Reviewer #1 (Public Review):

Summary:<br /> The work of Muller and colleagues concerns the question of where we place our feet when passing uneven terrain, in particular how we trade-off path length against the steepness of each single step. The authors find that paths are chosen that are consistently less steep and deviate from the straight line more than an average random path, suggesting that participants indeed trade-off steepness for path length. They show that this might be related to biomechanical properties, specifically the leg length of the walkers. In addition, they show using a neural network model that participants could choose the footholds based on their sensory (visual) information about depth.

Strengths:<br /> The work is a natural continuation of some of the researchers' earlier work that related the immediately following steps to gaze [17]. Methodologically, the work is very impressive and presents a further step forward towards understanding real-world locomotion and its interaction with sampling visual information. While some of the results may seem somewhat trivial in hindsight (as always in this kind of study), I still think this is a very important approach to understanding locomotion in the wild better.

Weaknesses:<br /> The manuscript as it stands has several issues with the reporting of the results and the statistics. In particular, it is hard to assess the inter-individual variability, as some of the data are aggregated across individuals, while in other cases only central tendencies (means or medians) are reported without providing measures of variability; this is critical, in particular as N=9 is a rather small sample size. It would also be helpful to see the actual data for some of the information merely described in the text (e.g., the dependence of \Delta H on path length). When reporting statistical analyses, test statistics and degrees of freedom should be given (or other variants that unambiguously describe the analysis). The CNN analysis chosen to link the step data to visual sampling (gaze and depth features) should be motivated more clearly, and it should describe how training and test sets were generated and separated for this analysis. There are also some parts of figures, where it is unclear what is shown or where units are missing. The details are listed in the private review section, as I believe that all of these issues can be fixed in principle without additional experiments.

Reviewer #1 (Public Review):

Overall, the experiments are well-designed and the results of the study are exciting. We have one major concern, as well as a few minor comments that are detailed in the following.

Major:<br /> 1. The authors suggest that "Visuomotor experience induces functional and structural plasticity of chandelier cells". One puzzling thing here, however, is that mice constantly experience visuomotor coupling throughout life which is not different from experience in the virtual tunnel. Why do the authors think that the coupled experience in the VR induces stronger experience-dependent changes than the coupled experience in the home cage? Could this be a time-dependent effect (e.g. arousal levels could systematically decrease with the number of head-fixed VR sessions)? The control experiment here would be to have a group of mice that experience similar visual flow without coupling between movement and visual flow feedback. Either change would be experience-dependent of course, but having the "visuomotor experience dependent" in the title might be a bit strong given the lack of control for that. We would suggest changing the pitch of the manuscript to one of the conclusions the authors can make cleanly (e.g. Figure 4).

Minor:<br /> 2. "ChCs shape the communication hierarchy of cortical networks providing visual and contextual information." We are not sure what this means.

3. "respond to locomotion and visuomotor mismatch, indicating arousal-related activity" This is not clear. We think we understand what the authors mean but would suggest rephrasing.

4. 'based on morphological properties revealed that 87% (287/329) of labeled neurons were ChCs" Please specify the morphological properties used for the classification somewhere in the methods.

5. We may have missed this - in the patch clamp experiment (Fig.1 H-K), please add information about how many mice/slices these experiments were performed in.

6. "These findings suggest that the rabies-labeled L1-4 neurons providing monosynaptic input to ChCs are predominantly inhibitory neurons". We are not sure this conclusion is warranted given the sparse set of neurons labelled and the low number of cells recorded in the paired patch experiment. We would suggest properly testing (e.g. stain for GABA on the rabies data) or rephrasing.

7. Figure 2E. A direct comparison of dF/F across different cell types can be subject to a problematic interpretation. The transfer function from spikes to calcium can be different from cell type to cell type. Additionally, the two cell populations have been marked with different constructs (despite the fact that it's the same GECI) further reducing the reliability of dF/F comparisons. We would recommend using a different representation here that does not rely on a direct comparison of dF/F responses (e.g. like the "response strength" used in Figure 3B). Assuming calcium dynamics are different in ChCs and PyCs - this similarity in calcium response is likely a coincidence.

8. If ChCs are more strongly driven by locomotion and arousal, then it's a bit counterintuitive that at the beginning of the visual corridor when locomotion speed consistently increases, the activity of ChCs consistently decreases. This does not appear to be driven by suppression by visual stimuli as it is present also in the first and last 20cm of the tunnel where there are no visual stimuli. How do the authors explain this?

9. The authors mention that "ChC responses underwent sensory-evoked plasticity during the repeated visual exposure, even though the visual stimuli were different from those encountered during training in the virtual tunnel". How would this work? And would this mean all visual responses are reduced? What is special about the visual experience in the virtual tunnel? It does not inherently differ from visual experience in the home cage, given that the test stimuli (full field gratings) are different from both.

10. Just as a point to consider for future experiments: For the open-loop control experiments, the visual flow is constant (20cm/s) - ideally, this would be a replay of the running speed the mouse previously generated to match statistics.

11. We would recommend specifying the parameters used for neuropil correction in the methods section.

12. If we understand correctly, the F0 used for the dF/F calculation is different from that used for division. Why is this?

13. Authors compare neuronal responses using "baseline-corrected average". Please specify the parameters of the baseline correction (i.e. what is used as baseline here).

Reviewer #1 (Public Review):

Summary:<br /> The authors aim to consider the effects of phonotactics on the effectiveness of memory reactivation during sleep. They have created artificial words that are either typical or atypical and showed that reactivation improves memory for the latter but not the former.

Strengths:<br /> This is an interesting design and a creative way of manipulating memory strength and typicality. In addition, the spectral analysis on both the wakefulness data and the sleep data is well done. The article is clearly written and provides a relevant and comprehensive of the literature and of how the results contribute to it.

Weaknesses:<br /> 1. Unlike most research involving artificial language or language in general, the task engaged in this manuscript did not require (or test) learning of meaning or translation. Instead, the artificial words were arbitrarily categorised and memory was tested for that categorisation. This somewhat limits the interpretation of the results as they pertain to language science, and qualifies comparisons with other language-related sleep studies that the manuscript builds on.

