation of results.

The authors mention that ARM generates minimal noise; however, if those sounds are paired with stimulus presentation they could still prompt a withdrawal response. Including some 'catch' trials in an experiment could test for this.

The experimental design in Figure 2 is unclear- did each experimenter have their own cohort of 10 mice, or was a single cohort of mice shared? If shared, there's some concern about repeat testing.

Reviewer #3 (Public Review):

Summary:

This report describes the development and initial applications of the ARM (Automated Reproducible Mechano-stimulator), a programmable tool that delivers various mechanical stimuli to a select target (most frequently, a rodent hindpaw). Comparisons to traditional testing methods (e.g., experimenter application of stimuli) reveal that the ARM reduces variability in the anatomical targeting, height, velocity, and total time of stimulus application. Given that the ARM can be controlled remotely, this device was also used to assess the effect of the experimenter's presence on reflexive responses to mechanical stimulation. Lastly, the ARM was used to stimulate rodent hind paws while measuring neuronal activity in the basolateral nucleus of the amygdala (BLA), a brain region that is associated with the negative effect of pain. This device, and similar automated devices, will undoubtedly reduce experimenter-related variability in reflexive mechanical behavior tests; this may increase experimental reproducibility between laboratories.

Strengths:

Clear examples of variability in experimenter stimulus application are provided and then contrasted with uniform stimulus application that is inherent to the ARM.

Weaknesses:

Limited details are provided for statistical tests and inappropriate claims are cited for individual tests. For example, in Figure 2, differences between researchers at specific forces are reported to be supported by a 2-way ANOVA; these differences should be derived from a post-hoc test that was completed only if the independent variable effects (or interaction effect) were found to be significant in the 2-way ANOVA. In other instances, statistical test details are not provided at all (e.g., Figures 3B, 3C, Figure 4, Figure 6G).

One of the arguments for using the ARM is that it will minimize the effect that the experimenter's presence may have on animal behavior. In the current manuscript, the effects of the experimenter's presence on both habituation time and aspects of the withdrawal reflex are minimal for Researcher 2 and non-existent for Research 1. This is surprising given that Researcher 2 is female; the effect of experimenter presence was previously documented for male experiments as the authors appropriately point out (Sorge et al. PMID: 24776635). In general, this argument could be strengthened (or perhaps negated) if more than N=2 experiments were included in this assessment.

The in vivo BLA calcium imaging data feel out of place in this manuscript. Is the point of Figure 6 to illustrate how the ARM can be coupled to Inscopix (or other external inputs) software? If yes, the following should be addressed: why do the up-regulated and down-regulated cell activities start increasing/decreasing before the "event" (i.e., stimulus application) in Figure 6F? Why are the paw withdrawal latencies and paw distanced travelled values in Figures 6I and 6J respectively so much faster/shorter than those illustrated in Figure 5 where the same approach was used?

Another advance of this manuscript is the integration of a 500 fps camera (as opposed to a 2000 fps camera) in the PAWS platform. To convince readers that the use of this more accessible camera yields similar data, a comparison of the results for cotton swabs and pinprick should be completed between the 500 fps and 2000 fps cameras. In other words, repeat Supplementary Figure 3 with the 2000 fps camera and compare those results to the data currently illustrated in this figure.

Reviewer #1 (Public Review):

Summary:

The authors set out to evaluate the regulation of interferon (IFN) gene expression in fish, using mainly zebrafish as a model system. Similar to more widely characterized mammalian systems, fish IFN is induced during viral infection through the action of the transcription factor IRF3 which is activated by phosphorylation by the kinase TBK1. It has been previously shown in many systems that TBK1 is subjected to both positive and negative regulation to control IFN production. In this work, the authors find that the cell cycle kinase CDK2 functions as a TBK1 inhibitor by decreasing its abundance through the recruitment of the ubiquitinylation ligase, Dtx4, which has been similarly implicated in the regulation of mammalian TBK1. Experimental data are presented showing that CDK2 interacts with both TBK1 and Dtx4, leading to TBK1 K48 ubiquitinylation on K567 and its subsequent degradation by the proteasome.

Strengths:

The strengths of this manuscript are its novel demonstration of the involvement of CDK2 in a process in fish that is controlled by different factors in other vertebrates and its clear and supportive experimental data.

Weaknesses:

The weaknesses of the study include the following. 1) It remains unclear whether the function described for CDK2 is regulatory, that is, it affects TBK1 levels during physiological responses such as viral infection or cell cycle progression, or if it is homeostatic, governing the basal abundance of TBK1 but not responding to signaling. 2) The authors have not explored whether the catalytic activity of CDK2 is required for TBK1 ubiquitinylation and, if so, what its target specificity is. 3) Given the multitude of CDK isoforms in fish, it remains unexplored whether the identified fish CDK2 homolog is a requisite cell cycle regulator or if its action in the cell cycle is redundant with other CDKs.

Reviewer #2 (Public Review):

Summary:

In this paper, the authors describe a novel function involving the cell cycle protein kinase CDK2, which binds to TBK1 (an essential component of the innate immune response) leading to its degradation in a ubiquitin/proteasome-dependent manner. Moreover, the E3 ubiquitin ligase, Dtx4, is implicated in the process by which CDK2 increases the K48-linked ubiquitination of TBK1. This paper presents intriguing findings on the function of CDK2 in lower vertebrates, particularly its regulation of IFN expression and antiviral immunity.

Strengths:

(1) The research employs a variety of experimental approaches to address a single question. The data are largely convincing and appear to be well executed.

(2) The evidence is strong and includes a combination of in vivo and in vitro experiments, including knockout models, protein interaction studies, and ubiquitination analyses.

(3) This study significantly impacts the field of immunology and virology, particularly concerning the antiviral mechanisms in lower vertebrates. The findings provide new insights into the regulation of IFN expression and the broader role of CDK2 in immune responses. The methods and data presented in this paper are highly valuable for the scientific community, offering new avenues for research into antiviral strategies and the development of therapeutic interventions targeting CDK2 and its associated pathways.

Weaknesses:

(1) While the study focuses on fish, the broader implications for other lower vertebrates and higher vertebrates are not extensively discussed.

(2) The study heavily relies on specific fish models, which may limit the generalizability of the findings across different species.

Reviewer #1 (Public Review):

Faiz et al. investigate small molecule-driven direct lineage reprogramming of mouse postnatal mouse astrocytes to oligodendrocyte lineage cells (OLCs). They use a combination of in vitro, in vivo, and computational approaches to confirm lineage conversion and to examine the key underlying transcription factors and signaling pathways. Lentiviral delivery of transcription factors previously reported to be essential in OLC fate determination-Sox10, Olig2, and Nkx2.2-to astrocytes allows for lineage tracing. They found that these transcription factors are sufficient in reprogramming astrocytes to iOLCs, but that the OLCs range in maturity level depending on which factor they are transfected with. They followed up with scRNA-seq analysis of transfected and control cultures 14DPT, confirming that TF-induced astrocytes take on canonical OLC gene signatures. By performing astrocyte lineage fate mapping, they further confirmed that TF-induced astrocytes give rise to iOLCs. Finally, they examined the distinct genetic drivers of this fate conversion using scRNA-seq and deep learning models of Sox10- astrocytes at multiple time points throughout the reprogramming. These findings are certainly relevant to diseases characterized by the perturbation of OLC maturation and/or myelination, such as Multiple Sclerosis and Alzheimer's Disease. Their application of such a wide array of experimental approaches gives more weight to their findings and allows for the identification of additional genetic drivers of astrocyte to iOLC conversion that could be explored in future studies. Overall, I find this manuscript thoughtfully constructed and only have a few questions to be addressed.

(1) The authors suggest that Sox10- and Olig2- transduced astrocytes result in distinct subpopulations iOLCs. Considering it was discussed in the introduction that these TFs cyclically regulate one another throughout differentiation, could they speculate as to why such varying iOLCs resulted from the induction of these two TFs?

(2) In Figure 1B it appears that the Sox10- MBP+ tdTomato+ cells decreases from D12 to D14. Does this make sense considering MBP is a marker of more mature OLCs?

(3) Previous studies have shown that MBP expression and myelination in vitro occurs at the earliest around 4-6 weeks of culturing. When assessing whether further maturation would increase MBP positivity, authors only cultured cells up to 22 DPT and saw no significant increase. Has a lengthier culture timeline been attempted?

(4) Figure S4D is described as "examples of tdTomatonegzsGreen+OLCmarker+ cells that arose from a tdTomatoneg cell with an astrocyte morphology." The zsGreen+ tdTomato- cell is not convincingly of "astrocyte morphology"; it could be a bipolar OLC. To strengthen the conclusions and remove this subjectivity, more extensive characterizations of astrocyte versus OLC morphology in the introduction or results are warranted. This would make this observation more convincing since there is clearly an overlap in the characteristics of these cell types.

Reviewer #2 (Public Review):

The study by Bajohr investigates the important question of whether astrocytes can generate oligodendrocytes by direct lineage conversion (DLR). The authors ectopically express three transcription factors - Sox10, Olig2 and Nkx6.2 - in cultured postnatal mouse astrocytes and use a combination of Aldh1|1-astrocyte fate mapping and live cell imaging to demonstrate that Sox10 converts astrocytes to MBP+ oligodendrocytes, whereas Olig2 expression converts astrocytes to PDFRalpha+ oligodendrocyte progenitor cells. Nkx6.2 does not induce lineage conversion. The authors use single-cell RNAseq over 14 days post-transduction to uncover molecular signatures of newly generated iOLs.

The potential to convert astrocytes to oligodendrocytes has been previously analyzed and demonstrated. Despite the extensive molecular characterization of the direct astrocyte-oligodendrocyte lineage conversion, the paper by Bajohr et al. does not represent significant progress. The entire study is performed in cultured cells, and it is not demonstrated whether this lineage conversion can be induced in astrocytes in vivo, particularly at which developmental stage (postnatal, adult?) and in which brain region. The authors also state that generating oligodendrocytes from astrocytes could be relevant for oligodendrocyte regeneration and myelin repair, but they don't demonstrate that lineage conversion can be induced under pathological conditions, particularly after white matter demyelination. Specific issues are outlined below.

(1) The authors perform an extensive characterization of Sox10-mediated DLR by scRNAseq and demonstrate a clear trajectory of lineage conversion from astrocytes to terminally differentiated MBP+ iOLCs. A similar type of analysis should be performed after Olig2 transduction, to determine whether transcriptomics of OPC induction overlaps with any phase of MBP+ oligodendrocyte induction.

(2) A complete immunohistochemical characterization of the cultures should be performed at different time points after Sox10 and Olig2 transduction to confirm OL lineage cell phenotypes.

Joint Public Review:

The manuscript "Engineering of PAClight1P78A: A High-Performance Class-B1 GPCR-Based Sensor for PACAP1-38" by Cola et al. presents the development of a novel genetically encoded sensor, PAClight1P78A, based on the human PAC1 receptor. The authors provide a thorough in vitro and in vivo characterization of this sensor, demonstrating its potential utility across various applications in life sciences, including drug development and basic research.

The main criticism of this manuscript after initial review is that the PACLight1 sensor has not been shown to detect the release of endogenous PACAP, whether in culture, in vivo, or ex vivo. The authors appear to be cognizant of this significant limitation (for a PACAP sensor) but no significant changes to address this limitation are provided in the revision.

While the sensor that is described here is new and the experimental results support the conclusions, the sensor reported here is not suited for the detection of endogenous PACAP release in vivo. In some respects, this manuscript could be seen as a stepping stone for further development either by the authors or other groups. Indeed, in many cases initial versions of genetically encoded sensors undergo substantial development post-publication, as exemplified by the evolution of GCaMP. However, the situation with the PAClight sensor reported here requires a different approach. Unlike GCaMP, which was one of the first genetically encoded calcium indicators, PAClight is another variant in a series of GPCR-fluorophore conjugates, following methodologies similar to those developed in the Lin Tian lab and the multiple GRAB-based sensors from Yulong Li's lab. These sensors have already demonstrated in vivo applicability, setting a standard that PAClight must meet or exceed to confirm its value and novelty.

Given that the title of the manuscript, "Probing PAC1 receptor activation across species with an engineered sensor," implies broader applicability, it potentially misleads readers about the sensor's utility in vivo, where "in vivo" should be understood as referring to the detection of endogenous PACAP release.

To align the manuscript with the expectations set by its title, it is crucial that the authors either provide substantial in vivo validation (ability to detect endogenous release of PACAP) or revise the title and the text to clarify that the sensor is primarily intended to detect exogenously applied PACAP. This clarification will ensure that the manuscript accurately reflects the sensor's current capabilities and scope of use.

Reviewer #1 (Public Review):

Summary:

Non-B DNA structures such as G4s and R-loops have the potential to impact genome stability, gene transcription, and cell differentiation. This study investigates the distribution of G4s and R-loops in human and mouse cells using some interesting technical modifications of existing Tn5-based approaches. This work confirms that the helicase DHX9 could regulate the formation and/or stability of both structures in mouse embryonic stem cells (mESCs). It also provides evidence that the lack of DHX9 in mESCs interferes with their ability to differentiate.

Strengths:

HepG4-seq, the new antibody-free strategy to map G4s based on the ability of Hemin to act as a peroxidase when complexed to G4s, is interesting. This study also provides more evidence that the distribution pattern of G4s and R-loops might vary substantially from one cell type to another.

Weaknesses:

This study is essentially descriptive and does not provide conclusive evidence that lack of DHX9 does interfere with the ability of mESCs to differentiate by regulating directly the stability of either G4 or R-loops. In the end, it does not substantially improve our understanding of DHX9's mode of action.

There is no in-depth comparison of the newly generated data with existing datasets and no rigorous control was presented to test the specificity of the hemin-G4 interaction (a lot of the hemin-dependent signal seems to occur in the cytoplasm, which is unexpected).

The authors talk about co-occurrence between G4 and R-loops but their data does not actually demonstrate co-occurrence in time. If the same loci could form alternatively either R-loops or G4 and if DHX9 was somehow involved in determining the balance between G4s and R-loops, the authors would probably obtain the same distribution pattern. To manipulate R-loop levels in vivo and test how this affects HEPG4-seq signals would have been helpful.

This study relies exclusively on Tn5-based mapping strategies. This is a problem as global changes in DNA accessibility might strongly skew the results. It is unclear at this stage whether the lack of DHX9, BLM, or WRN has an impact on DNA accessibility, which might underlie the differences that were observed. Moreover, Tn5 cleaves DNA at a nearby accessible site, which might be at an unknown distance away from the site of interest. The spatial accuracy of Tn5-based methods is therefore debatable, which is a problem when trying to demonstrate spatial co-occurrence. Alternative mapping methods would have been helpful.

Reviewer #2 (Public Review):

Summary:

In this study, Liu et al. explore the interplay between G-quadruplexes (G4s) and R-loops. The authors developed novel techniques, HepG4-seq and HBD-seq, to capture and map these nucleic acid structures genome-wide in human HEK293 cells and mouse embryonic stem cells (mESCs). They identified dynamic, cell-type-specific distributions of co-localized G4s and R-loops, which predominantly localize at active promoters and enhancers of transcriptionally active genes. Furthermore, they assessed the role of helicase Dhx9 in regulating these structures and their impact on gene expression and cellular functions.