2. The details of the behavioural task are hard to understand as described in the manuscript. Specifically, I wasn't able to understand when words were to be responded to with the left or right button. What were the instructions? Were half of the words randomly paired with left and half with right and then half of each rewarded and half unrewarded? Or was the task to know if a word was rewarded or not and right/left responses reflected the participants' guesses as to the reward (yes/no)? Please explain this fully in the methods, but also briefly in the caption to Figure 1 (e.g., panel C) and in the Results section.

3. Relatedly, it is unclear how reward or lack thereof would translate cleanly into a categorisation of hits/misses/correct rejections/false alarms, as explained in the text and shown in Figure 1D. If the item was of the non-rewarded class and the participant got it correct, they avoided loss. Why would that be considered a correct rejection, as the text suggests? It is no less of a hit than the rewarded-correct, it's just the trial was set up in a way that limits gains. This seems to mix together signal detection nomenclature (in which reward is uniform and there are two options, one of which is correct and one isn't) and loss-aversion types of studies (in which reward is different for two types of stimuli, but for each type you can have H/M/CR/FA separably). Again, it might all stem from me not understanding the task, but at the very least this required extended explanations. Once the authors address this, they should also update Fig 1D. This complexity makes the results relatively hard to interpret and the merit of the manuscript hard to access. Unless there are strong hypotheses about reward's impact on memory (which, as far as I can see, are not at the core of the paper), there should be no difference in the manner in which the currently labelled "hits" and "CR" are deemed - both are correct memories. Treating them differently may have implications on the d', which is the main memory measure in the paper, and possibly on measures of decision bias that are used as well.

4. The study starts off with a sample size of N=39 but excludes 17 participants for some crucial analyses. This is a high number, and it's not entirely clear from the text whether exclusion criteria were pre-registered or decided upon before looking at the data. Having said that, some criteria seem very reasonable (e.g., excluding participants who were not fully exposed to words during sleep). It would still be helpful to see that the trend remains when including all participants who had sufficient exposure during sleep. Also, please carefully mention for each analysis what the N was.

5. Relatedly, the final N is low for a between-subjects study (N=11 per group). This is adequately mentioned as a limitation, but since it does qualify the results, it seemed important to mention it in the public review.

6. The linguistic statistics used for establishing the artificial words are all based on American English, and are therefore in misalignment with the spoken language of the participants (which was German). The authors should address this limitation and discuss possible differences between the languages. Also, if the authors checked whether participants were fluent in English they should report these results and possibly consider them in their analyses. In all fairness, the behavioural effects presented in Figure 2A are convincing, providing a valuable manipulation test.

7. With regard to the higher probability of nested spindles for the high- vs low-PP cueing conditions, the authors should try and explore whether what the results show is a general increase for spindles altogether (as has been reported in the past to be correlated with TMR benefit and sleep more generally) or a specific increase in nested spindles (with no significant change in the absolute numbers of post-cue spindles). In both cases, the results would be interesting, but differentiating the two is necessary in order to make the claim that nesting is what increased rather than spindle density altogether, regardless of the SW phase.

Reviewer #1 (Public Review):

Overall, the manuscript has been improved by addressing some of the concerns, however, I am still very confused about the data analysis due to the use of data transformation (relative %fos), the fact that some graphs only show regions that are significant and the interpretation of the PCA analysis which I find inappropriate. Moreover, many answers in the rebuttal did not make it to the final manuscript and are not discussed and limitations raised by the reviewers are not discussed either.

1a. The addition of the EEG/EMG is useful, however, this information is not discussed. For instance, there are differences in EEG/EMG between the two groups (only Ket significantly increased delta/theta power, and only ISO decreased EMG power). These results should be discussed as well as the limitation of not having physiological measures of anesthesia to control for the anesthesia depth.<br /> 1b. The possibility that the differences in fos observed may be due to the doses used should be discussed.<br /> 1c. The possibility that the differences in fos observed may be due kinetic of anesthetic used should be discussed.

2b. I am confused because Fig 2C seems to show significant decrease in %fos in the hypothalamus, midbrain and cerebellum after KET, while the author responded that " in our analysis, we did not detect regions with significant downregulation when comparing anesthetized mice with controls." Moreover the new figure in the rebuttal in response to reviewer 2 suggests that Ket increases Fos in almost every single region (green vs blue) which is not the conclusion of the paper.

3. There are still critical misinterpretations of the PCA analysis. For instance, it is mentioned that "KET is associated with the activation of cortical regions (as evidenced by positive PC1 coefficients in MOB, AON, MO, ACA, and ORB) and the inhibition of subcortical areas (indicated by negative coefficients) " as well as "KET displays cortical activation and subcortical inhibition, whereas ISO shows a contrasting preference, activating the cerebral nucleus (CNU) and the hypothalamus while inhibiting cortical areas. To reduce inter-individual variability." These interpretations are in complete contradiction with the answer 2b above that there was no region that had decreased Fos by either anesthetic.

4. I still do not understand the rationale for the use of that metric. The use of a % of total Fos makes the data for each region dependent on the data of the other regions which wrongly leads to the conclusion that some regions are inhibited while they are not when looking at the raw data. Moreover, the interdependence of the variable (relative density) may affect the covariance structure which the PCA relies upon. Why not using the PCA on the logarithm of the raw data or on a relative density compared to the control group on a region-per-region basis instead of the whole brain?

Fig. 2B: it's unclear to me why the regions are connected by a line. Such representation is normally used for time series/within-subject series. What is the rationale for the order of the regions and the use of the line? The line connecting randomly organized regions is meaningless and confusing.

Fig 6A. the correlation matrices are difficult to interpret because of the low resolution and arbitrary order of brain regions. I recommend using hierarchical clustering and/or a combination of hierarchical clustering and anatomical organization (e.g. PMID: 31937658). While it is difficult to add the name of the regions on the graph I recommend providing supplementary figures with large high-resolution figures with the name of each brain region so the reader can actually identify the correlation between specific brain regions and the whole brain,

Rationale for Metric Choice: Note that I do not dispute the choice of the log which is appropriate, it is the choice of using the relative density that I am questioning.

5. I am still having difficulties understanding Fig. 3.<br /> Panel A: The lack of identification for the dots in panel A makes it impossible to understand which regions are relevant.<br /> Panel B: what is the metric that the up/down arrow summarizes? Fos density? Relative density? PC1/2?<br /> Panel C: it's unclear to me why the regions are connected by a line. Such representation is normally used for time series/within-subject series. What is the rationale for the order of the regions?

Reviewer #1 (Public Review):

Summary:<br /> This paper makes important contributions to the structural analysis of the DNA replication-linked nucleosome assembly machine termed Chromatin Assembly Factor-1 (CAF-1). The authors focus on the interplay of domains that bind DNA, histones, and replication clamp protein PCNA.

Strengths:<br /> The authors analyze soluble complexes containing full-length versions of all three fission yeast CAF-1 subunits, an important accomplishment given that many previous structural and biophysical studies have focused on truncated complexes. New data here supports previous experiments indicating that the KER domain is a long alpha helix that binds DNA. Via NMR, the authors discover structural changes at the histone binding site, defined here with high resolution. Most strikingly, the experiments here show that for the S. pombe CAF-1 complex, the WHD domain at the C-terminus of the large subunit lacks DNA binding activity observed in the human and budding yeast homologs, indicating a surprising divergence in the evolution of this complex. Together, these are important contributions to the understanding of how the CAF-1 complex works.

Weaknesses:<br /> 1. There are some aspects of the experimentation that are incompletely described:

In the SEC data (Fig. S1C) it appears that Pcf1 in the absence of other proteins forms three major peaks. Two are labeled as "1a" (eluting at ~8 mL) and "1b" (~10-11 mL). It appears that Pcf1 alone or in complex with either or both of the other two subunits forms two different high molecular weight complexes (e.g. 4a/4b, 5a/5b, 6a/6b). There is also a third peak in the analysis of Pcf1 alone, which isn't named here, eluting at ~14 mL, overlapping the peaks labeled 2a, 4c, and 5c.

The text describing these different macromolecular complexes seems incomplete (p. 3, lines 32-33): "When isolated, both Pcf2 and Pcf3 are monomeric while Pcf1 forms large soluble oligomers". Which of the three Pcf1-alone peaks are oligomers, and how do we know? What is the third peak? The gel analysis across these chromatograms should be shown.

More importantly, was a particular SEC peak of the three-subunit CAF-1 complex (i.e. 4a or 4b) characterized in the further experimentation, or were the data obtained from the input material prior to the separation of the different peaks? If the latter, how might this have affected the results? Do the forms inter-convert spontaneously?

2. Given the strong structural predication about the roles of residues L359 and F380 (Fig. 2f), these should be mutated to determine effects on histone binding.

3. Could it be that the apparent lack of histone deposition by the delta-WHD mutant complex occurs because this mutant complex is unstable when added to the Xenopus extract?

Reviewer #1 (Public Review):

Summary:

Flavonoids are abundant in plant-based foods. They have been widely recognized for their health-promoting properties. There is increasing evidence that the effects of dietary flavonoids depend on their metabolism by gut bacteria, which can enhance, reduce or otherwise alter the flavonoids' bioactivities. On the other hand, little is known regarding the enzymes and species that can utilize flavonoids as metabolic substrates.

In the current manuscript, the authors analyzed the possibility to predict the degradation of flavonoids that we take up with our food by gut bacteria. In contrast to plants, bacteria do not contain obvious degradation enzymes.

Strengths:

To predict such enzymes with a broad substrate specificity (enzyme promiscuity) the authors optimized/modified a bioinformatic tool to predict whether a gut bacterial enzyme could catalyze a flavonoid reaction based on the chemical reaction similarity of the enzyme's native reaction and known flavonoid reactions in plants.<br /> They predicted such enzyme activities in genomes of bacteria that had been shown to occur in the human gut. Then, they cultivated selected bacteria with the predicted enzymatic activities and in fact showed, that they can degrade parts of these flavonoids. Together with the bioinformatic and mass spectrometry they identified a metabolization pathway of the flavonoid tilianin that spanned multiple species, i.e., Bifidobacterium longum subsp. animalis, Blautia coccoides, and Flavonifractor plautii. Lastly, the authors showed that tilianin metabolites exhibit protective effects against H2O2 through reactive oxygen species scavenging activity and thus, improve viability of a neuronal cell line, while the parent compound, tilianin, was ineffective. This protective effect might be due to gut microbiota-dependent physiological effects of dietary flavonoids.

Weaknesses:

1) To confirm the bioinformatic-based predictions the authors used in vitro culture experiments and LC-MS experiments. Although these in vitro experiments clearly add value to the bioinformatic prediction, they fall short of providing firm evidence for the predictions because they do not show whether the predicted enzymes really catalyze the predicted reactions. In theory, there could be other enzymes not identified bioinformatically that catalyze the reactions.

2) It is not clear how the authors selected the bacterial species. Did they analyze meta genome sequences or hundreds of genomes of gut bacteria? Did they analyze bacteria isolated from the gut or rather type strains? What about other bacterial species in the gut? Do they also encode relevant enzymes? If yes, how many do? This needs to be clarified.

3) The reported data on E. coli is difficult to understand. Has E. coli a different degradation pathway leading to the observed disappearance of tilianins?

Reviewer #1 (Public Review):

Summary:<br /> In this highly ambitious paper, Breen and Deffner used a multi-pronged approach to generate novel insights on how differences between male and female birds in their learning strategies might relate to patterns of invasion and spread into new geographic and urban areas.