The manuscript provides a detailed catalogue of the genome-wide distribution of G4s and R-loops. However, the conceptual advance and the physiological relevance of the findings are not obvious. Overall, the impact of the work on the field is limited to the utility of the presented methods and datasets.

Strengths:

(1) The development and optimization of HepG4-seq and HBD-seq offer novel methods to map native G4s and R-loops.

(2) The study provides extensive data on the distribution of G4s and R-loops, highlighting their co-localization in human and mouse cells.

(3) The study consolidates the role of Dhx9 in modulating these structures and explores its impact on mESC self-renewal and differentiation.

Weaknesses:

(1) The specificity of the biotinylation process and potential off-target effects are not addressed. The authors should provide more data to validate the specificity of the G4-hemin.

(2) Other methods exploring a catalytic dead RNAseH or the HBD to pull down R-loops have been described before. The superior quality of the presented methods in comparison to existing ones is not established. A clear comparison with other methods (BG4 CUT&Tag-seq, DRIP-seq, R-CHIP, etc) should be provided.

(3) Although the study demonstrates Dhx9's role in regulating co-localized G4s and R-loops, additional functional experiments (e.g., rescue experiments) are needed to confirm these findings.

(4) The manuscript would benefit from a more detailed discussion of the broader implications of co-localized G4s and R-loops.

(5) The manuscript lacks appropriate statistical analyses to support the major conclusions.

(6) The discussion could be expanded to address potential limitations and alternative explanations for the results.

Reviewer #3 (Public Review):

Summary:

The authors developed and optimized the methods for detecting G4s and R-loops independent of BG4 and S9.6 antibody, and mapped genomic native G4s and R-loops by HepG4-seq and HBD-seq, revealing that co-localized G4s and R-loops participate in regulating transcription and affecting the self-renewal and differentiation capabilities of mESCs.

Strengths:

By utilizing the peroxidase activity of G4-hemin complex and combining proximity labeling technology, the authors developed HepG4-seq (high throughput sequencing of hemin-induced proximal labelled G4s) , which can detect the dynamics of G4s in vivo. Meanwhile, the "GST-His6-2xHBD"-mediated CUT&Tag protocol (Wang et al., 2021) was optimized by replacing fusion protein and tag, the optimized HBD-seq avoids the generation of GST fusion protein aggregates and can reflect the genome-wide distribution of R-loops in vivo.

The authors employed HepG4-seq and HBD-seq to establish comprehensive maps of native co-localized G4s and R-loops in human HEK293 cells and mouse embryonic stem cells (mESCs). The data indicate that co-localized G4s and R-loops are dynamically altered in a cell type-dependent manner and are largely localized at active promoters and enhancers of transcriptionally active genes.

Combined with Dhx9 ChIP-seq and co-localized G4s and R-loops data in wild-type and dhx9KO mESCs, the authors confirm that the helicase Dhx9 is a direct and major regulator that regulates the formation and resolution of co-localized G4s and R-loops.

Depletion of Dhx9 impaired the self-renewal and differentiation capacities of mESCs by altering the transcription of co-localized G4s and R-loops-associated genes.

In conclusion, the authors provide an approach to studying the interplay between G4s and R-loops, shedding light on the important roles of co-localized G4s and R-loops in development and disease by regulating the transcription of related genes.

Weaknesses:

As we know, there are at least two structure data of S9.6 antibody very recently, and the questions about the specificity of the S9.6 antibody on RNA:DNA hybrids should be finished. The authors referred to (Hartono et al., 2018; Konig et al., 2017; Phillips et al., 2013) need to be updated, and the authors' bias against S9.6 antibodies needs also to be changed. However, as the authors had questioned the specificity of the S9.6 antibody, they should compare it in parallel with the data they have and the data generated by the widely used S9.6 antibody.

Although HepG4-seq is an effective G4s detection technique, and the authors have also verified its reliability to some extent, given the strong link between ROS homeostasis and G4s formation, and hemin's affinity for different types of G4s, whether HepG4-seq reflects the dynamics of G4s in vivo more accurately than existing detection techniques still needs to be more carefully corroborated.

Reviewer #1 (Public Review):

Summary:

Medina et al, 2023 investigated the peripheral blood transcriptional responses in patients with diversifying disease outcomes. The authors characterized the blood transcriptome of four non-hospitalized individuals presenting mild disease and four patients hospitalized with severe disease. These individuals were observed longitudinally at three timepoints (0-, 7-, and 28-days post recruitment), and distinct transcriptional responses were observed between severe hospitalized patients and mild non-hospitalized individuals, especially during 0- and 7-day collection timepoints. Particularly, the authors found that increased expression of genes associated with NK cell cytotoxicity is associated with mild outcomes. Additional co-regulated gene network analyses positively correlates T cell activity with mild disease and neutrophil degranulation with severe disease.

Strengths:

The longitudinal measurements in individual participants at consistent collection intervals can offer an added dimension to the dataset that involves temporal trajectories of genes associated with disease outcomes and is a key strength of the study. The use of co-expressed gene networks specific to the cohort to complement enrichment results obtained from pre-determined gene sets can offer valuable insights into new associations/networks associated with disease progression and warrants further analyses on the biological functions enriched within these co-expressed network modules.

Weaknesses:

There is a large difference in the infection timeline (onset of symptom to recruitment) between mild and severe patient cohort. As immune responses during early infection can be highly dynamic, the differences in infection timeline may bias transcriptional signatures observed between the groups. The study is also limited by a small cohort size.

Comments on revised version:

The authors have addressed the specific concerns brought forth by the reviewers.

Reviewer #2 (Public Review):

In their manuscript, Medina and colleagues investigate transcriptional differences between mild and severe SARS-CoV-2 infections. Their analyses are very comprehensive incorporating a multitude of bioinformatics tools ranging from PCA plots, GSEA and DEG analysis, protein-protein interaction network, and weighted correlation network analyses. They conclude that in mild COVID-19 infection NK cell functionality is compromised and this is connected to cytokine interactions and Th1/Th2 cell differentiation pathways cross-talk, bridging the innate and the adaptive arms of the immune system. The authors successfully recruited participants with both mild and severe COVID-19 between November 2020 to May 2021. The analyzed cohort is gender and acceptably age-matched and the results reported are promising. Signatures associated with NK cell cytotoxicity in mild and neutrophil functions in the severe group during acute infection are the chief findings reported in this manuscript.

Comments on revised version:

The authors responded appropriately to the previous review critiques.

Reviewer #3 (Public Review):

Summary:

The authors discovered that the RdnE effector possesses DNase activity, and in competition, P. mirabilis having RdnE outcompetes the null strain. Additionally, they presented evidence that the RdnI immunity protein binds to RdnE, suppressing its toxicity. Interestingly, the authors demonstrated that the RdnI homolog from a different phylum (i.e., Actinomycetota) provides cross-species protection against RdnE injected from P. mirabilis, despite the limited identity between the immunity sequences. Finally, using metagenomic data from human-associated microbiomes, the authors provided bioinformatic evidence that the rdnE/rdnI gene pair is widespread and present in individual microbiomes. Overall, the discovery of broad protection by non-cognate immunity is intriguing, although not necessarily surprising in retrospect, considering the prolonged period during which Earth was a microbial battlefield/paradise.

Strengths:

The authors presented a strong rationale in the manuscript and characterized the molecular mechanism of the RdnE effector both in vitro and in the heterologous expression model. The utilization of the bacterial two-hybrid system, along with the competition assays, to study the protective action of RdnI immunity is informative. Furthermore, the authors conducted bioinformatic analyses throughout the manuscript, examining the primary sequence, predicted structural, and metagenomic levels, which significantly underscore the significance and importance of the EI pair.

Weaknesses:

(1) The interaction between RdnI and RdnE appears to be complex and requires further investigation. The manuscript's data does not conclusively explain how RdnI provides a "promiscuous" immunity function, particularly regarding the RdnI mutant/chimera derivatives. The lack of protection observed in these cases might be attributed to other factors, such as a decrease in protein expression levels or misfolding of the proteins. Additionally, the transient nature of the binding interaction could be insufficient to offer effective defenses.<br /> (2) The results from the mixed population competition would benefit from quantitative analysis. The swarm competition assays only yield binary outcomes (Yes or No), limiting the ability to obtain more detailed insights from the data.<br /> (3) The discovery of cross-species protection is solely evident in the heterologous expression-competition model. It remains uncertain whether this is an isolated occurrence or a common characteristic of RdnI immunity proteins across various scenarios. Further investigations are necessary to determine the generality of this behavior.

Reviewer #4 (Public Review):

Summary:

Knecht et al. elucidate a Type VI Secretion System (T6SS) effector-immunity pair in Proteus mirabilis. They demonstrate that the effector protein RdnE exhibits DNase activity in vitro and induces toxicity when ectopically expressed in cells, the latter being neutralized by the cognate immunity protein RdnI. The authors identify major regions within RdnI necessary for the interaction and neutralization of RdnE. Notably, they report cross-talk where both cognate and non-cognate RdnI proteins can neutralize RdnE, mitigating its fitness advantage in bacterial co-swarm assays. A comprehensive metagenomic analysis revealed an abundance of rdnI over rdnE genes in most gut samples, suggesting a potential role of rdnI in providing a fitness advantage against bacteria encoding for RdnE effector.

Strengths:

The authors successfully combined biochemical and microbiological experiments with bioinformatics analysis to advance the understanding of the T6SS-mediated population dynamics in bacteria. The co-swarm functional assay is of particular interest as it demonstrates how bacterial strains carrying only rdnI immunity genes could potentially compete in the same niche with other species armed with toxic rdnE effector genes. The manuscript is well-written, and the figures are self-explanatory.

Weaknesses:

(1) How would the authors explain the discrepancy observed in Figure 4 G and Figure 4 S3 B where two RdnI proteins from Prevotella and Pseudomonas genera do not bind to RdnE_Proteus in BACTH, whereas they co-elute with a RdnE_Proteus-FLAG with efficiency comparable to the cross-neutralizing RdnI_Rothia? Similarly, the interaction results obtained in BACTH with RdnI truncate (Figure 4E) or chimeric RdnI (Figure 4I, lane 4) could be a result of an overexpressed T18-fusion variant.<br /> Alternative in vitro protein binding assay would be beneficial.

(2) Based on the bioinformatic analysis the Rothia and Prevotella species harboring rdnE/I genes co-occurred in 5% of metagenomes tested, suggesting that these bacteria could come into contact. The manuscript would benefit greatly if authors demonstrated that RdnI proteins from Rothia or Prevotella could cross-neutralize its own and its 'neighbor' RdnE effectors, for example in an E. coli viability assay. The cross-neutralizing co-swarming results (Figure 4F) could also be further validated in viability assay as shown in Figure 2 S1.

(3) Little is known about whether RdnE is delivered via T6SS as a full-length protein or as the shorter C-terminal fragment. There is a possibility that immunity proteins could recognize RdnE regions beyond the C-terminal 138 amino acids that authors used in their in vitro assays.

Reviewer #5 (Public Review):

This work investigates a T6SS effector-immunity pair from Proteus mirabilis. The authors make several interesting claims, particularly regarding the mechanism of effector inhibition by the immunity protein. However, it appears that these claims are not fully supported by the evidence provided.

I have read the revised manuscript, the public reviews, and the authors' updated responses to these reviews. In my opinion, the concerns raised by the reviewers remain relevant even after the authors' revisions. Since previous reviews have excellently described the strengths and weaknesses of this work, I will focus on my major concerns:

(1) The authors describe RdnE-RdnI, a T6SS effector-immunity pair from Proteus mirabilis. RdnE is actually the C-terminal domain of IdrD, a 1581-amino-acid protein containing PAAR and RHS domains. This work does not provide evidence for T6SS-dependent secretion of the effector, instead supplying references to previous works.

(2) While the authors claim the function of the RdnE domain is unknown, it was previously shown to be evolutionarily related to PoNe and TseV, both of which are known DNA nucleases. Although the authors cite the relevant references, they do not clearly disclose this information.

(3) The authors claim that RdnE contains two different domains: the first is the PD-(D/E)XK domain, and the second, referred to as "region 2," follows it. Unfortunately, no structural evidence is provided to support this claim, not even a predicted model demonstrating that these are indeed separate domains.

(4) One of the major claims made in this work is that RdnI binding to RdnE is not sufficient for RdnE inhibition, suggesting a more sophisticated mechanism. The authors base this theory on differences between the ability of RdnI to bind RdnE (shown using bacterial two-hybrid assays) and the ability to protect against RdnE toxicity in swarm competition assays. Specifically, they show that the first 85 amino acids of RdnI bind to the short RdnE domain in the bacterial two-hybrid assay but do not protect against the full-length effector in the swarm competition assay. They also demonstrate that performing seven mutations in conserved residues in RdnE or replacing parts of RdnI with parts from other RdnI homologs leads to the same phenomenon.

While these findings are interesting and even intriguing, in my opinion, the current evidence does not support their theory. A simple explanation for the differences between the assays is that while the N-terminal domain of RdnI is sufficient for binding to RdnE, inhibition of the active site of RdnE requires binding of a second domain to RdnE. In that sense, it should be noted that while the authors use co-IP assays to show the interaction between RdnE and full-length RdnI, they do not use it to show the interaction between RdnE and the first 85 amino acids of RdnI.

(5) The authors claim that a "conserved motif" within RdnI plays a role in the inhibition of RdnE. To investigate this, they replace this motif with sequences from several RdnI homologs, demonstrating that in one case, it is possible to exchange these conserved motifs between RdnI homologs that inhibit Proteus RdnE. However, they also show that even if the conserved motif is taken from an RdnI homolog that cannot inhibit Proteus RdnE, the hybrid protein can still protect cells in a swarm competition assay. This result raises concerns regarding the relevance of this conserved motif.

(6) Lastly, regarding the theory that immunity proteins can protect against non-cognate effectors, it appears that the authors based their theory on a single case where RdnI from Rothia protected against RdnE from Proteus. In my opinion, a more thorough investigation, involving testing many homologs, is needed to substantiate this theory.

Public Review:

The authors used an innovative technic to study the visual vigilance based on high-acuity vision, the fovea. Combining motion-capture features and visual space around the head, the authors were able to estimate the visual fixation of free-feeding pigeon at any moment. Simulating predator attacks on screens, they showed that 1) pigeons used their fovea to inspect predators cues, 2) the behavioural state (feeding or head-up) influenced the latency to use the fovea and 3) the use of the fovea decrease the latency to escape of both the individual that foveate the predators cues but also the other flock members.

The paper is very interesting, and combines innovative technic well adapted to study the importance of high-acuity vision for spotting a predator, but also of improving the behavioural response (escaping). The results are strong and the models used are well-adapted. This paper is a major contribution to our understanding of the use of visual adaptation in a foraging context when at risk. This is also a major contribution to the understanding of individual interaction in a flock.

Reviewer #1 (Public Review):

Summary:

In this preprint, the authors systematically and rigorously investigate how specific classes of residue mutations alter the critical temperature as a proxy for the driving forces for phase separation. The work is well executed, the manuscript well-written, and the results reasonable and insightful.

Strengths:

The introductory material does an excellent job of being precise in language and ideas while summarizing the state of the art. The simulation design, execution, and analysis are exceptional and set the standard for these types of large-scale simulation studies. The results, interpretations, and Discussion are largely nuanced, clear, and well-motivated.

Weaknesses:

This is not exactly a weakness, but I think it would future-proof the authors' conclusions to clarify a few key caveats associated with this work. Most notably, given the underlying implementation of the Mpipi model, temperature dependencies for intermolecular interactions driven by solvent effects (e.g., hydrophobic effect and charge-mediated interactions facilitated by desolvation penalties) are not captured. This itself is not a "weakness" per se, but it means I would imagine CERTAIN types of features would not be well-captured; notably, my expectation is that at higher temperatures, proline-rich sequences drive intermolecular interactions, but at lower temperatures, they do not. This is likely also true for the aliphatic residues, although these are found less frequently in IDRs. As such, it may be worth the authors explicitly discussing.

Similarly, prior work has established the importance of an alpha-helical region in TDP-43, as well as the role of aliphatic residues in driving TDP-43's assembly (see Schmidt et al 2019). I recognize the authors have focussed here on a specific set of mutations, so it may be worth (in the Discussion) mentioning [1] what impact, if any, they expect transient or persistent secondary structure to have on their conclusions and [2] how they expect aliphatic residues to contribute. These can and probably should be speculative as opposed to definitive.

Again - these are not raised as weaknesses in terms of this work, but the fact they are not discussed is a minor weakness, and the preprint's use and impact would be improved on such a discussion.

Reviewer #2 (Public Review):

This is an interesting manuscript where a CA-only CG model (Mpipi) was used to examine the critical temperature (Tc) of phase separation of a set of 140 variants of prion-like low complexity domains (PLDs). The key result is that Tc of these PLDs seems to have a linear dependence on substitutions of various sticker and space residues. This is potentially useful for estimating the Tc shift when making novel mutations of a PLD. However, I have strong reservations about the significance of this observation as well as some aspects of the technical detail and writing of the manuscript.

(1) Writing of the manuscript: The manuscript can be significantly shortened with more concise discussions. The current text reads as very wordy in places. It even appears that the authors may be trying a bit too hard to make a big deal out of the observed linear dependence.

The manuscript needs to be toned done to minimize self-promotion throughout the text. Some of the glaring examples include the wording "unprecedented", "our research marks a significant milestone in the field of computational studies of protein phase behavior ..", "Our work explores a new framework to describe, quantitatively, the phase behavior ...", and others.

There is really little need to emphasize the need to manage a large number of simulations for all 140 variants. Yes, some thoughts need to go into designing and managing the jobs and organizing the data, but it is pretty standard in computational studies. For example, large-scale protein ligand-free energy calculations can require one to a few orders of magnitude larger number of runs, and it is pretty routine.

When discussing the agreement with experimental results on Tm, it should be noted that the values of R > 0.93 and RMSD < 14 K are based on only 16 data points. I am not sure that one should refer to this as "extended validation". It is more like a limited validation given the small data size.

Results of linear fitting shown in Eq 4-12 should be summarized in a single table instead of scattering across multiple pages.

The title may also be toned down a bit given the limited significance of the observed linear dependence.

(2) Significance and reliability of Tc: Given the simplicity of Mpipi (a CA-only model that can only describe polymer chain dimension) and the low complexity nature of PLDs, the sequence composition itself is expected to be the key determinant of Tc. This is also reflected in various mean-field theories. It is well known that other factors will contribute, such as patterning (examined in this work as well), residual structures, and conformational preferences in dilute and dense phases. The observed roughly linear dependence is a nice confirmation but really unsurprising by itself. It appears how many of the constructs deviate from the expected linear dependence (e.g., Figure 4A) may be more interesting to explore.

The assumption that all systems investigated here belong to the same universality class as a 3D Ising model and the use of Eqn 20 and 21 to derive Tc is poorly justified. Several papers have discussed this issue, e.g., see Pappu Chem Rev 2023 and others. Muthukumar and coworkers further showed that the scaling of the relevant order parameters, including the conserved order parameter, does not follow the 3D Ising model. More appropriate theoretical models including various mean field theories can be used to derive binodal from their data, such as using Rohit Pappu's FIREBALL toolset. Imposing the physics of the 3D Ising model as done in the current work creates challenges for equivalence relationships that are likely unjustified.

While it has been a common practice to extract Tc when fitting the coexistence densities, it is not a parameter that is directly relevant physiologically. Instead, Csat would be much more relevant to think about if phase separation could occur in cells.

Reviewer #3 (Public Review):

Summary:

"Decoding Phase Separation of Prion-Like Domains through Data-Driven Scaling Laws" by Maristany et al. offers a significant contribution to the understanding of phase separation in prion-like domains (PLDs). The study investigates the phase separation behavior of PLDs, which are intrinsically disordered regions within proteins that have a propensity to undergo liquid-liquid phase separation (LLPS). This phenomenon is crucial in forming biomolecular condensates, which play essential roles in cellular organization and function. The authors employ a data-driven approach to establish predictive scaling laws that describe the phase behavior of these domains.

Strengths:

The study benefits from a robust dataset encompassing a wide range of PLDs, which enhances the generalizability of the findings. The authors' meticulous curation and analysis of this data add to the study's robustness. The scaling laws derived from the data provide predictive insights into the phase behavior of PLDs, which can be useful in the future for the design of synthetic biomolecular condensates.

Weaknesses:

While the data-driven approach is powerful, the study could benefit from more experimental validation. Experimental studies confirming the predictions of the scaling laws would strengthen the conclusions. For example, in Figure 1, the Tc of TDP-43 is below 300 K even though it can undergo LLPS under standard conditions. Figure 2 clearly highlights the quantitative accuracy of the model for hnRNPA1 PLD mutants, but its applicability to other systems such as TDP-43, FUS, TIA1, EWSR1, etc., may be questionable.

The authors may wish to consider checking if the scaling behavior is only observed for Tc or if other experimentally relevant quantities such as Csat also show similar behavior. Additionally, providing more intuitive explanations could make the findings more broadly accessible.

The study focuses on a particular subset of intrinsically disordered regions. While this is necessary for depth, it may limit the applicability of the findings to other types of phase-separating biomolecules. The authors may wish to discuss why this is not a concern. Some statements in the paper may require careful evaluation for general applicability, and I encourage the authors to exercise caution while making general conclusions. For example, "Therefore, our results reveal that it is almost twice more destabilizing to mutate Arg to Lys than to replace Arg with any uncharged, non-aromatic amino acid..." This may not be true if the protein has a lot of negative charges.

I am surprised that a quarter of a million CPU hours are described as staggering in terms of computational requirements.

Reviewer #1 (Public Review):

Summary:

In this paper, the authors had 2 aims:

(1) Measure macaques' aversion to sand and see if its' removal is intentional, as it is likely in an unpleasurable sensation that causes tooth damage.

(2) Show that or see if monkeys engage in suboptimal behavior by cleaning foods beyond the point of diminishing returns, and see if this was related to individual traits such as sex and rank, and behavioral technique.

They attempted to achieve these aims through a combination of geochemical analysis of sand, field experiments, and comparing predictions to an analytical model.

The authors' conclusions were that they verified a long-standing assumption that monkeys have an aversion to sand as it contains many potentially damaging fine-grained silicates and that removing it via brushing or washing is intentional.

They also concluded that monkeys will clean food for longer than is necessary, i.e. beyond the point of diminishing returns, and that this is rank-dependent.

High and low-ranking monkeys tended not to wash their food, but instead over-brushed it, potentially to minimize handling time and maximize caloric intake, despite the long-term cumulative costs of sand.

This was interpreted through the *disposable soma hypothesis*, where dominants maximize immediate needs to maintain rank and increase reproductive success at the potential expense of long-term health and survival.

Strengths:

The field experiment seemed well-designed, and their quantification of physical and mineral properties of quartz particles (relative to human detection thresholds) seemed good relative to their feret diameter and particle circularity (to a reviewer who is not an expert in sand). The *Rank Determination* and *Measuring Sand* sections were clear.

In achieving Aim 1, the authors validated a commonly interpreted, but unmeasured function, of macaque and primate behavior-- a key study/finding in primate food processing and cultural transmission research.

I commend their approach in developing a quantitative model to generate predictions to compare to empirical data for their second aim.

This is something others should strive for.

I really appreciated the historical context of this paper in the introduction, and found it very enjoyable and easy to read.

I do think that interpreting these results in the context of the *disposable soma hypothesis* and the potential implications in the *paleolithic matters* section about interpreting dental wear in the fossil record are worthwhile.

Weaknesses:

Most of the weaknesses in this paper lie in statistical methods, visualization, and a missing connection to the marginal value theorem and optimal foraging theory.

I think all of these weaknesses are solvable.

The data and code were not submitted. Therefore I was unable to better understand the simulation or to provide useful feedback on the stats, the connection between the two, and its relevance to the broader community.

(1) Statistics:

(a) AIC and outcome distributions

The use of AIC for hierarchical models, and models with different outcome distributions brought up several concerns.

The authors appear to use AIC to help inform which model to use for their primary analyses in Tables S1 and S2. It is unclear which of these models are analyzed in Tables S3 and S4.

AIC should not be used on hierarchical models, and something like WAIC (or DIC which has other caveats) would be more appropriate.

Also, using information criteria on Mixture Models like Negative Binomials (aka Gamma-Poisson) should be done with extreme caution, or not at all, as the values are highly sensitive to the data structure.

Some researchers also say that information criteria should not be used to compare models with different outcome distributions - although this might be slightly less of a concern as all of your models are essentially variations on a Poisson GLM.

Discussion on this can be found in McElreath Statistical Rethinking (Section 12.1.3) and Gelman et al. BDA3 (Chapter 7).

Choosing an outcome distribution, based on your understanding of the data generating process is a better approach than relying on AIC, especially in this context where it can be misleading.

(b) Zeros

I also had some concerns about how zeros were treated in the models.

In lines 217-218, they mentioned that "if a monkey consumed a cucumber slice without brushing or washing it, the zero-second duration was included in both GLMMs."

This zero implies no processing and should not be treated as a length 0 duration of processing.

This suggests to me that a zero-inflated poisson or zero-inflated negative binomial, would be the best choice for modelling the data as it is essentially a 2-step process:<br /> (i) Do they process the cucumber at all?<br /> (ii) If so do they wash or brush, and how is this predicted by rank and treatment?

(2) Absence of Links to Foraging Theory

Optimal cleaning time model: the optimality model was not well described including how it was programmed. Better description and documentation of this model, along with code (Mathematica judging from the plot?) is needed.

There seems to be much conceptual and theoretical overlap with foraging theory models that were not well described - namely the *marginal value theorem (Charnov (1976), Krebs et al. (1974),) and its subsequent advances* (see https://doi.org/10.1016/j.jaa.2016.03.002 and https://doi.org/10.1086/283929 for examples).

In the suggestions, I attached the R code where I replicated their model to show that it is *mathematically identical to the marginal value theorem*. This was not mentioned at all in the text or citations.

This is a well-studied literature since the 1970's and there is a history of studies that compare behavior to an optimality model and fail (or do find) instances where animals conform or diverge with its predictions (https://doi.org/10.1146/annurev.es.15.110184.002515). This link should be highlighted, and interpreting it in that theoretical context will make it more broadly applicable to behavioral ecologists.

The data was subsetted to include instances where there were < 3 monkeys present to avoid confounds of rank, but it is important to know that optimal behavior might vary by individual, and can change in a social context depending on rank (see https://doi.org/10.1016/j.tree.2022.06.010). Discussion of this, and further exploration of it in the data would strengthen the overall contribution of this manuscript to the field, but I understand that the researchers wish to avoid that in this paper for it is a complex topic, which this dataset is uniquely suited to address.

(3) Interpretation and validity of model relative to data

In lines 92-102, they present summary statistics (I think) showing that time spent brushing and washing is consistent with washing or brushing to remove sand.

In the **mitigating tooth wear** section (line 73) and corresponding Figure S1 showing surface sand removed, more detail about how these numbers were acquired, and statistical modelling, is needed.

This is important as uncertainty and measurement error around these metrics are key to the central finding and interpretation of Aim 2 in this paper.

It appears that the researchers simulated the monkey's brushing and washing behaviors (similar to https://doi.org/10.1007/s10071-009-0230-3).

How many researchers simulated monkey behavior and how many times?

What are the repeat points in Figure S1?

What is the number of trials or number of people?

This effect appears stronger for washing than brushing as well - if so, why?

More info about this data, and the uncertainty in this is important, as it is key to the second central claim of this paper.

The estimates of removing between 76% +/- 7 and 93% +/- 4 of sand (visualized in Figure S1), are statistical estimates.

I would find the argument more convincing if after propagating for the uncertainty in handling in sand removal rates, and the corresponding half-saturation constants, if this processing for food is too long, after accounting for diminishing returns held true.<br /> It is very possible that after accounting for uncertainty and variation in handling time and removal rates, the second result may not hold true.

I was not able to convince myself of this via reanalysis as the description of the data in the text was not enough to simulate it myself.

Essentially, this would imply that in Figure 3 the predicted value would have some variation around it (informed by boundary conditions of time being positive, and percents having floors and ceilings) and that a range of predicting cleaning times (optimal give-up times) would be plotted in Figure 3.

This could be accomplished in a Bayesian approach, Or by simply plotting multiple predictions given some confidence interval around, c and h.

Reviewer #2 (Public Review):

Summary:

This field experiment aimed to assess what motivates macaque monkeys to clean food items prior to consumption and the relative costs and benefits of different cleaning approaches (manually brushing sand from food versus dousing food items in water). The experiment teases apart if/how the benefits of these approaches are mediated by the amount of debris on food and the monkeys' rank in terms of the costs of consuming sand versus the time and energy required to remove it. The authors not only examined the behavioral responses of wild macaques to three conditions of food sand contamination but also tested the relative costs of consuming different levels and sizes of sand particulates. Through this, the authors propose considerations of the macaques' motivations to clean food and the balance they take in energetic gains from consuming food versus the costs of cleaning food and consuming sand. Their data reveal that food washing is more effective in removing sand, but more costly than manually brushing off sand. This study also revealed that only mid-ranked monkeys washed their food, while high and low-ranked monkeys were more likely to remove sand via brushing it off food with their hands.

Strengths:

This study provides a very in-depth consideration of the motivations of macaques to clean their food, and the relative costs and benefits of different food cleaning techniques. Not only did the study test the behavior of wild macaques via a simple yet elegant field study, but they also performed a detailed analysis of the sand particulates to understand the level of potential tooth wear that consuming it could result in. By relying on a wild group of macaques that have been part of a long-term study site, the team also had detailed behavioral data on the population to allow for rank assessments of the animals. This comprehensive study provides important foundational information for a better understanding of how and why macaques clean food, that inform existing and future considerations of this as a potential cultural behavior.

Weaknesses:

As currently written, the paper does not provide sufficient background on this population of animals and their prior demonstrations of food-cleaning behavior or other object-handling behaviors (e.g., stone handling). Moreover, the authors' conclusions focus on the behavior of high-ranked animals, but subordinate animals also showed similar behavioral patterns and they should be considered in more detail too.

Reviewer #3 (Public Review):

This paper provides evidence that food washing and brushing in wild long-tailed macaques are deliberate behaviors to remove sand that can damage tooth enamel. The demonstration of the immediate functional importance of these behaviors is nicely done. However, the paper also makes the claim that macaques systematically differ in their investment in food cleaning because of rank-dependent differences in their costs and benefits. This latter conclusion is not, in my view, well-supported, for several reasons.