The empirical results, drawn from data available in online archives, showed that while males and females are similar in their initial efficiency of learning a standard color-food association (e.g., color X = food; color Y = no food) scenario when the associations are switched (now, color Y = food, X= no food), males are more efficient than females at adjusting to the new situation (i.e., faster at 'reversal learning'). Clearly, if animals live in an unstable world, where associations between cues (e.g., color) and what is good versus bad might change unpredictably, it is important to be good at reversal learning. In these grackles, males tend to disperse into new areas before females. It is thus fascinating that males appear to be better than females at reversal learning. Importantly, to gain a better understanding of underlying learning mechanisms, the authors use a Bayesian learning model to assess the relative role of two mechanisms (each governed by a single parameter) that might contribute to differences in learning. They find that what they term 'risk sensitive' learning is the key to explaining the differences in reversal learning. Males tend to exhibit higher risk sensitivity which explains their faster reversal learning. The authors then tested the validity of their empirical results by running agent-based simulations where 10,000 computer-simulated 'birds' were asked to make feeding choices using the learning parameters estimated from real birds. Perhaps not surprisingly, the computer birds exhibited learning patterns that were strikingly similar to the real birds. Finally, the authors ran evolutionary algorithms that simulate evolution by natural selection where the key traits that can evolve are the two learning parameters. They find that under conditions that might be common in urban environments, high-risk sensitivity is indeed favored.

Strengths:<br /> The paper addresses a critically important issue in the modern world. Clearly, some organisms (some species, some individuals) are adjusting well and thriving in the modern, human-altered world, while others are doing poorly. Understanding how organisms cope with human-induced environmental change, and why some are particularly good at adjusting to change is thus an important question.

The comparison of male versus female reversal learning across three populations that differ in years since they were first invaded by grackles is one of few, perhaps the first in any species, to address this important issue experimentally.

Using a combination of experimental results, statistical simulations, and evolutionary modeling is a powerful method for elucidating novel insights.

Weaknesses:<br /> The match between the broader conceptual background involving range expansion, urbanization, and sex-biased dispersal and learning, and the actual comparison of three urban populations along a range expansion gradient was somewhat confusing. The fact that three populations were compared along a range expansion gradient implies an expectation that they might differ because they are at very different points in a range expansion. Indeed, the predicted differences between males and females are largely couched in terms of population differences based on their 'location' along the range-expansion gradient. However, the fact that they are all urban areas suggests that one might not expect the populations to differ. In addition, the evolutionary model suggests that all animals, male or female, living in urban environments (that the authors suggest are stable but unpredictable) should exhibit high-risk sensitivity. Given that all grackles, male and female, in all populations, are both living in urban environments and likely come from an urban background, should males and females differ in their learning behavior? Clarification would be useful.

Reinforcement learning mechanisms:<br /> Although the authors' title, abstract, and conclusions emphasize the importance of variation in 'risk sensitivity', most readers in this field will very possibly misunderstand what this means biologically. Both the authors' use of the term 'risk sensitivity' and their statistical methods for measuring this concept have potential problems.

First, most behavioral ecologists think of risk as predation risk which is not considered in this paper. Secondarily, some might think of risk as uncertainty. Here, as discussed in more detail below, the 'risk sensitivity' parameter basically influences how strongly an option's attractiveness affects the animal's choice of that option. They say that this is in line with foraging theory (Stephens and Krebs 2019) where sensitivity means seeking higher expected payoffs based on prior experience. To me, this sounds like 'reward sensitivity', but not what most think of as 'risk sensitivity'. This problem can be easily fixed by changing the name of the term.

In addition, however, the parameter does not measure sensitivity to rewards per se - rewards are not in equation 2. As noted above, instead, equation 2 addresses the sensitivity of choice to the attraction score which can be sensitive to rewards, though in complex ways depending on the updating parameter. Second, equations 1 and 2 involve one specific assumption about how sensitivity to rewards vs. to attraction influences the probability of choosing an option. In essence, the authors split the translation from rewards to behavioral choices into 2 steps. Step 1 is how strongly rewards influence an option's attractiveness and step 2 is how strongly attractiveness influences the actual choice to use that option. The equation for step 1 is linear whereas the equation for step 2 has an exponential component. Whether a relationship is linear or exponential can clearly have a major effect on how parameter values influence outcomes. Is there a justification for the form of these equations? The analyses suggest that the exponential component provides a better explanation than the linear component for the difference between males and females in the sequence of choices made by birds, but translating that to the concepts of information updating versus reward sensitivity is unclear. As noted above, the authors' equation for reward sensitivity does not actually include rewards explicitly, but instead only responds to rewards if the rewards influence attraction scores. The more strongly recent rewards drive an update of attraction scores, the more strongly they also influence food choices. While this is intuitively reasonable, I am skeptical about the authors' biological/cognitive conclusions that are couched in terms of words (updating rate and risk sensitivity) that readers will likely interpret as concepts that, in my view, do not actually concur with what the models and analyses address.

To emphasize, while the authors imply that their analyses separate the updating rate from 'risk sensitivity', both the 'updating parameter' and the 'risk sensitivity' parameter influence both the strength of updating and the sensitivity to reward payoffs in the sense of altering the tendency to prefer an option based on recent experience with payoffs. As noted in the previous paragraph, the main difference between the two parameters is whether they relate to behaviour linearly versus with an exponential component.

Overall, while the statistical analyses based on equations (1) and (2) seem to have identified something interesting about two steps underlying learning patterns, to maximize the valuable conceptual impact that these analyses have for the field, more thinking is required to better understand the biological meaning of how these two parameters relate to observed behaviours, and the 'risk sensitivity' parameter needs to be re-named.

Agent-based simulations:<br /> The authors estimated two learning parameters based on the behaviour of real birds, and then ran simulations to see whether computer 'birds' that base their choices on those learning parameters return behaviours that, on average, mirror the behaviour of the real birds. This exercise is clearly circular. In old-style, statistical terms, I suppose this means that the R-square of the statistical model is good. A more insightful use of the simulations would be to identify situations where the simulation does not do as well in mirroring behaviour that it is designed to mirror.