First, as is typical in many primate studies, the authors construct sex-specific ordinal rank hierarchies. This makes sense since hierarchies for males and hierarchies for females are determined by different processes and have different consequences. However, if I understand it correctly, they are then lumped together in all statistical analyses of rank, which makes the apparent rank effect very difficult to understand. The challenge of interpretation is increased because there are twice as many adult females in the group as adult males, so the rank is confounded by sex (because all low-rank values are adult females).

Second, because only one social group is being studied, the conclusions about rank may be heavily driven by individual identity, not rank per se. An analysis involving replicate social groups (which granted, may be impossible here) or longitudinal data showing a change in behavior following a change in rank would be much more compelling.

Third, there is no evidence presented on the actual fitness-related costs of tooth wear or the benefits of slightly faster food consumption. Support for these arguments is provided based on other papers, some of which come from highly resource-limited populations (and different species). But this is a population that is supplemented by tourists with melons, cucumbers, and pineapples! In the absence of more direct data on fitness costs and benefits, the paper makes overly strong claims about the ability to explain its observations based on "immediate energetic requirements" (abstract), "difference...freighted with fitness consequences" (line 80), and "pressing energetic needs"/"live fast, die young" (lines 121-122--there is no evidence that tooth wear is associated with morbidity or mortality here). The idea that high-ranking animals are "sacrificing their teeth at the altar of high rank" seems extreme.

Reviewer #1 (Public Review):

Summary:

The authors attempt to understand how cells forage for spatially heterogeneous complex polysaccharides. They aimed to quantify the foraging behavior and interrogate its genetic basis. The results show that cells aggregate near complex polysaccharides and disperse when simpler byproducts are added. Dispersing cells tend to move towards the polysaccharide. The authors also use transcriptomics to attempt to understand which genes support each of these behaviors - with motility and transporter related genes being highly expressed during dispersal, as expected.

Strengths:

The paper is well written and builds on previous studies by some of the authors showing similar behavior by a different species of bacteria (Caulobacter) on another polysaccharide (xylan). The conceptual model presented at the end encapsulates the findings and provides an interesting hypothesis. I also find the observation of chemotaxis towards the polysaccharide in the experimental conditions interesting.

Weaknesses:

Much of the genetic analysis, as it stands, is quite speculative and descriptive. I found myself confused about many of the genes (e.g., quorum sensing) that pop up enriched during dispersal quite in contrast to my expectations. While the authors do discuss this in the text as worth following up on, I think the analysis as it stands is speculative about the behaviors observed. In the authors' defense, I acknowledge that it might have the potential to generate hypotheses and thus aid future studies.

Reviewer #2 (Public Review):

Summary:

The paper sets out to understand the mechanisms underlying the colonization and degradation of marine particles using a natural Vibrio isolate as a model. The data are measurements of motility and gene expressing using microfluidic devices and RNA sequencing. The results reveal that degradation products of alginate do stimulate motility but not chemotaxis. In contrast, alginate itself (the polymer) does stimulate chemotaxis. Further, the dispersal from degrading alginate is density dependent, increasing at higher density. The evidence for these claims are strong. From these the authors propose a narrative (Fig. 6) for growth and dispersal cycles in this system. The idea is that cells colonize and degrade alginate, this degradation stimulates motility and dispersal followed by chemotaxis to a new alginate source. This complete narrative has modest support in the data. A quantitative description of these dynamics awaits future studies.

Strengths:

The microfluidic measurements are the central strength of the paper. The density dependence claim is qualitatively supported by the data. The motility and chemotaxis claims are also well supported by the data. The presentation of the experiment and results are well done. The study serves to motivate a unifying picture of growth and dispersal in marine systems. This is a key process in the global carbon cycle.

Weaknesses:

Perhaps not a weakness, but a glimmer that this is not yet the full story. The RNA expression data show alginate lyase expression in response to digested alginate which is unexpected given the narrative articulated above. Why express lyases while leaving the polymer patch via motility? This question is addressed in the Discussion. A holistic and quantitative picture of the proposed process in Figure 6 awaits additional studies.

Reviewer #3 (Public Review):

Summary:

In this manuscript, Stubbusch and coauthors examine the foraging behavior of a marine species consuming an abundant marine polysaccharide. Laboratory experiments in a microfluidic setup are complemented with transcriptomic analyses aiming at assessing the genetic bases of the observed behavior. Bacterial cells consuming the polysaccharide form cohesive aggregates, while start dispersing away when the byproduct of the digestion of the polysaccharide start accumulating. Dispersing cells, tend to be attracted by the polysaccharide. Expression data show that motility genes are enriched during the dispersal phase, as expected. Counterintuitively, in the same phase, genes for transporters and digestions of polysaccharide are also highly expressed.

Strengths:

The manuscript is very well written and easy to follow. The topic is interesting and timely. The genetic analyses provide a new, albeit complex, angle to the study of foraging behaviors in bacteria, adding to previous studies conducted on other species.

Weaknesses:

I find this paper very descriptive and speculative. The results of the genetic analyses are quite counterintuitive; therefore, I understand the difficulty of connecting them to the observations coming from experiments in the microfluidic device. However, they could be better placed in the literature of foraging - dispersal cycles, beyond bacteria. In addition, the interpretation of the results is sometimes confusing.

Reviewer #1 (Public Review):

The present paper presents a new, simple, and cost-effective technique for multimodal EM imaging that combines the strengths of volume scanning electron microscopy (SEM) and electron microscopic tomography. The novel ATUM-Tomo approach enables the consecutive inspection of selected areas of interest by correlated serial SEM and TEM, optionally in combination with CLEM, as demonstrated. The most important finding of ATUM-Tomo and particularly correlative ATUM-Tomo is that it can bridge several scales from the cellular to the high-resolution subcellular scale, from the micrometer to low nanometer resolution, which is particularly important for the ultrastructural analysis of biological regions of interest as demonstrated here by focal pathologies or rare cellular and subcellular structures. Both imaging modalities are non-destructive, thus allowing re-imaging and hierarchical imaging at the SEM and TEM levels, which is particularly important for precious samples, such as human biopsies or specimens from complex CLEM experiments. The paper demonstrates that the new approach is very helpful in analyses of pathologically altered brains, including humans brain tissue samples, that require high-resolution SEM and TEM in combination with immunohistochemistry for analysis. Even the combination with tracers would be possible. In sum, ATUM-Tomo opens up new possibilities in multimodal volume EM imaging for diverse biological areas of research.

Strengths

This paper is a very nice piece of work. It combines modern, high-end, state-of-the-art technology that allows to investigate diverse biological questions in different fields and at multiple scales. The paper is clear and well-written. It is accompanied by excellent figures, supplementals, and colored 3D-reconstructions that make it easy for the reader to follow the experimental procedure and the scientific context alike.

Weaknesses

There is a bit of an imbalance between the description of the state-of-the-art methodology and the scientific context. The discussion of the latter could be expanded.

Reviewer #2 (Public Review):

Kislinger et al. present a method permitting a targeted, multi-scale ultrastructural imaging approach to bridge the resolution gap between large-scale scanning electron microscopy (SEM) and transmission electron microscopy (TEM). The key methodological development consists of an approach to recover sections of resin-embedded material produced by Automated Tape Collecting Ultramicrotomy (ATUM), thereby permitting regions of interest identified by serial section SEM (ATUM-SEM) screening to be subsequently re-examined at higher resolution by TEM tomography (ATUM-Tomo). The study shows that both formvar and permanent marker coatings are in principle compatible with solvent-based release of pre-screened sections from ATUM tape (carbon nanotubule or Kapton tape). However, a comparative analysis of potential limitations and artifacts introduced by these respective coatings revealed permanent marker to provide a superior coating; permanent marker coatings are more easily and reliably applied to tape with only minor contaminants affecting the recovered section-tape interface with negligible influence on tomogram interpretation. Convincing proof-of-principle is provided by integrating this novel ATUMTomo technique into a technically impressive correlated light and electron microscopy (CLEM) approach specifically tailored to investigate ultrastructural manifestations of trauma-induced changes in blood-brain barrier permeability.

Strengths

Schematics and figures are very well-constructed, illustrating the workflow in a logical and easily interpretable manner. Light and electron microscope image data are of excellent quality, and the efficacy of the ATUM-Tomo approach is evidenced by a qualitative assessment of ATUM-SEM performance using coated tape variants and a convincing correlation between scanning and transmission electron microscopy imaging modalities. Potential ultrastructural artifacts induced via solvent exposure and any subsequent mechanical stress incurred during section detachment were thoroughly and systematically investigated using appropriate methods and reported with commendable transparency. In summary, the presented data convincingly support the claims of the study. A major strength of this work includes its general applicability to a broad range of biological questions and ultrastructural targets demanding resolutions exceeding that obtained via serial section and destructive block-face imaging approaches alone. The level of methodological detail provided is sufficient for replication of the ATUM-Tomo technique in other laboratories. Consequently, this relatively simple and cost-effective technique is widely adoptable by electron microscopy laboratories, and its integration into existing ATUM-SEM workflows supports a versatile and non-destructive imaging regime enabling high-resolution details of targeted structures to be interpreted within anatomical and subcellular contexts.

Weaknesses

I find no significant weaknesses in the current version of the manuscript.

Reviewer #1 (Public Review):

Summary:

In this study, Faniyan and colleagues build on their recent finding that renal Glut2 knockout mice display normal fasting blood glucose levels despite massive glucosuria. Renal Glut2 knockout mice were found to exhibit increased endogenous glucose production along with decreased hepatic metabolites associated with glucose metabolism. Crh mRNA levels were higher in the hypothalamus while circulating ACTH and corticosterone was elevated in this model. While these mice were able to maintain normal fasting glucose levels, ablating afferent renal signals to the brain caused low fasting blood glucose levels. In addition, the higher CRH and higher corticosterone levels of the knockout mice were lost following this denervation. Finally, acute phase proteins were altered, plasma Gpx3 was lower, and major urinary protein MUP18 and its gene expression were higher in renal Glut2 knockout mice. Overall, the main conclusion that afferent signaling from the kidney is required for renal glut2 dependent increases in endogenous glucose production is well supported by these findings.

Strengths:

An important strength of the paper is the novelty of the identification of kidney to brain communication as being important for glucose homeostasis. Previous studies had focused on other functions of the kidney modulated by or modulating brain function. This work is likely to promote interest in CNS pathways that respond to afferent renal signals and the response of the HPA axis to glucosuria. Additional strengths of this paper stem from the use of incisive techniques. Specifically, the authors use isotope enabled measurement of endogenous glucose production by GC-MS/MS, capsaicin ablation of afferent renal nerves, and multifiber recording from the renal nerve. The authors also paid excellent attention to rigor in the design and performance of these studies. For example, they used appropriate surgical controls, confirmed denervation through renal pelvic CGRP measurement, and avoided the confounding effects of nerve regrowth over time. These factors strengthen confidence in their results. Finally, humans with glucose transporter mutations and those being treated with SGLT2 inhibitors show a compensatory increase in endogenous glucose production. Therefore, this study strengthens the case for using renal Glut2 knockout mice as a model for understanding the physiology of these patients.

Comments on latest version:

My concerns have been addressed.

Reviewer #1 (Public Review):

Summary:

Authors explore how sex-peptide (SP) affects post-mating behaviours in adult females, such as receptivity and egg laying. This study identifies different neurons in the adult brain and the VNC that become activated by SP, largely by using an intersectional gene expression approach (split-GAL4) to narrow down the specific neurons involved. They confirm that SP binds to the well-known Sex Peptide Receptor (SPR), initiating a cascade of physiological and behavioural changes related to receptivity and egg laying.

Areas of improvement and suggestions:

(1) "These results suggest the SP targets interneurons in the brain that feed into higher processing centers from different entry points likely representing different sensory input" and "All together, these data suggest that the abdominal ganglion harbors several distinct type of neurons involved in directing PMRs"<br /> The characterization of the post-mating circuitry has been largely described by the group of Barry Dickson and other labs. I suggest ruling out a potential effect of mSP in any of the well-known post-mating neuronal circuitry, i.e: SPSN, SAG, pC1, vpoDN or OviDNs neurons. A combination of available split-Gal4 should be sufficient to prove this.

(2) Authors must show how specific is their "head" (elav/otd-flp) and "trunk" (elav/tsh) expression of mSP by showing images of the same constructs driving GFP.

(3) VT3280 is termed as a SAG driver. However, VT3280 is a SPSN specific driver (Feng et al., 2014; Jang et al., 2017; Scheunemann et al., 2019; Laturney et al., 2023). The authors should clarify this.

(4) Intersectional approaches must rule out the influence of SP on sex-peptide sensing neurons (SPSN) in the ovary by combining their constructs with SPSN-Gal80 construct. In line with this, most of their lines targets the SAG circuit (4I, J and K). Again, here they need to rule out the involvement of SPSN in their receptivity/egg laying phenotypes. Especially because "In the female genital tract, these split-Gal4 combinations show expression in genital tract neurons with innervations running along oviduct and uterine walls (Figures S3A-S3E)".

(5) The authors separate head (brain) from trunk (VNC) responses, but they don't narrow down the neural circuits involved on each response. A detailed characterization of the involved circuits especially in the case of the VNC is needed to (a) show that the intersectional approach is indeed labelling distinct subtypes and (b) how these distinct neurons influence oviposition.

Reviewer #3 (Public Review):

Summary:

This paper reports new findings regarding neuronal circuitries responsible for female post-mating responses (PMRs) in Drosophila. The PMRs are induced by sex peptide (SP) transferred from males during mating. The authors sought to identify SP target neurons using a membrane-tethered SP (mSP) and a collection of GAL4 lines, each containing a fragment derived from the regulatory regions of the SPR, fru, and dsx genes involved in PMR. They identified several lines that induced PMR upon expression of mSP. Using split-GAL4 lines, they identified distinct SP-sensing neurons in the central brain and ventral nerve cord. Analyses of pre- and post-synaptic connection using retro- and trans-Tango placed SP target neurons at the interface of sensory processing interneurons that connect to two common post-synaptic processing neuronal populations in the brain. The authors proposed that SP interferes with the processing of sensory inputs from multiple modalities.

Strengths:

Besides the main results described in the summary above, the authors discovered the following:

(1) Reduction of receptivity and induction of egg-laying are separable by restricting the expression of membrane-tethered SP (mSP): head-specific expression of mSP induces reduction of receptivity only, whereas trunk-specific expression of mSP induces oviposition only. Also, they identified a GAL4 line (SPR12) that induced egg laying but did not reduce receptivity.

(2) Expression of mSP in the genital tract sensory neurons does not induce PMR. The authors identified three GAL4 drivers (SPR3, SPR 21, and fru9), which robustly expressed mSP in genital tract sensory neurons but did not induce PMRs. Also, SPR12 does not express in genital tract neurons but induces egg laying by expressing mSP.

Weaknesses:

(1) Intersectional expression involving ppk-GAL4-DBD was negative in all GAL4AD lines (Supp. Fig.S5). As the authors mentioned, ppk neurons may not intersect with SPR, fru, dsx, and FD6 neurons in inducing PMRs by mSP. However, since there was no PMR induction and no GAL4 expression at all in any combination with GAL4-AD lines used in this study, I would like to have a positive control, where intersectional expression of mSP in ppk-GAL4-DBD and other GAL4-AD lines (e.g., ppk-GAL4-AD) would induce PMR.

(2) The results of SPR RNAi knock-down experiments are inconclusive (Figure 5). SPR RNAi cancelled the PMR in dsx ∩ fru11/12 and partially in SPR8 ∩ fru 11/12 neurons. SPR RNAi in dsx ∩ SPR8 neurons turned virgin females unreceptive; it is unclear whether SPR mediates the phenotype in SPR8 ∩ fru 11/12 and dsx ∩ SPR8 neurons.

SPR RNAi knock-down experiments may also help clarify whether mSP worked autocrine or juxtacrine to induce PMR. mSP may produce juxtacrine signaling, which is cell non-autonomous.

Reviewer #2 (Public Review):

Sex peptide (SP) transferred during mating from male to female induces various physiological responses in the receiving female. Among those, the increase in oviposition and decrease in sexual receptivity are very remarkable. Naturally, a long standing and significant question is the identity of the underlying sex peptide target neurons that express the SP receptor and are underlying these responses. Identification of these neurons will eventually lead to the identification of the underlying neuronal circuitry.

The Soller lab has addressed this important question already several years ago (Haussmann et al. 2013), using relevant GAL4-lines and membrane-tethered SP. The results already showed that the action of SP on receptivity and oviposition is mediated by different neuronal subsets and hence can be separated. The GAL4-lines used at that time were, however, broad, and the individual identity of the relevant neurons remained unclear.

In the present paper, Nallasivan and colleagues carried this analysis one step further, using new intersectional approaches and transsynaptic tracing.

Strength:

The intersectional approach is appropriate and state-of-the art. The analysis is a very comprehensive tour-de-force and experiments are carefully performed to a high standard. The authors also produced a useful new transgenic line (UAS-FRTstopFRT mSP). The finding that neurons in the brain (head) mediate the SP effect on receptivity, while neurons in the abdomen and thorax (ventral nerve cord or peripheral neurons) mediate the SP effect on oviposition, is a significant step forward in the endavour to identify the underlying neuronal networks and hence a mechanistic understanding of SP action. Though this result is not entirely unexpected, it is novel as it was not shown before.

Weakness:

Though the analysis identifies a small set of neurons underlying SP responses, it does not go the last step to individually identify at least a few of them. The last paragraph in the discussion rightfully speculates about the neurochemical identity of some of the intersection neurons (e.g. dopaminergic P1 neurons, NPF neurons). At least these suggested identities could have been confirmed by straight-forward immunostainings agains NPF or TH, for which antisera are available. Moreover, specific GAL4 lines for NPF or P1 or at least TH neurons are available which could be used to express mSP to test whether SP activation of those neurons is sufficient to trigger the SP effect.

Reviewer #1 (Public Review):

Previous Review:

The authors have identified the predicted EBE of PthA4 in the promoter of Cs9g12620, which is induced by Xcc. The authors identified a homolog of Cs9g12620, which has variations in the promoter region. The authors show PthA4 suppresses Cs9g12620 promoter activity independent of the binding action. The authors also show that CsLOB1 binds to the promoter of Cs9g12620. Interestingly, the authors show that PthA4 interacts with CsLOB1 at protein level. Finally, it shows that Cs9g12620 is important for canker symptoms. Overall, this study has reported some interesting discoveries and the writing is generally well done. However, the discoveries are affected by the reliability of the data and some flaws of the experimental designs.

Here are some major issues:

The authors have demonstrated that Cs9g12620 contains the EBE of PthA4 in the promoter region, to show that PthA4 controls Cs9g12620, the authors need to compare to the wild type Xcc and pthA4 mutant for Cs9g12620 expression. The data in Figure 1 is not enough.

The authors confirmed the interaction between PthA4 and the EBE in the promoter of Cs9g12620 using DNA electrophoretic mobility shift assay (EMSA). However, Fig. 2B is not convincing. The lane without GST-PthA4 also clearly showed mobility shift. For EMSA assay, the authors need also to include non-labeled probe as competitor to verify the specificity. The description of the EMSA in this paper suggests that it was not done properly. It is suggested the authors to redo this EMSA assay following the protocol: Electrophoretic mobility shift assay (EMSA) for detecting protein-nucleic acid interactions PMID: 17703195.

The authors also claimed that PthA4 suppresses the promote activity of Cs9g12620. The data is not convincing and also contradicts with their own data that overexpression of Cs9g12620 causes canker and silencing of it reduces canker considering PthA4 is required for canker development. The authors conducted the assays using transient expression of PthA4. It should be done with Xcc wild type, pthA4 mutant and negative control to inoculate citrus plants to check the expression of Cs9g12620.

Fig. 6 AB is not convincing. There are no apparent differences. The variations shown in B is common in different wild type samples. It is suggested that the authors to conduct transgenic instead of transient overexpression.

Gene silencing data needs more appropriate controls. Fig. D. seems to suggest canker symptoms actually happen for the RNAi treated. The authors need to make sure same amount of Xcc was used for both CTV empty vector and the RNAi. It is suggested a blink test is needed here.

Comments on revised version:

Point 1: Addressed well.

Point 2: The EMSA was reconducted with adding unlabeled DNA, however, the results are still not convincing. Firstly, in fig.3D lane 5, with the absence of unlabeled DNA, the shifted bound signal wasn't reduced significantly. Secondly, still in fig.3D lane 5, the free labeled DNA probe at the bottom of the gel didn't increase. Which together mean that the unlabeled DNA was unable to compete with the labeled DNA and the "bound" shifted bands might not be true positive.

Point 3: The authors didn't address the question clearly regarding the connection between the inhibition of Cs9g12620 promoter by PthA4 and the positive function of Cs9g12620 on citrus canker.

Point 4: The comment was not addressed. Fig.7A and B are not convincing. Firstly, no evidence shows the expression of transiently expressed genes. Secondly, hard to tell the difference in 7A. Thirdly, since CsLOB1 positively regulates Cs9g12620, why expressing of CsLOB1 is unable to cause phenotype, while expression of PthA4 does?

Point 5: addressed.

Reviewer #1 (Public Review):

Summary:

Orlovski and his colleagues revealed an interesting phenomenon that SAP54-overexpressing leaf exposure to leafhopper males is required for the attraction of followed females. By transcriptomic analysis, they demonstrated that SAP54 effectively suppresses biotic stress response pathways in leaves exposed to the males. Furthermore, they clarified how SAP54, by targeting SVP, heightens leaf vulnerability to leafhopper males, thus facilitating female attraction and subsequent plant colonization by the insects.

Strengths:

The phenomenon of this study is interesting and exciting.

Weaknesses:

The underlying mechanisms of this phenomenon are not convincing.

Reviewer #2 (Public Review):

Summary:

In this study, the authors show that leaf exposure to leafhopper males is required for female attraction in the SAP54-expressing plant. They clarify how SAP54, by degrading SVP, suppresses biotic stress response pathways in leaves exposed to the males, thus facilitating female attraction and plant colonization.

Strengths:

This study suggests the possibility that the attraction of insect vectors to leaves is the major function of SAP54, and the induction of the leaf-like flowers may be a side-effect of the degradation of MTFs and SVP. It is a very surprising discovery that only male insect vectors can effectively suppress the plant's biotic stress response pathway. Although there has been interest in the phyllody symptoms induced by SAP54, the purpose, and advantage of secreting SAP54 were unknown. The results of this study shed light on the significance of secreted proteins in the phytoplasma life cycle and should be highly evaluated.

Weaknesses:

One weakness of this study is that the mechanisms by which male and female leafhoppers differentially affect plant defense responses remain unclear, although I understand that this is a future study.

The authors show that female feeding suppresses female colonization on SAP54-expressing plants. This is also an intriguing phenomenon but this study doesn't explain its molecular mechanism (Figure 7).

Reviewer #1 (Public Review):

Summary:

The authors used video tracking of 4 larval cichlid species and medaka to quantify prey-capture behaviors.

Strengths:

Comparing these behaviors is in principle an interesting question, and helps to address the typicality of the much better-understood zebrafish model. The authors make a good effort to analyze their data quantitatively.

Weaknesses:

(1) The overall conclusion, as summarized in the abstract as "Together, our study documents the diversification of locomotor and oculomotor adaptations among hunting teleost larvae" is not that compelling. What would be much more interesting would be to directly relate these differences to different ecological niches (e.g. different types of natural prey, visual scene conditions, height in water column etc), and/or differences in neural circuit mechanisms. While I appreciate that this paper provides a first step on this path, by itself it seems on the verge of stamp collecting, i.e. collecting and cataloging observations without a clear, overarching hypothesis or theoretical framework.

(2) The data to support some of the claims is either weak or lacking entirely.

Reviewer #2 (Public Review):

Summary:

This is a fascinating study about the behavioral kinematics of prey capture in larvae of several fish species (zebrafish, four cichlid species, and medaka). The authors describe in great detail swimming kinematics, hunting movement, eye movement as well as prey capture kinematics across these species. One striking finding is that cichlids and zebrafish use binocular vision to hunt for prey whereas medaka uses a monocular hunting style with a sideways motion to capture prey. The behavioral variation described in this study forms a strong foundation for future studies on the mechanisms underlying variation in hunting styles.

Strengths:

In general, the paper is well-written and documents very interesting data. The authors used sophisticated analyses that help appreciate the complexity of the behaviors examined. The discussion attempts to place the paper in a broader, comparative context. Overall, this paper reveals novel insight into an important behavior across different teleost species and lays a foundation for future studies on the neural and genetic basis of these distinct swimming and hunting behaviors.

Weaknesses:

The paper is rather descriptive in nature, although more context is provided in the discussion. Most figures are great, but I think the authors could add a couple of visual aids in certain places to explain how certain components were measured.

Reviewer #3 (Public Review):

Summary:

This paper uses 2D pose estimation and quantitative behavioral analyses to compare patterns of prey capture behavior used by six species of freshwater larval fish, including zebrafish, medaka, and four cichlids. The convincing comparison of tail and eye kinematics during hunts reveals that cichlids and zebrafish use binocular vision and similar hunting strategies, but that cichlids make use of an expanded set of action types. The authors also provide convincing evidence that medaka instead use monocular vision during hunts. This finding has important implications for the evolution of distinct distance estimation algorithms used by larval teleost fish species during prey capture.

Strengths:

The quality of the behavioral data is solid and the high frame rate allowed for careful quantification and comparison of eye and tail dynamics during hunts. The statistical approach to assess eye vergence states (Figure 2B) is elegant, the cross-species comparison of prey location throughout each hunt phase is well done (Figure 3B-D), and the demonstration that swim bout tail kinematics from diverse species can be embedded in a shared "canonical" principal component space to explain most of the variance in 2D postural dynamics for each species (Figure 4A-C) provides a simple and powerful framework for future studies of behavioral diversification across fish species.

Weaknesses:

More evidence is needed to assess the types of visual monocular depth cues used by medaka fish to estimate prey location, but that is beyond the scope of this compelling paper. For example, medaka may estimate depth through knowledge of expected prey size, accommodation, defocus blur, ocular parallax, and/or other possible algorithms to complement cues from motion parallax.

Reviewer #1 (Public Review):

Summary and Strengths:

The study focuses on PIM1 and 2 in CD8 T cell activation and differentiation. These two serine/threonine kinases belong to a large network of Serine/Threonine kinases that acts following engagement of the TCR and of cytokine receptors and phosphorylates proteins that control transcriptional, translational and metabolic programs that result in effector and memory T cell differentiation. The expression of PIM1 and PIM2 is induced by the T-cell receptor and several cytokine receptors. The present study capitalized on high-resolution quantitative analysis of the proteomes and transcriptomes of Pim1/Pim2-deficient CD8 T cells to decipher how the PIM1/2 kinases control TCR-driven activation and IL-2/IL-15-driven proliferation, and differentiation into effector T cells.<br /> Quantitative mass spectrometry-based proteomics analysis of naïve OT1 CD8 T cell stimulated with their cognate peptide showed that the PIM1 protein was induced within 3 hours of TCR engagement and its expression was sustained at least up to 24 hours. The kinetics of PIM2 expression was protracted as compared to that of PIM1. Such TCR-dependent expression of PIM1/2 correlated with the analysis of both Pim1 and Pim2 mRNA. In contrast, Pim3 mRNA was only expressed at very low levels and the PIM3 protein was not detected by mass spectrometry. Therefore, PIM1 and 2 are the major PIM kinases in recently activated T cells. Pim1/Pim2 double knockout (Pim dKO) mice were generated on a B6 background and found to express a lower number of splenocytes. No difference in TCR/CD28-driven proliferation was observed between WT and Pim dKO T cells over 3 days in culture. Quantitative proteomics of >7000 proteins further revealed no substantial quantitative or qualitative differences in protein content or proteome composition. Therefore, other signaling pathways can compensate for the lack of PIM kinases downstream of TCR activation.

Considering that PIM1 and PIM2 kinase expression is regulated by IL-2 and IL-15, antigen-primed CD8 T cells were expanded in IL-15 to generate memory phenotype CD8 T cells or expanded in IL-2 to generate effector cytotoxic T lymphocytes (CTL). Analysis of the survival, proliferation, proteome, and transcriptome of Pim dKO CD8 T cells kept for 6 days in IL-15 showed that PIM1 and PIM2 are dispensable to drive the IL-15-mediated metabolic or differentiation programs of antigen-primed CD8 T cells. Moreover, Pim1/Pim2-deficiency had no impact on the ability of IL-2 to maintain CD8 T cell viability and proliferation. However, WT CTL downregulated the expression of CD62L whereas the Pim dKO CTL sustained higher CD62L expression. Pim dKO CTL was also smaller and less granular than WT CTL. Comparison of the proteome of day 6 IL-2 cultured WT and Pim dKO CTL showed that the latter expressed lower levels of the glucose transporters, SLC2A1 and SLC2A3, of a number of proteins involved in fatty acid and cholesterol biosynthesis, and CTL effector proteins such as granzymes, perforin, IFNg, and TNFa. Parallel transcriptomics analysis showed that the reduced expression of perforin and some granzymes correlated with a decrease in their mRNA whereas the decreased protein levels of granzymes B and A, and the glucose transporters SLC2A1 and SLC2A3 did not correspond with decreased mRNA expression. Therefore, PIM kinases are likely required for IL-2 to maximally control protein synthesis in CD8 CTL. Along that line, the translational repressor PDCD4 was increased in Pim dKO CTL and pan-PIM kinase inhibitors caused a reduction in protein synthesis rates in IL-2-expanded CTL. Finally, the differences between Pim dKO and WT CTL in terms of CD62L expression resulted in Pim dKO CTL but not WT CTL retained the capacity to home to secondary lymphoid organs. In conclusion, this thorough and solid study showed that the PIM1/2 kinases shape the effector CD8 T cell proteomes rather than transcriptomes and are important mediators of IL2-signalling and CD8 T cell trafficking.

Weaknesses:

None identified by this reviewer.