Reviewer #1 (Public Review):

This manuscript tried to answer a long-standing question in an important research topic. I read it with great interest. The quality of the science is high, and the text is clearly written. The conclusion is exciting. However, I feel that the phenotype of the transgenic line may be explained by an alternative idea. At least, the results should be more carefully discussed.

Specific comments:

1) Stability or activity (Fv/Fm) was not affected in PSII with the W14F mutation in D1. If W14F really represents the status of PSII with oxidized D1, what is the reason for the degradation of almost normal D1?

2) To focus on the PSII in which W14 is oxidized, this research depends on the W14F mutant lines. It is critical how exactly the W-to-F substitution mimics the oxidized W. The authors tried to show it in Figure 5. Because of the technical difficulty, it may be unfair to request more evidence. But the paper would be more convincing with the results directly monitoring the oxidized D1 to be recognized by FtsH.

3) Figure 3. If the F14 mimics the oxidized W14 and is sensed by FtsH, I would expect the degradation of D1 even under the growth light. The actual result suggests that W14F mutation partially modifies the structure of D1 under high light and this structural modification of D1 is sensed by FtsH. Namely, high light may induce another event which is recognized by FtsH. The W14F is just an enhancer.

Reviewer #1 (Public Review):

There are a number of outstanding questions concerning how cohesin turnover on DNA is controlled by various accessory factors and how such turnover is controlled by post-translational modification. In this paper, Nasmyth et al. perform a series of AlphaFold structure predictions that aim to address several of these outstanding questions. Their structure predictions suggest that the release factor WAPL forms a ternary complex with PDS5 and SA/SCC3. This ternary complex appears to be able to bind the N-terminal end of SCC1, suggesting how formation of such a complex could stabilize an open state of the cohesin ring. Additional calculations suggest how the Eco/ESCO acetyltransferases and Sororin engage the SMC3 head domain presumably to protect against WAPL-mediated release.

This work thus demonstrates the power of AF prediction methods and how they can lead to a number of interesting and testable hypotheses that can transform our understanding of cohesin regulation. These findings require orthogonal experimental validation, but authors argue convincingly that such validation should not be a pre-requisite to publication.

In their revised version, the authors did not systematically include model confidence scores, and it therefore remains difficult for the reader to evaluate the reliability of the models obtained. The authors correctly point out that such metrics are available on figshare. It is therefore possible to obtain such information. The caveat is that it remains to the user to identify and extract the relevant information. While they claim that they have labeled N- and C-termini in their figures, no such labeling can be seen in the revised version. Addition of such labels, at least for some of the figures, would help the user to navigate the models.

The authors have now updated figure legends to indicate which protein is referred to by the chain labels shown in PAE plots.

It is exciting to see AF-multimer predictions being applied to cohesin. As some of the reported interactions are not universally conserved and some involve relatively small interfaces the possibility arises that these interfaces show poor or borderline confidence scores. As some of these interfaces map to mutants that have previously been obtained by hypothesis-free genetic screens and mutational analyses, they appear nevertheless valid. Thus, an important point to make is that even interfaces that show modest confidence scores may turn out to be valid while others may be not.

Joint Public Review:

The study as a concept is well designed, although there is still one issue I see in the methodology.

I still have concerns with their attempts to combine the different scales of data. While the use of point data is great, it limits the sample size, and they have included the district to country level data to try and increase the sample size. The problem is that although they try to get an overall estimate at the district/state/country by taking 10 random sample points, which could be a method to get an estimate for the district/state/country. It would be a suitable method if the primates were evenly distributed across the district/state/country. The reality is that the primates are not evenly distributed across the district/state/country therefore the random point sampling is not a reasonable method to get an estimate of the environmental variables in relation to the macaques. For example if you had a mountainous country and you took 10 random points to estimate altitude, you would end up with a large number, but if all the animals of interest lived on the coast, your average altitude is meaningless in relation to the animals of interest as they are all living at low altitude. The fact that the model relies less on highly variable components and places more reliance on less variable components, is really not relevant as the district/state/country measurements have no real meaning in relation to the distribution of masques.

A simple possible way forward could be to run the model without the district/state/country samples and see what the outcome is. If the outcome is similar then the random point method may be viable (but if it gives the same outcome as ignoring those samples then you don't need the district/state/country samples). If you get a totally different outcome then it should raise concerns about using the district/state/country samples.

This paper is a really nice piece of work and is a valuable contribution but the district/state/country sample issue really needs to be addressed.

Reviewer #1 (Public Review):

Summary:<br /> This manuscript addresses the regulation of the osmosensing protein kinases, WNK1 and WNK3. Prior work by the authors has shown that these enzymes are activated by PEG400 or ethylene glycol and inhibited by chloride ion, and that activation is associated with a conformational transition from dimer to monomer. In X-ray structures of the WNK1/SA inactive dimer, a water-mediated hydrogen bond network was observed between the catalytic loop (CL) and the activation loop (AL), named CWN1. This led to the proposal that bound water may be part of the osmosensing mechanism.

The current study carries this work further, by applying PEG400 to Xtals of dimeric WNK1/SA. This results in a change in kinase conformation and space group, along with 4-9 fewer waters in CWN1 and the complete disappearance of another water cluster (CWN2) located at the dimer interface. Six conserved residues lining the CWN1 pocket in WNK3 are mutated to determine effects on activity and inhibition by chloride ion (measured by AL autophosphorylation) and monomer-dimer interconversion (light scattering).

The results show that two mutants (E314Q/A in WNK3) at a site central to the water cluster result in increased kinase activity (autophosphorylation), and increased SLS, interpreted as aggregation. Three sites (D279A, Y346F, M301A) inhibit kinase activity with varying effects on oligomerization - Y346A and M301A retain monomer-dimer ratios similar to WT while D279N promotes aggregation. K236A and K307A show activity and monomer:dimer ratios similar to WT. Selected mutants (E314Q, D279N, Y346F) and WT appear to retain osmosensitivity with comparable activation by PEG400.