Reviewer #2 (Public Review):

Summary:

Using a suite of techniques (e.g., RNA seq, proteomics, and functional experiments ex vivo) this paper extensively focuses on the role of PIM1/2 kinases during CD8 T-cell activation and cytokine-driven (i.e., IL-2 or IL-15) differentiation. The authors' key finding is that PIM1/2 enhances protein synthesis in response to IL-2 stimulation, but not IL-15, in CD8+ T cells. Loss of PIM1/2 made T cells less 'effector-like', with lower granzyme and cytokine production, and a surface profile that maintained homing towards secondary lymphoid tissue. The cytokines the authors focus on are IL-15 and Il-2, which drive naïve CD8 T cells towards memory or effector states, respectively. Although PIM1/2 are upregulated in response to T-cell activation and cytokine stimulation (e.g., IL-15, and to a greater extent, IL-2), using T cells isolated from a global mouse genetic knockout background of PIM1/2, the authors find that PIM1/2 did not significantly influence T-cell activation, proliferation, or expression of anything in the proteome under anti-CD3/CD28 driven activation with/without cytokine (i.e., IL-15) stimulation ex vivo. This is perhaps somewhat surprising given PIM1/2 is upregulated, albeit to a small degree, in response to IL-15, and yet PIM1/2 did not seem to influence CD8+ T cell differentiation towards a memory state. Even more surprising is that IL-15 was previously shown to influence the metabolic programming of intestinal intraepithelial lymphocytes, suggesting cell-type specific effects from PIM kinases. What the authors went on to show, however, is that PIM1/2 KO altered CD8 T cell proteomes in response to IL-2. Using proteomics, they saw increased expression of homing receptors (i.e., L-selectin, CCR7), but reduced expression of metabolism-related proteins (e.g., GLUT1/3 & cholesterol biosynthesis) and effector-function related proteins (e.g., IFNy and granzymes). Rather neatly, by performing both RNA-seq and proteomics on the same IL-2 stimulated WT vs. PIM1/2 KO cells, the authors found that changes at the proteome level were not corroborated by differences in RNA uncovering that PIM1/2 predominantly influence protein synthesis/translation. Effectively, PIM1/2 knockout reduced the differentiation of CD8+ T cells towards an effector state. In vivo adoptive transfer experiments showed that PIM1/2KO cells homed better to secondary lymphoid tissue, presumably owing to their heightened L-selectin expression (although this was not directly examined).

Strengths:

Overall, I think the paper is scientifically good, and I have no major qualms with the paper. The paper as it stands is solid, and while the experimental aim of this paper was quite specific/niche, it is overall a nice addition to our understanding of how serine/threonine kinases impact T cell state, tissue homing, and functionality. Of note, they hint towards a more general finding that kinases may have distinct behaviour in different T-cell subtypes/states. I particularly liked their use of matched RNA-seq and proteomics to first suggest that PIM1/2 kinases may predominantly influence translation (then going on to verify this via their protein translation experiment - although I must add this was only done using PIM kinase inhibitors, not the PIM1/2KO cells). I also liked that they used small molecule inhibitors to acutely reduce PIM1/2 activity, which corroborated some of their mouse knockout findings - this experiment helps resolve any findings resulting from potential adaptation issues from the PIM1/2 global knockout in mice but also gives it a more translational link given the potential use of PIM kinase inhibitors in the clinic. The proteomics and RNA seq dataset may be of general use to the community, particularly for analysis of IL-15 or IL-2 stimulated CD8+ T cells.

Weaknesses:

It would be good to perform some experiments in human T cells too, given the ease of e.g., the small molecule inhibitor experiment. Would also be good for the authors to include a few experiments where PIM1/2 have been transduced back into the PIM1/2 KO T cells, to see if this reverts any differences observed in response to IL-2 - although the reviewer notes that the timeline for altering primary T cells via lentivirus/CRISPR may be on the cusp of being practical such that functional experiments can be performed on day 6 after first stimulating T cells. Other experiments could also look at how PIM1/2 KO influences the differentiation of T cell populations/states during ex vivo stimulation of PBMCs or in vivo infection models using (high-dimensional) flow cytometry (rather than using bulk proteomics/RNA seq which only provide an overview of all cell combined). Alongside this, performing a PCA of bulk RNA seq/proteomes or Untreated vs. IL-2 vs. IL-15 of WT and PIM1/2 knockout T cells would help cement their argument in the discussion about PIM1/2 knockout cells being distinct from a memory phenotype.

Joint Public Review:

Summary:

This paper by Beath et. al. identifies a potential regulatory role for proteins involved in cytoplasmic streaming and maintaining the grouping of paternal organelles: holding sperm contents in the fertilized embryos away from the oocyte meiotic spindle so that they don't get ejected into the polar body during meiotic chromosome segregation. The authors show that by time-lapse video, paternal mitochondria (used as a readout for sperm and its genome) is excluded from yolk granules and maternal mitochondria, even when moving long distances by cytoplasmic streaming. To understand how this exclusion is accomplished, they first show that it is independent of both internal packing and the engulfment of the paternal chromosomes by the maternal endoplasmic reticulum creating an impermeable barrier. They then test whether the control of cytoplasmic steaming affects this exclusion by knocking down two microtubule motors, Katanin and kinesis I. They find that the ER ring, which is used as a proxy for paternal chromosomes, undergoes extensive displacement with these treatments during anaphase I and interacts with the meiotic spindle, supporting their hypothesis that the exclusion of paternal chromosomes is regulated by cytoplasmic streaming. Next, they test whether a regulator of maternal ER organization, ATX-2, disrupts sperm organization so that they can combine the double depletion of ATX-2 and KLP-7, presumably because klp-7 RNAi (unlike mei-1 RNAi) does not affect polar body extrusion and they can report on what happens to paternal chromosomes. They find that the knockdown of both ATX-2 and KLP-7 produces a higher incidence of what appears to be the capture of paternal chromosomes by the meiotic spindle (5/24 vs 1/25). However, this capture event appears to halt the cell cycle, preventing the authors from directly observing whether this would result in the paternal chromosomes being ejected into the polar body.

The authors addressed the vast majority of the Reviewer's comments including the addition of new figures, re-wording of data interpretation and discussion points to better reflect the claims of the paper. There remain a few outstanding points which were not addressed.

In many cases the number of embryos analyzed or events capture remains low and the authors conclude that these sample sizes prevented statistical significance. It's not clear if more embryos were analyzed or if more capture would lead to statistical significance. Language capturing this caveat should also be included in the manuscript. A specific example of this is given below:

In the double knockdown of ATX-2 and KLP-7, there was no significant difference between single and double knockdowns and the ER ring displacement was not analyzed in this double mutant. Further, there was no difference in the frequency of sperm capture between single and double ATX-2 and KLP-7 due to low sample size, the the strength of the conclusion of this manuscript would be greatly improved if both of these results were further explored.

Reviewer #2 (Public Review):

Summary:<br /> The authors used four datasets spanning 30 countries to examine funding success and research quality score for various disciplines. They examined whether funding or research quality score were influenced by majority gender of the discipline and whether these affected men, women, or both within each discipline. They found that disciplines dominated by women have lower funding success and research quality score than disciplines dominated by men. These findings are surprising because even the men in women-dominated fields experienced lower funding success and research quality score.

Strengths:<br /> - The authors utilized a comprehensive dataset covering 30 countries to explore the influence of the majority gender in academic disciplines on funding success and research quality scores.<br /> - Findings suggest a systemic issue where disciplines with a higher proportion of women have lower evaluations and funding success for all researchers, regardless of gender.<br /> - The manuscript is notable for its large sample size and the diverse international scope, enhancing the generalizability of the results.<br /> - The work accounts for various factors including age, number of research outputs, and bibliometric measures, strengthening the validity of the findings.<br /> - The manuscript raises important questions about unconscious bias in research evaluation and funding decisions, as evidenced by lower scores in women-dominated fields even for researchers that are men.<br /> - The study provides a nuanced view of gender bias, showing that it is not limited to individuals but extends to entire disciplines, impacting the perception and funding and quality or worth of research.<br /> - This work underscores the need to explore motivations behind gender distribution across fields, hinting at deep-rooted societal and institutional barriers.<br /> - The authors have opened a discussion on potential solutions to counter bias, like adjusting funding paylines or anonymizing applications, or other practical solutions.<br /> - While pointing out limitations such as the absence of data from major research-producing countries, the manuscript paves the way for future studies to examine whether its findings are universally applicable.<br /> - The study carefully uses the existing data (including PBRF funding panel gender diversity) to examine gender bias. These types of datasets are often not readily accessible for analysis. Here, the authors have used the available data to the fullest extent possible.

The authors have addressed the concerns I had about the original version.

Reviewer #3 (Public Review):<br /> This study seeks to investigate one aspect of disparity in academia: how gender balance in a discipline is valued in terms of evaluated research quality score and funding success. This is important in understanding disparities within academia.<br /> This study uses publicly available data to investigate covariation between gender balance in an academic discipline and:<br /> individual research quality scores of New Zealand academics as evaluated by one of 14 broader subject panels.<br /> [ii] funding success in Australia, Canada, Europe, UK.

The authors have addressed the concerns I had about the original version

Reviewer #1 (Public Review):

Summary: The authors present a close to complete annotation of the male Drosophila ventral nerve cord, a critical part of the fly's central nervous system.

Strengths: The manuscript describes an enormous amount of work that takes the first steps towards presenting and comprehending the complexity and organization of the ventral nerve cord. The analysis is thorough and complete. It also makes the effort to connect this EM-centric view of the nervous system to more classical analyses, such as the previously defined hemilineages, that also describe the organization of the fly nervous system. There are many, many insights that come from this work that will be valuable to the field for the foreseeable future.

Weaknesses: With more than 60 primary figures, the paper is overwhelming and cannot be read and digested in a single sitting. The result is more like a detailed resource rather than a typical research paper.

Reviewer #2 (Public Review):

Summary and strengths:<br /> This massive paper describes the identity and connectivity of neurons reconstructed from a volumetric EM image volume of the ventral nerve cord (VNC) of a male fruit fly. The segmentation of the EM data was described in one companion paper; the classification of the neurons entering the VNC from the brain (descending neurons or DNs) and the motor neurons leaving the VNC was described in a second companion paper. Here, the authors describe a system for annotating the remaining neurons in the VNC, which include intrinsic neurons, ascending neurons, and sensory neurons, representing the vast majority of neurons in the dataset. Another fundamental contribution of this paper is the identification of the developmental origins (hemilineage) of each intrinsic neuron in the VNC. These comprehensive hemilineage annotations can be used to understand the relationship between development and circuit structure, provide insight into neurotransmitter identity, and facilitate comparisons across insect species.Many sensory neurons are also annotated by comparison to past literature. Overall, defining and applying this annotation system provides the field with a standard nomenclature and resource for future studies of VNC anatomy, connectivity, and development. This is a monumental effort that will fundamentally transform the field of Drosophila neuroscience and provide a roadmap for similar connectomic studies in other organisms.

Weaknesses:<br /> Despite the significant merit of these contributions, the manuscript is challenging to read and comprehend. In some places, it seems to be attempting to comprehensively document everything the authors found in this immense dataset. In other places, there are gaps in scholarship and analysis. As it is currently constructed, I worry that the manuscript will intimidate general readers looking for an entry point to the system, and ostracize specialized readers who are unable to use the paper as a comprehensive reference due to its confusing organization.

The bulk of the 559 pages of the submitted paper is taken up by a set of dashboard figures for each of ~40 hemilineages. Formatting the paper as an eLife publication will certainly help condense these supplemental figures into a more manageable format, but 68 primary figures will remain, and many of these also lack quality and clarity. Without articulating a clear function for each plot, it is hard to know what the authors missed or chose not to show. As an example, many of the axis labels indicate the hemilineage of a group of neurons, but are ordered haphazardly and so small as to be illegible; if the hemilineage name is too small, and in a bespoke order for that data, then is the reader meant to ignore the specific hemilineage labels?

The text has similar problems of emphasis. It is often meandering and repetitive. Overlapping information is found in multiple places, which causes the paper to be much longer than it needs to be. For example, the concept of hemilineages is introduced three times before the subtitle "Introduction to hemilineage-based organisation". When cell typing is introduced, it is unclear how this relates to serial motif, hemilineage, etc; "Secondary hemilineages" follow the Cell typing title. Like the overwhelming number of graphical elements, this gives the impression that little attention has been paid to curating and editing the text. It is unclear whether the authors intend for the paper to be read linearly or used as a reference. In addition, descriptions of the naming system are often followed by extensive caveats and exceptions, giving the impression that the system is not airtight and possibly fluid. At many points, the text vacillates between careful consideration of the dataset's limitations and overly grandiose claims. These presentation flaws overshadow the paper's fundamental contribution of describing a reasonable and useful cell-typing system and placing intrinsic neurons within this framework.

References to past Drosophila literature are inconsistent and references to work from other insects are generally not included; for example, the extensive past work on leg sensory neurons in locusts, cockroaches, and stick insects. Such omissions are understandable in a situation where brevity is paramount. However, this paper adopts a comprehensive and authoritative tone that gives the reader an impression of completeness that does not hold up under careful scrutiny.

The paper accompanies the release of the MANC dataset (EM images, segmentation, annotations) through a web browser-based tool: clio.janelia.org. The paper would be improved by distilling it down to its core elements, and then encouraging readers to explore the dataset through this interactive interface. Streamlining the paper by removing extraneous and incomplete analyses would provide the reader with a conceptual or practical framework on which to base their own queries of the connectome.

Reviewer #1 (Public Review):

This study generated 3D cell constructs from endometrial cell mixtures that were seeded in the Matrigel scaffold. The cell assemblies were treated with hormones to induce a "window of implantation" (WOI) state.

The authors did their best to revise their study according to the reviewers' comments. However, the study remains unconvincing and at the same time too dense and not focused enough.

(1) The use of the term organoids is still confusing and should be avoided. Organoids are epithelial tissue-resembling structures. Hence, the multiple-cell aggregates developed here are rather "co-culture models" (or "assembloids"). It is still unexpected (unlikely) that these structures containing epithelial, stromal and immune cells can be robustly passaged in the epithelial growth conditions used. All other research groups developing real organoids from endometrium have shown that only the epithelial compartment remains in culture at passaging (while the stromal compartment is lost). If authors keep to their idea, they should perform scRNA-seq on both early and late (passage 6-10) "organoids". And they should provide details of culturing/passaging/plating etc that are different with other groups and might explain why they keep stromal and immune cells in their culture for such a long time. In other words, they should then in detail compare their method to the standard method of all other researchers in the field, and show the differences in survival and growth of the stromal and immune cells.<br /> (2) The paper is still much too dense, touching upon all kind of conclusions from the manifold bioinformatic analyses. The latter should be much clearer and better described, and then some interesting findings (pathways/genes) should be highlighted without mentioning every single aspect that is observed. The paper needs a lot of editing to better focus and extract take-home messages, not bombing the reader with a mass of pathways, genes etc which makes the manuscript just not readable or 'digest-able'. There is no explanation whatever and no clear rationale why certain genes are included in a list while others are not. There is the impression that mass bioinformatics is applied without enough focus.<br /> (3) The study is much too descriptive and does not show functional validation or exploration (except glycogen production). Some interesting findings extracted from the bioinformatics must be functionally tested.<br /> (4) In contrast to what was found in vivo (Wang et al. 2020), no abrupt change in gene expression pattern is mentioned here from the (early-)secretory to the WoI phase. Should be discussed. Although the bioinformatic analyses point into this direction, there are major concerns which must be solved before the study can provide the needed reliability and credibility for revision.<br /> (5) All data should be benchmarked to the Wang et al 2020 and Garcia-Alonso et al. 2021 papers reporting very detailed scRNA-seq data, and not only the Stephen R. Quake 2020 paper.<br /> (6) Fig. 2B: Vimentin staining is not at all clear. F-actin could be used to show the typical morphology of the stromal cells?<br /> (7) Where does the term "EMT-derived stromal cells" come from? On what basis has this term been coined?<br /> (8) CD44 is shown in Fig. 2D but the text mentions CD45 (line 159)?<br /> (9) All quantification experiments (of stainings etc) should be in detail described how this was done. It looks very difficult (almost not feasible) when looking at the provided pictures to count the stained cells.<br /> (10) Fig. 3C: it is unclear how quantification can be reliably done. Moreover, OLFM4 looks positive in all cells of Ctrl, but authors still see an increase?<br /> (11) Fig. 3F: Met is downregulated which is not in accordance with the mentioned activation of the PI3K-AKT pathway.<br /> (12) Lines 222-226: transcriptome and proteome differences are not significant; so, how meaningful are the results then? Then, it is very hard to conclude an evolution from secretory phase to WoI.<br /> (13) WoI organoids show an increased number of cilia. However, some literature shows the opposite, i.e. less ciliated cells in the endometrial lining at WoI (to keep the embryo in place). How to reconcile?<br /> (14) How are pinopodes distinguished from microvilli? Moreover, Fig. 3 does not show the typical EM structure of cilia.<br /> (15) There is a recently published paper demonstrating another model for implantation. This paper should be referenced as well (Shibata et al. Science Advances, 2024).<br /> (16) Line 78: two groups were the first here (Turco and Borreto) and should both be mentioned.<br /> (17) Line 554: "as an alternative platform" - alternative to what? Authors answer reviewers' comments by just changing one word, but this makes the text odd.

Reviewer #2 (Public Review):

In this research, Zhang et al. have pioneered the creation of an advanced organoid culture designed to emulate the intricate characteristics of endometrial tissue during the crucial Window of Implantation (WOI) phase. Their method involves the incorporation of three distinct hormones into the organoid culture, coupled with additives that replicate the dynamics of the menstrual cycle. Through a series of assays, they underscore the striking parallels between the endometrial tissue present during the WOI and their crafted organoids. Through a comparative analysis involving historical endometrial tissue data and control organoids, they establish a system that exhibits a capacity to simulate the intricate nuances of the WOI.

The authors made a commendable effort to address the majority of the statements. Developing an endometrial organoid culture methodology that mimics the window of implantation is a game-changer for studying the implantation process. However, the authors should strive to enhance the results to demonstrate how different WOI organoids are from SEC organoids, ensuring whether they are worth using in implantation studies, or a proper demonstration using implantation experiments.

Reviewer #1 (Public Review):

Summary:

In this manuscript, the authors conducted an important study that explored an innovative regenerative treatment for pediatric craniofacial bone loss, with a particular focus on investigating the impacts of JAGGED1 (JAG1) signaling.

Strengths:

Building on their prior research involving the effect of JAG1 on murine cranial neural crest cells, the authors demonstrated successful bone regeneration in an in vivo murine bone loss model with a critically-sized cranial defect, where they delivered JAG1 with pediatric human bone-derived osteoblast-like cells in the hydrogel. Additionally, their findings unveiled a crucial mechanism wherein JAG1 induces pediatric osteoblast commitment and bone regeneration through the phosphorylation of p70 S6K. This discovery offers a promising avenue for potential treatment, involving targeted delivery of JAG1 and activation of downstream p70 s6K, for pediatric craniofacial bone loss. Overall, the experimental design is appropriate, and the results are clearly presented.

Reviewer #2 (Public Review):

The current manuscript undoubtedly demonstrates that JAG1 can induced osteogenesis via non-canonical signaling. In fact, using the mouse-calvarial critical defect model, the authors have clearly shown the anabolic regenerative effect of JAG1 in via non-canonical pathways. Exploring the molecular mechanisms, the authors have shown that non-canonically JAG1 is regulating multiple pathways including STAT5, AKT, P38, JNK, NF-ĸB, and p70 S6K, which together possibly culminate to the activation of p70 S6K. In summary these findings have significant implications in designing new approaches for bone regenerative research.

Reviewer #1 (Public Review):

Summary:

In this paper, proteomics analysis of the plasma of human subjects that underwent an exercise training regime consisting of a combination of endurance and resistance exercise led to the identification of several proteins that were responsive to exercise training. Confirming previous studies, many exercise-responsive secreted proteins were found to be involved in the extra-cellular matrix. The protein CD300LG was singled out as a potential novel exercise biomarker and the subject of numerous follow-up analyses. The levels of CD300LG were correlated with insulin sensitivity. The analysis of various open-source datasets led to the tentative suggestion that CD300LG might be connected with angiogenesis, liver fat, and insulin sensitivity. CD300LG was found to be most highly expressed in subcutaneous adipose tissue and specifically in venular endothelial cells. In a subset of subjects from the UK Biobank, serum CD300LG levels were positively associated with several measures of physical activity - particularly vigorous activity. In addition, serum CD300LG levels were negatively associated with glucose levels and type 2 diabetes. Genetic studies hinted at these associations possibly being causal. Mice carrying alterations in the CD300LG gene displayed impaired glucose tolerance, but no change in fasting glucose and insulin. Whether the production of CD300LG is changed in the mutant mice is unclear.

Strengths:

The specific proteomics approach conducted to identify novel proteins impacted by exercise training is new. The authors are resourceful in the exploitation of existing datasets to gain additional information on CD300LG.

Weaknesses:

While the analyses of multiple open-source datasets are necessary and useful, they lead to relatively unspecific correlative data that collectively insufficiently advance our knowledge of CD300LG and merely represent the starting point for more detailed investigations. Additional more targeted experiments of CD300LG are necessary to gain a better understanding of the role of CD300LG and the mechanism by which exercise training may influence CD300LG levels. One should also be careful to rely on external data for such delicate experiments as mouse phenotyping. Can the authors vouch for the quality of the data collected?

Reviewer #2 (Public Review):

Summary:

This manuscript from Lee-Odegard et al reports proteomic profiling of exercise plasma in humans, leading to the discovery of CD300LG as a secreted exercise-inducible plasma protein. Correlational studies show associations of CD300LG with glycemic traits. Lastly, the authors query available public data from CD300LG-KO mice to establish a causal role for CD300LG as a potential link between exercise and glucose metabolism. However, the strengths of this manuscript were balanced by the moderate to major weaknesses. Therefore in my opinion, while this is an interesting study, the conclusions remain preliminary and are not fully supported by the experiments shown so far.

Strengths:

(1) Data from a well-phenotyped human cohort showing exercise-inducible increases in CD300LG.

(2) Associations between CD300LG and glucose and other cardiometabolic traits in humans, that have not previously been reported.

(3) Correlation to CD300LG mRNA levels in adipose provides additional evidence for exercise-inducible increases in CD300LG.

Weaknesses:

(1) CD300LG is by sequence a single-pass transmembrane protein that is exclusively localized to the plasma membrane. How CD300LG can be secreted remains a mystery. More evidence should be provided to understand the molecular nature of circulating CD300LG. Is it full-length? Is there a cleaved fragment? Where is the epitope where the o-link is binding to CD300LG? Does transfection of CD300LG to cells in vitro result in secreted CD300LG?

(2) There is a growing recognition of specificity issues with both the O-link and somalogic platforms. Therefore it is critical that the authors use antibodies, targeted mass spectrometry, or some other methods to validate that CD300LG really is increased instead of just relying on the O-link data.

(3) It is insufficient simply to query the IMPC phenotyping data for CD300LG; the authors should obtain the animals and reproduce or determine the glucose phenotypes in their own hands. In addition, this would allow the investigators to answer key questions like the phenotype of these animals after a GTT, whether glucose production or glucose uptake is affected, whether insulin secretion in response to glucose is normal, effects of high-fat diet, and other standard mouse metabolic phenotyping assays.

(4) I was unable to find the time point at which plasma was collected at the 12-week time point. Was it immediately after the last bout of exercise (an acute response) or after some time after the training protocol (trained state)?

Reviewer #3 (Public Review):

In multiple cancers, the key roles of B cells are emerging in the tumor microenvironment (TME). The authors of this study appropriately introduce that B cells are relatively under-characterised in the TME and argue correctly that it is not known how the B cell receptor (BCR) repertoires across tumor, lymph node and peripheral blood relate. The authors therefore supply a potentially useful study evaluating the tumor, lymph node and peripheral blood BCR repertoires and site-to-site as well as intra-site relationships. The authors employ sophisticated analysis techniques, although the description of the methods is incomplete.

Major strengths:

(1) The authors provide a unique analysis of BCR repertoires across tumor, dLN, and peripheral blood. The work provides useful insights into inter- and intra-site BCR repertoire heterogeneity. While patient-to-patient variation is expected, the findings with regard to intra-tumor and intra-dLN heterogeneity with the use of fragments from the same tissue are of importance, contribute to the understanding of the TME, and will inform future study design.

(2) A particular strength of the study is the detailed CDR3 physicochemical properties analysis which leads the authors to observations that suggest a less-specific BCR repertoire of TIL-B compared to circulating B cells.

Concerns and comments on current version:

The revision has improved the manuscript but, in my opinion, remains inadequate. While most of my requested changes have been made, I do not see an expansion of Fig1A legend to incorporate more details about the analysis. Lacking details of methodology was a concern from all reviewers. Similarly, the 'fragmented' narrative was a concern of all reviewers. These matters have not been dealt with adequately enough - there are parts of the manuscript which remain fragmented and confusing. The narrative and analysis does not explain how the plasma cell bias has been dealt with adequately and in fact is simply just confusing. There is a paragraph at the beginning of the discussion re the plasma cell bias, which should be re-written to be clearer and moved to have a prominent place early in the results. Why are these results not properly presented? They are key for interpretation of the manuscript. Furthermore, the sorted plasma cell sequencing analysis also has only been performed on two patients. Another issue is that some disease cohorts are entirely composed of patients with metastasis, some without but metastasis is not mentioned. Metastasis has been shown to impact the immune landscape.

A reviewer brought up a concern about the overlap analysis and I also asked for an explanation on why this F2 metric chosen. Part of the rebuttal argues that another metric was explored showing similar results, thus conclusion reached is reasonable. Remarkably, these data are not only omitted from the manuscript, but is not even provided for the reviewers.

This manuscript certainly includes some interesting and useful work. Unfortunately, a comprehensive re-write was required to make the work much clearer and easier to understand and this has not been realised.

Reviewer #1 (Public Review):

Summary:

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

Strengths:

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

Weaknesses:

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

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

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

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

(5) This manuscript proposes a new method of 2D neural culture. However, the description and representation of the method are currently insufficient.<br /> (a) The results section would benefit from a clear and concise, but step-by-step overview of the protocol. The current description refers to an earlier paper and appears to skip over some key steps. This section would benefit from being completely rewritten. This is not a replacement for a clear methods section, but a section that allows readers to clearly interpret results presented later.<br /> (b) Along the same lines, the graphical abstract should be much more detailed. It should contain the time frames and the media used at the different stages of the protocol, seeding numbers, etc.

Reviewer #2 (Public Review):

Summary:

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

Strengths:

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

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

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

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

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

Weaknesses:

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

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

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

Reviewer #3 (Public Review):

Summary:

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

Strengths:

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

Weaknesses:

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

Reviewer #2 (Public Review):

Summary:

The manuscript by Kelbert et al. presents results on the involvement of the yeast transcription factor Sfp1 in the stabilisation of transcripts whose synthesis it stimulates. Sfp1 is known to affect the synthesis of a number of important cellular transcripts, such as many of those that code for ribosomal proteins. The hypothesis that a transcription factor can remain bound to the nascent transcript and affect its cytoplasmic half-life is attractive. However, the association of Sfp1 with cytoplasmic transcripts remains to be validated, as explained in the following comments:

A two-hybrid based assay for protein-protein interactions identified Sfp1, a transcription factor known for its effects on ribosomal protein gene expression, as interacting with Rpb4, a subunit of RNA polymerase II. Classical two-hybrid experiments depend on the presence of the tested proteins in the nucleus of yeast cells, suggesting that the observed interaction occurs in the nucleus. Unfortunately, the two-hybrid method cannot determine whether the interaction is direct or mediated by nucleic acids. The revised version of the manuscript now states that the observed interaction could be indirect.

To understand to which RNA Sfp1 might bind, the authors used an N-terminally tagged fusion protein in a cross-linking and purification experiment. This method identified 264 transcripts for which the CRAC signal was considered positive and which mostly correspond to abundant mRNAs, including 74 ribosomal protein mRNAs or metabolic enzyme-abundant mRNAs such as PGK1. The authors did not provide evidence for the specificity of the observed CRAC signal, in particular what would be the background of a similar experiment performed without UV cross-linking. This is crucial, as Figure S2G shows very localized and sharp peaks for the CRAC signal, often associated with over-amplification of weak signal during sequencing library preparation.

In a validation experiment, the presence of several mRNAs in a purified SFP1 fraction was measured at levels that reflect the relative levels of RNA in a total RNA extract. Negative controls showing that abundant mRNAs not found in the CRAC experiment were clearly depleted from the purified fraction with Sfp1 would be crucial to assess the specificity of the observed protein-RNA interactions (to complement Fig. 2D). The CRAC-selected mRNAs were enriched for genes whose expression was previously shown to be upregulated upon Sfp1 overexpression (Albert et al., 2019). The presence of unspliced RPL30 pre-mRNA in the Sfp1 purification was interpreted as a sign of co-transcriptional assembly of Sfp1 into mRNA, but in the absence of valid negative controls, this hypothesis would require further experimental validation. Also, whether the fraction of mRNA bound by Sfp1 is nuclear or cytoplasmic is unclear.

To address the important question of whether co-transcriptional assembly of Spf1 with transcripts could alter their stability, the authors first used a reporter system in which the RPL30 transcription unit is transferred to vectors under different transcriptional contexts, as previously described by the Choder laboratory (Bregman et al. 2011). While RPL30 expressed under an ACT1 promoter was barely detectable, the highest levels of RNA were observed in the context of the native upstream RPL30 sequence when Rap1 binding sites were also present. Sfp1 showed better association with reporter mRNAs containing Rap1 binding sites in the promoter region. Removal of the Rap1 binding sites from the reporter vector also led to a drastic decrease in reporter mRNA levels. Co-purification of reporter RNA with Sfp1 was only observed when Rap1 binding sites were included in the reporter. Negative controls for all the purification experiments might be useful.

To complement the biochemical data presented in the first part of the manuscript, the authors turned to the deletion or rapid depletion of SFP1 and used labelling experiments to assess changes in the rate of synthesis, abundance and decay of mRNAs under these conditions. An important observation was that in the absence of Sfp1, mRNAs encoding ribosomal protein genes not only had a reduced synthesis rate, but also an increased degradation rate. This important observation needs careful validation, as genomic run-on experiments were used to measure half-lives, and this particular method was found to give results that correlated poorly with other measures of half-life in yeast (e.g. Chappelboim et al., 2022 for a comparison). As an additional validation, a temperature shift to 42{degree sign}C was used to show that , for specific ribosomal protein mRNA, the degradation was faster, assuming that transcription stops at that temperature. It would be important to cite and discuss the work from the Tollervey laboratory showing that a temperature shift to 42{degree sign}C leads to a strong and specific decrease in ribosomal protein mRNA levels, probably through an accelerated RNA degradation (Bresson et al., Mol Cell 2020, e.g. Fig 5E). Finally, the conclusion that mRNA deadenylation rate is altered in the absence of Sfp1, is difficult to assess from the presented results (Fig. 3D).