The study concludes that osmolytes may activate the kinase by removing waters from the CWN1 and CWN2 clusters, suggesting that waters might be considered allosteric ligands that promote the inactive structure of WNKs. The differing effects of mutations may be ascribed to disruption of the water networks as well as inhibitory perturbations at the active site.

Strengths:<br /> This study presents a novel and unique function for bound water, and its potential role to explain osmosensory regulation. The mechanism is innovative and the new structures and mutational data presented by the work will be useful for further investigations of the mechanisms that enable cells to respond to osmotic pressure.

Weaknesses:<br /> Given that all mutants tested showed the same degree of activation by PEG400, it seemed possible that PEG400 might be an allosteric activator of WNK1/3 through direct binding interactions. Perhaps PEG400 eliminates CWN1/2 waters by inducing conformational changes so that water loss is an effect not a cause of activation. To address this it would be helpful to comment on whether new electron densities appeared in the X-ray structure of WNK1/SA/PEG400 that might reflect PEG400 interactions with chains A or B. It would also be helpful to discuss any experiments that might have been done in previous work to examine the direct binding of glycerol and other osmolytes to WNKs.

The study would benefit from a deeper discussion about how to reconcile the different effects of mutations. For example, wouldn't most or all of the mutations be expected to disrupt the water network, and relieve the proposed autoinhibition? This seemed especially true for some of the residues, like Y420(Y346), D353(D279), and K310(K236), which based on Fig 3 appeared to interact with waters that were removed by PEG400.

Alternatively, perhaps the waters in CWN2 are more important for maintaining the autoinhibited structure. This possibility would be useful to discuss, and perhaps comment on what may be known about the energetic contributions of bound water towards stabilizing dimers.

It would also be useful to comment on why aggregation of E319Q/A shouldn't inhibit kinase activity instead of activating it.

The X-ray work was done entirely with WNK1 while the mutational work was done entirely with WNK3. Therefore, a simple explanation for the disconnect between structure and mutations might be that WNK1 and WNK3 differ enough that predictions from the structure of one are not applicable to mutations of the other. It would be helpful to describe past work comparing the structure and regulation of WNK1 and WNK3 that support the assumption of their interchangeability.

Reviewer #1 (Public Review):

The non-classical MHCII-like protein H2-M is essential for the loading of peptides on MHCII. The discovery that DM was partnered with a second MHCII-like protein, H2-O, which squelched or modified its activity was confounding. It was immediately speculated that H2-O was likely diminished self-peptide presentation. This led to the hypothesis that H2-O was involved in preventing unwanted CD4 T cell activation, thereby making autoimmunity less likely. 25 years of analysis of H2-O deficient mice have, indeed, shown that the self-peptide repertoire in the absence of H2-O is modestly altered. Demonstrating that autoimmunity results from this altered peptide repertoire has been decidedly less convincing. Old mice are reported to have increased serum anti-nuclear antibody titers, but mice prone to type 1 diabetes (T1D) and systemic lupus erythematosus (SLE) were not impacted by the loss of H2-O (Lee et al, 2021). Induction of the multiple sclerosis-like disease, EAE, in mice, was also shown to not be impacted by Lee et al 2021, although in a previous paper (Welsh et al 2020), the authors of this current manuscript suggest otherwise. Unfortunately, these discrepancies are not acknowledged by the authors, and the papers are, for the most part, not referenced.

In addition to antigen-presenting cells, H2-O is also found in MHCII-expressing medullary epithelial cells, suggesting it might play a role in T-cell selection. Direct data to support this idea, however, has, at most, shown a minimal impact. In this manuscript, the authors follow up on their previous paper (Welsh et al, 2020) to further evaluate changes to T cell development. The conclusions are that H2-O impacts Treg development and changes the frequency and homeostasis of CD4 T cells. Although these would be interesting results, the data analysis is flawed, the presentation is incomplete, and the conclusions are exaggerated.

T-cell development analysis shown in Figs. 1 and 2 use the discovery from the Hogquist lab (Breed et all 2019) that thymocytes destined for clonal deletion can be differentiated from those still "auditioning" for selection by FACS for expression of cleaved caspase 3. Detection relies on complex FACS analysis that requires the exclusion of multiple populations, followed by accurate gating on CD5+TCRb+ cells (see Hogquist Fig. 1A). The authors apparently neglected to use the essential gating steps, but rather only used CD4 and CCR7 expression (Fig. 1A). This deviation from the Hogquist approach makes interpretation of Figs 1 and 2 meaningless. Even if this is an oversight in the description of the experiments, key conclusions are drawn from minimal changes to CD69 expression. CD69 is expressed as a continuum in the thymus (a "shoulder") making gating somewhat subjective and prone to variation from experiment to experiment. At the minimum, FACS data should be shown to indicate how these changes were measured, plus variations from mouse to mouse should be plotted, with statistics. FACS data needs to be shown to define how the complex semi-mature, M1, and M2 populations were defined (see Hogquist Fig. 2) from which key conclusions are drawn.

To make the data more robust, 1) cell numbers must be included for all experiments;

2) rather than normalizing results to "the average H2-O WT levels", the actual data should be included;

3) figures should be more completely labeled/described;

4) FACS gating strategies should be clearly laid out (again, see Hogquist for examples). Furthermore, efforts must be made to explain why results are so different from analyses of H2-O deficient mice that have been published by many other groups. For example, the reported "dramatic increase in the proportion of CD3+CD4+ T cells" is not consistent with previous reports starting with Lars Karlsson's initial report (Liljedahl et al 1998). Extensive spontaneous activation of CD4 T cells has also not been reported in other papers that have studied these mice. Again, the paper is not placed in the context of the long, very thorough analysis of both the H2-O deficient mice and the study of H2-O/DO and H2-M/DM in general.

Reviewer #1 (Public Review):

Summary:<br /> Ciliary rootlet is a structure associated with the ciliary basal body (centriole) with beautiful striation observed by electron microscopy. It has been known for more than a century, but its function and protein arrangement are still unknown. This work reconstructed the near-atomic resolution 3D structure of the rootlet using cryo-electron tomography, discovered a number of interesting filamentous structures inside, and built a molecular model of the rootlet.