The effects of SFP1 on transcription were investigated by chromatin purification with Rpb3, a subunit of RNA polymerase, and the results were compared with synthesis rates determined by genomic run-on experiments. The decrease in polII presence on transcripts in the absence of SFP1 was not accompanied by a marked decrease in transcript output, suggesting an effect of Sfp1 in ensuring robust transcription and avoiding RNA polymerase backtracking. To further investigate the phenotypes associated with the depletion or absence of Sfp1, the authors examined the presence of Rpb4 along transcription units compared to Rpb3. An effect of spf1 deficiency was that this ratio, which decreased from the start of transcription towards the end of transcripts, increased slightly. To what extent this result is important for the main message of the manuscript is unclear.

Suggestions: a) please clearly indicate in the figures when they correspond to reanalyses of published results. b) In table S2, it would be important to mention what the results represent and what statistics were used for the selection of "positive" hits.

Strengths:

- Diversity of experimental approaches used.<br /> - Validation of large-scale results with appropriate reporters.

Weaknesses:

- Lack of controls for the CRAC results and lack of negative controls for the co-purification experiments that were used to validate specific mRNA targets potentially bound by Sfp1.<br /> - Several conclusions are derived from complex correlative analyses that fully depend on the validity of the aforementioned Sfp1-mRNA interactions.

Reviewer #1 (Public Review):

This work seeks to understand how behaviour-related information is represented in the neural activity of the primate motor cortex. To this end, a statistical model of neural activity is presented that enables a non-linear separation of behaviour-related from unrelated activity. As a generative model, it enables the separate analysis of these two activity modes, here primarily done by assessing the decoding performance of hand movements the monkeys perform in the experiments. Several lines of analysis are presented to show that while the neurons with significant tuning to movements strongly contribute to the behaviourally-relevant activity subspace, less or un-tuned neurons also carry decodable information. It is further shown that the discovered subspaces enable linear decoding, leading the authors to conclude that motor cortex read-out can be linear.

Strengths:

In my opinion, using an expressive generative model to analyse neural state spaces is an interesting approach to understand neural population coding. While potentially sacrificing interpretability, this approach allows capturing both redundancies and synergies in the code as done in this paper. The model presented here is a natural non-linear extension of a previous linear model PSID) and uses weak supervision in a manner similar to a previous non-linear model (TNDM).

Weaknesses:

This revised version provides additional evidence to support the author's claims regarding model performance and interpretation of the structure of the resulting latent spaces, in particular the distributed neural code over the whole recorded population, not just the well-tuned neurons. The improved ability to linearly decode behaviour from the relevant subspace and the analysis of the linear subspace projections in my opinion convincingly demonstrates that the model picks up behaviour-relevant dynamics, and that these are distributed widely across the population. As reviewer 3 also points out, I would, however, caution to interpret this as evidence for linear read-out of the motor system - your model performs a non-linear transformation, and while this is indeed linearly decodable, the motor system would need to do something similar first to achieve the same. In fact to me it seems to show the opposite, that behaviour-related information may not be generally accessible to linear decoders (including to down-stream brain areas).

As in my initial review, I would also caution against making strong claims about identifiability although this work and TNDM seem to show that in practise such methods work quite well. CEBRA, in contrast, offers some theoretical guarantees, but it is not a generative model, so would not allow the type of analysis done in this paper. In your model there is a para,eter \alpha to balance between neural and behaviour reconstruction. This seems very similar to TNDM and has to be optimised - if this is correct, then there is manual intervention required to identify a good model.

Somewhat related, I also found that the now comprehensive comparison with related models shows that the using decoding performance (R2) as a metric for model comparison may be problematic: the R2 values reported in Figure 2 (e.g. the MC_RTT dataset) should be compared to the values reported in the neural latent benchmark, which represent well-tuned models (e.g. AutoLFADS). The numbers (difficult to see, a table with numbers in the appendix would be useful, see: https://eval.ai/web/challenges/challenge-page/1256/leaderboard) seem lower than what can be obtained with models without latent space disentanglement. While this does not necessarily invalidate the conclusions drawn here, it shows that decoding performance can depend on a variety of model choices, and may not be ideal to discriminate between models. I'm also surprised by the low neural R2 for LFADS I assume this is condition-averaged) - LFADS tends to perform very well on this metric.

One statement I still cannot follow is how the prior of the variational distribution is modelled. You say you depart from the usual Gaussian prior, but equation 7 seems to suggest there is a normal prior. Are the parameters of this distribution learned? As I pointed out earlier, I however suspect this may not matter much as you give the prior a very low weight. I also still am not sure how you generate a sample from the variational distribution, do you just draw one for each pass?

Summary:

This paper presents a very interesting analysis, but some concerns remain that mainly stem from the complexity of deep learning models. It would be good to acknowledge these as readers without relevant background need to understand where the possible caveats are.

Reviewer #2 (Public Review):

Li et al present a method to extract "behaviorally relevant" signals from neural activity. The method is meant to solve a problem which likely has high utility for neuroscience researchers. There are numerous existing methods to achieve this goal some of which the authors compare their method to-thankfully, the revised version includes one of the major previous omissions (TNDM). However, I still believe that d-VAE is a promising approach that has its own advantages. Still, I have issues with the paper as-is. The authors have made relatively few modifications to the text based on my previous comments, and the responses have largely just dismissed my feedback and restated claims from the paper. Nearly all of my previous comments remain relevant for this revised manuscript. As such, they have done little to assuage my concerns, the most important of which I will restate here using the labels/notation (Q1, Q2, etc) from the reviewer response.

(Q1) I still remain unconvinced that the core findings of the paper are "unexpected". In the response to my previous Specific Comment #1, they say "We use the term 'unexpected' due to the disparity between our findings and the prior understanding concerning neural encoding and decoding." However, they provide no citations or grounding for why they make those claims. What prior understanding makes it unexpected that encoding is more complex than decoding given the entropy, sparseness, and high dimensionality of neural signals (the "encoding") compared to the smoothness and low dimensionality of typical behavioural signals (the "decoding")?

(Q2) I still take issue with the premise that signals in the brain are "irrelevant" simply because they do not correlate with a fixed temporal lag with a particular behavioural feature hand-chosen by the experimenter. In the response to my previous review, the authors say "we employ terms like 'behaviorally-relevant' and 'behaviorally-irrelevant' only regarding behavioral variables of interest measured within a given task, such as arm kinematics during a motor control task.". This is just a restatement of their definition, not a response to my concern, and does not address my concern that the method requires a fixed temporal lag and continual decoding/encoding. My example of reward signals remains. There is a huge body of literature dating back to the 70s on the linear relationships between neural and activity and arm kinematics; in a sense, the authors have chosen the "variable of interest" that proves their point. This all ties back to the previous comment: this is mostly expected, not unexpected, when relating apparently-stochastic, discrete action potential events to smoothly varying limb kinematics.

(Q5) The authors seem to have missed the spirit of my critique: to say "linear readout is performed in motor cortex" is an over-interpretation of what their model can show.

(Q7) Agreeing with my critique is not sufficient; please provide the data or simulations that provides the context for the reference in the fano factor. I believe my critique is still valid.

(Q8) Thank you for comparing to TNDM, it's a useful benchmark.

Reviewer #4 (Public Review):

I am a new reviewer for this manuscript, which has been reviewed before. The authors provide a variational autoencoder that has three objectives in the loss: linear reconstruction of behavior from embeddings, reconstruction of neural data, and KL divergence term related to the variational model elements. They take the output of the VAE as the "behaviorally relevant" part of neural data and call the residual "behaviorally irrelevant". Results aim to inspect the linear versus nonlinear behavior decoding using the original raw neural data versus the inferred behaviorally relevant and irrelevant parts of the signal.

Overall, studying neural computations that are behaviorally relevant or not is an important problem, which several previous studies have explored (for example PSID in (Sani et al. 2021), TNDM in (Hurwitz et al. 2021), TAME-GP in (Balzani et al. 2023), pi-VAE in (Zhou and Wei 2020), and dPCA in (Kobak et al. 2016), etc). However, this manuscript does not properly put their work in the context of such prior works. For example, the abstract states "One solution is to accurately separate behaviorally-relevant and irrelevant signals, but this approach remains elusive", which is not the case given that these prior works have done that. The same is true for various claims in the main text, for example "Furthermore, we found that the dimensionality of primary subspace of raw signals (26, 64, and 45 for datasets A, B, and C) is significantly higher than that of behaviorally-relevant signals (7, 13, and 9), indicating that using raw signals to estimate the neural dimensionality of behaviors leads to an overestimation" (line 321). This finding was presented in (Sani et al. 2021) and (Hurwitz et al. 2021), which is not clarified here. This issue of putting the work in context has been brought up by other reviewers previously but seems to remain largely unaddressed. The introduction is inaccurate also in that it mixes up methods that were designed for separation of behaviorally relevant information with those that are unsupervised and do not aim to do so (e.g., LFADS). The introduction should be significantly revised to explicitly discuss prior models/works that specifically formulated this behavior separation and what these prior studies found, and how this study differs.

Beyond the above, some of the main claims/conclusions made by the manuscript are not properly supported by the analyses and results, which has also been brought up by other reviewers but not fully addressed. First, the analyses here do not support the linear readout from the motor cortex because i) by construction, the VAE here is trained to have a linear readout from its embedding in its loss, which can bias its outputs toward doing well with a linear decoder/readout, and ii) the overall mapping from neural data to behavior includes both the VAE and the linear readout and thus is always nonlinear (even when a linear Kalman filter is used for decoding). This claim is also vague as there is no definition of readout from "motor cortex" or what it means. Why is the readout from the bottleneck of this particular VAE the readout of motor cortex? Second, other claims about properties of individual neurons are also confounded because the VAE is a population-level model that extracts the bottleneck from all neurons. Thus, information can leak from any set of neurons to other sets of neurons during the inference of behaviorally relevant parts of signals. Overall, the results do not convincingly support the claims, and thus the claims should be carefully revised and significantly tempered to avoid misinterpretation by readers.

Below I briefly expand on these as well as other issues, and provide suggestions:

(1) Claims about linearity of "motor cortex" readout are not supported by results yet stated even in the abstract. Instead, what the results support is that for decoding behavior from the output of the dVAE model -- that is trained specifically to have a linear behavior readout from its embedding -- a nonlinear readout does not help. This result can be biased by the very construction of the dVAE's loss that encourages a linear readout/decoding from embeddings and thus does not imply a finding about motor cortex.

(2) Related to the above, it is unclear what the manuscript means by readout from motor cortex. A clearer definition of "readout" (a mapping from what to what?) in general is needed. The mapping that the linearity/nonlinearity claims refer to is from the *inferred* behaviorally relevant neural signals, which themselves are inferred nonlinearly using the VAE. This should be explicitly clarified in all claims, i.e., that only the mapping from distilled signals to behavior is linear, not the whole mapping from neural data to behavior. Again, to say the readout from motor cortex is linear is not supported, including in the abstract.

(3) Claims about individual neurons are also confounded. The d-VAE distilling processing is a population level embedding so the individual distilled neurons are not obtainable on their own without using the population data. This population level approach also raises the possibility that information can leak from one neuron to another during distillation, which is indeed what the authors hope would recover true information about individual neurons that wasn't there in the recording (the pixel denoising example). The authors acknowledge the possibility that information could leak to a neuron that didn't truly have that information and try to rule it out to some extent with some simulations and by comparing the distilled behaviorally relevant signals to the original neural signals. But ultimately, the distilled signals are different enough from the original signals to substantially improve decoding of low information neurons, and one cannot be sure if all of the information in distilled signals from any individual neuron truly belongs to that neuron. It is still quite likely that some of the improved behavior prediction of the distilled version of low-information neurons is due to leakage of behaviorally relevant information from other neurons, not the former's inherent behavioral information. This should be explicitly acknowledged in the manuscript.

(4) Given the nuances involved in appropriate comparisons across methods and since two of the datasets are public, the authors should provide their complete code (not just the dVAE method code), including the code for data loading, data preprocessing, model fitting and model evaluation for all methods and public datasets. This will alleviate concerns and allow readers to confirm conclusions (e.g., figure 2) for themselves down the line.

(5) Related to 1) above, the authors should explore the results if the affine network h(.) (from embedding to behavior) was replaced with a nonlinear ANN. Perhaps linear decoders would no longer be as close to nonlinear decoders. Regardless, the claim of linearity should be revised as described in 1) and 2) above, and all caveats should be discussed.

(6) The beginning of the section on the "smaller R2 neurons" should clearly define what R2 is being discussed. Based on the response to previous reviewers, this R2 "signifies the proportion of neuronal activity variance explained by the linear encoding model, calculated using raw signals". This should be mentioned and made clear in the main text whenever this R2 is referred to.

(7) Various terms require clear definitions. The authors sometimes use vague terminology (e.g., "useless") without a clear definition. Similarly, discussions regarding dimensionality could benefit from more precise definitions. How is neural dimensionality defined? For example, how is "neural dimensionality of specific behaviors" (line 590) defined? Related to this, I agree with Reviewer 2 that a clear definition of irrelevant should be mentioned that clarifies that relevance is roughly taken as "correlated or predictive with a fixed time lag". The analyses do not explore relevance with arbitrary time lags between neural and behavior data.

(8) CEBRA itself doesn't provide a neural reconstruction from its embeddings, but one could obtain one via a regression from extracted CEBRA embeddings to neural data. In addition to decoding results of CEBRA (figure S3), the neural reconstruction of CEBRA should be computed and CEBRA should be added to Figure 2 to see how the behaviorally relevant and irrelevant signals from CEBRA compare to other methods.

References:

Kobak, Dmitry, Wieland Brendel, Christos Constantinidis, Claudia E Feierstein, Adam Kepecs, Zachary F Mainen, Xue-Lian Qi, Ranulfo Romo, Naoshige Uchida, and Christian K Machens. 2016. "Demixed Principal Component Analysis of Neural Population Data." Edited by Mark CW van Rossum. eLife 5 (April): e10989. https://doi.org/10.7554/eLife.10989.

Sani, Omid G., Hamidreza Abbaspourazad, Yan T. Wong, Bijan Pesaran, and Maryam M. Shanechi. 2021. "Modeling Behaviorally Relevant Neural Dynamics Enabled by Preferential Subspace Identification." Nature Neuroscience 24 (1): 140-49. https://doi.org/10.1038/s41593-020-00733-0.

Zhou, Ding, and Xue-Xin Wei. 2020. "Learning Identifiable and Interpretable Latent Models of High-Dimensional Neural Activity Using Pi-VAE." In Advances in Neural Information Processing Systems, 33:7234-47. Curran Associates, Inc. https://proceedings.neurips.cc/paper/2020/hash/510f2318f324cf07fce24c3a4b89c771-Abstract.html.

Hurwitz, Cole, Akash Srivastava, Kai Xu, Justin Jude, Matthew Perich, Lee Miller, and Matthias Hennig. 2021. "Targeted Neural Dynamical Modeling." In Advances in Neural Information Processing Systems. Vol. 34. https://proceedings.neurips.cc/paper/2021/hash/f5cfbc876972bd0d031c8abc37344c28-Abstract.html.

Balzani, Edoardo, Jean-Paul G. Noel, Pedro Herrero-Vidal, Dora E. Angelaki, and Cristina Savin. 2023. "A Probabilistic Framework for Task-Aligned Intra- and Inter-Area Neural Manifold Estimation." In . https://openreview.net/forum?id=kt-dcBQcSA.