Strengths:<br /> The authors exploited the currently possible ability of cryo-ET and used it appropriately to describe the 3D structure of the rootlet. They carefully conducted subtomogram averaging and classification, which enabled an unprecedented detailed view of this structure. The dual use of (nearly) intact rootlets from cilia and extracted (demembraned) rootlets enabled them to describe with confidence how D1/D2/A bands form periodic structures and cross with longitudinal filaments, which are likely coiled-coil.

Weaknesses:<br /> Some more clarifications are needed. This reviewer believes that the authors can address them.

Reviewer #1 (Public Review):

The authors set out to define the molecular basis for LP as the origin of BRCA1-deficient breast cancers. They showed that LPs have the highest level of replicative stress, and hypothesise that this may account for their tendency to transform. They went on to identify ELF3 as a candidate driver of LP transformation and showed that ELF3 expression is up-regulated in response to replicative stress as well as BRCA1 deficiency. They went on to show that ELF3 inactivation led to a higher level of DNA damage, which may result from compromised replicative stress responses.

While the manuscript supports the interesting idea wherein ELF3 may fuel LP cell transformation, it remains obscure how ELF3 promotes cell tolerance to DNA damage. Interestingly the authors proposed that ELF3 suppresses excessive genomic instability, but in my opinion, I do not see any evidence that supports this claim. In fact, one might think that genomic instability is key to cell transformation.

Reviewer #1 (Public Review):

Summary:<br /> The authors analyzed 102 human embryos in order to address outstanding questions about human lower spinal development and secondary neural tube formation. Through whole embryo imaging and histologic analysis, they provide exceptional quantification of the timing of posterior neuropore closure, rate of lower spinal somite formation, and formation and regression of the human "tail." Their analysis also provides convincing qualitative evidence of the cellular and molecular mechanisms at play during lower spinal development by identifying the presence of caspase-dependent programmed cell death and the dynamic expression of FGF8/WNT3A within the elongating embryo. Interestingly, they identify multiple polarized lumens within the site of secondary neural tube formation and add a solid argument for the mode of formation of this structure; however, in its current state, the evidence for a conclusive morphogenetic mechanism remains elusive. Finally, the authors provide a substantial review of the existing publications related to human lower spinal development, creating an excellent reference and demonstrating the importance of continuing to utilize each of these precious samples for furthering our understanding of human development.

Strengths:<br /> This manuscript provides an excellent window into the key morphogenetic events of human caudal neural tube formation. Figures 1 and 2 provide beautiful images and quantification of the developmental events, enabling comparison to models that are currently in use, including model organisms and the developing spinal organoid field. The characterization of somite development and later regression is particularly important.

Next, the authors addressed current questions regarding the molecular pathways present during the elongation of the embryo and later regression of the tail structure. The in situ hybridization experiments in Figures 5 and 6 demonstrate important evidence for a maintained neuromesodermal progenitor pool of stem cells that promote axial elongation. Additionally, the identification of caspase-dependent cell death within the human tail provides an explanation for the mechanism of this regression, especially given the notable lack of presence of any gross necrosis.

Finally, as mentioned above, the non-trivial collection and review of the existing human secondary neural tube and body formation literature is an important tool and organizes and synthesizes ~ 100 years of observations from precious human samples.

Weaknesses:<br /> While there are no glaringly incorrect claims from the authors, several of the conclusions could benefit from a form of quantification to support their observations:

1) The identification of the proximal to distal degeneration of the tailgut within the human tail is difficult to distinguish with the current images present in Figure 3. A picture within a picture of the area containing the tail gut could be provided to prominently demonstrate the cellular architecture. Additionally, quantification of the localization of apoptosis would strongly support this observation, as well as provide a visualization of the tail's regression overall. For example, a graph plotting the number of apoptotic cells versus the rostral to caudal locations of the transverse sections while accounting for the CS stage of each analyzed embryo could be created; this could even be further broken down by region of tail, for example, tailgut, ventral ectodermal ridge, somite, etc.

2) The identification of the mode of formation of the secondary neural tube is probably the most interesting question to be addressed, however, Figure 7's evidence is not completely satisfying in its current form. While I agree that it is unlikely that multiple polarization foci form within the most caudal part of the tail and coalesce more rostrally, I am equally unsure that a single polarization would form rostrally and then split and re-coalesce as it moves caudally, as is currently depicted by 7B.

Multiple groups have recently shown the influence of geometric confinement on neuroectoderm and its ability to polarize and form a singular central lumen (Karzbrun 2021, Knight 2018), or the inverse situation of a lack of confinement resulting in the presence of multiple lumens. The tapering of the diameter of the tail and its shared perimeter and curvature with the polarization bears a striking resemblance to this controlled confinement. An interesting quantification to depict would include the number of lumens versus the transverse section diameter and CS stage to see if there is any correlation between embryo size and the number of multiple polarizations. Anecdotally, the fusion of multiple polarizations/lumens tends to occur often in these human organoid-type platforms, while splitting to multiple lumens as the tissues mature does not. Other supplements to Figure 7 could include 3D renderings of lumens of interest as depicted in Catala 2021, especially if it demonstrates the re-coalescence as seen in 7B.

The non-pathologic presence of multiple polarizations in human tails compared to the rodent pathogenic counterpart is interesting given that rodents obviously maintain this appendage while it is lost in humans.

3) Of potential interest is the process of junctional neurulation describing the mechanistic joining of the primary and secondary neural tube, which has recently been explored in chick embryos and demonstrated to have relevance to human disease (Dady 2014, Eibach 2017, Kim 2021). While it is clear this paper's goal does not center on the relationship between primary and secondary neurulation, such a mechanism may be relevant to the authors' interpretation of their observations of lumen coalescence. I wonder if the embryos studied provide any evidence to support junctional neurulation.

Reviewer #1 (Public Review):

Summary:<br /> Leanza et al. investigated the regulation of Wnt signaling factors in the bone tissue obtained from individuals with or without type 2 diabetes. They showed that typical canonical Wnt ligands and downstream factors (Wnt10b, LEF1) are down-regulated, while Wnt5a and sclerostin mRNA are unregulated in diabetic bone tissue. Further, Wnt5a and sclerostin associated with the content of AGEs and SOST mRNA levels also correlated with glycemic control and disease duration.

Strengths:<br /> - A strength of the study is the investigation of Wnt signaling in bone tissue from humans with type 2 diabetes. Most studies measure only serum levels of Wnt inhibitors, but this study takes it further and looks into bone specifically.<br /> - The measurement of AGEs and its correlation to the Wnt signaling molecules is interesting and important. The correlation of sclerostin and Wnt5a with AGEs and disease duration suggests that inhibited Wnt signaling is paralleled by higher AGE levels and potentially weaker bone.<br /> - The methodology in terms of obtaining the bone samples and the rigorous evaluation of RNA integrity is great and provides a solid basis for further analyses.

Weaknesses:<br /> - A weakness may include the rather limited number of samples. Especially for some sub-analyses (e.g. RNA analyses), only a subset of samples was used.<br /> - How was the sample size determined? It seems like more samples might have been necessary to obtain significant results for methods with a higher standard deviation (e.g. histomorphometry).<br /> - Why is the number of samples different for the mRNA measurements? In most cases, there were 9, but in some 8 and in some 10?

Overall, this study validates findings from the group that reported similar findings in 2020. This validates their methodology and shows that alterations in Wnt signaling are reproducible in human bone tissue.

Reviewer #1 (Public Review):

In the study described in the manuscript, the authors identified Mecp2, a methyl-CpG binding protein, as a key regulator involved in the transcriptional shift during the exit of quiescent cells into the cell cycle. Their data show that Mecp2 levels were remarkably reduced during the priming/initiation stage of partial hepatectomy-induced liver regeneration and that altered Mecp2 expression affected the quiescence exit. Additionally, the authors identified Nedd4 E3 ligase that is required for the downregulation of Mecp2 during quiescence exit. This is an interesting study with well-presented data that supports the authors' conclusions regarding the role of Mecp2 in transcription regulation during the G0/G1 transition. However, the significance of the study is limited by a lack of mechanistic insights into the function of Mecp2 in the process. This weakness can be addressed by identifying the signaling pathway(s) that trigger Mecp2 degradation during the quiescence exit.

Reviewer #1 (Public Review):

The current study tests the hypothesis that inhibition of ryanodine receptor 2 (RyR2) in failing arrhythmogenic hearts reduces sarcoplasmic Ca leak, ventricular arrhythmias and improves contractile function. A guinea pig model of nonischemic heart failure (HF) was used and randomized to receive dantrolene (DS) or placebo in early or chronic HF. The authors show that DS treatment prevented ventricular arrhythmias and sudden cardiac death by decreasing dispersion of repolarization. The authors conclude that inhibition of RyR2 hyperactivity with DS mitigates the vicious cycle of sarcoplasmic Ca leak-induced increases in diastolic Ca and reactive oxygen species-mediated RyR2 oxidation. Moreover, the consequent increase in sarcoplasmic Ca2+ load improves contractile function.

In general, the study is well designed and the findings are likely to be of interest to the field.

Reviewer #1 (Public Review):

The manuscript focused on roles of a key fatty-acid synthesis enzyme, acetyl-coA-carboxylase 1 (ACC1), in the metabolism, gene regulation and homeostasis of invariant natural killer T (NKT_ cells and impact on these T cells' roles during asthma pathogenesis. The authors presented data showing that the acetyl-coA-carboxylase 1 enzyme regulates the expression of PPARg then the function of NKT cells including the secretion of Th2-type cytokines to impact on asthma pathogenesis. The results are clearcut and data were logically presented.

Reviewer #1 (Public Review):

Summary:<br /> The authors developed a deep learning method called H3-OPT, which combines the strength of AF2 and PLM to reach better prediction accuracy of antibody CDR-H3 loops than AF2 and IgFold. These improvements will have an impact on antibody structure prediction and design.

Strengths:<br /> The training data are carefully selected and clustered, the network design is simple and effective.

The improvements include smaller average Ca RMSD, backbone RMSD, side chain RMSD, more accurate surface residues and/or SASA, and more accurate H3 loop-antigen contacts.

The performance is validated from multiple angles.

Weaknesses:<br /> There are very limited prediction-then-validation cases, basically just one case.

Reviewer #1 (Public Review):

Mice and humans have two Cylicin genes (X-linked Cylicin 1 and the autosomal Cylicin 2) that encode cytoskeletal proteins. Cylicins are localized in the acrosomal region of round spermatids, yet they resemble a calyx component within the perinuclear theca of mature sperm nuclei. The function of Cylicins during this developmental stage of spermiogenesis (tail formation and head elongation/shaping) was not known. In this study, using CRISPR/Cas genome editing, the authors generated Cylc1-and Cylc2-knockout mouse lines to study the loss-of-function of each Cylicin or all together.

The major strengths of the study are the rigorous and comparative phenotypic analyses of all the combinatorial genotypes from the cross between the two mouse lines (Cylc1-/y, Cylc2-/-, Cylc1-/y Cylc2+/- and Cylc1-/y Cylc2-/-) at the levels of male fertility, cellular, and subcellular levels to support the conclusion of the study. While spermatogenesis appeared undisturbed, with germ cells of all types detected in the testis, low sperm counts in epididymis were observed. Mice were subfertile or infertile in a dose-dependent manner where fewer functional alleles had more severe phenotypes; the loss of Cylc2 was less tolerated than the loss of Cylc1. Thus, loss of Cylc1, and to an even greater extent, loss of Cylc2, leads to sperm structure anomalies and decreased sperm motility. Particularly, the sperm head and sperm head-neck region are affected, with calyx not forming in the absence of Cylicins, the acrosomal region being attached more loosely, and the sperm head itself appearing structurally rounder and shorter. Furthermore, manchette, which disassembles during spermiogenesis, persists in mature sperm of mice missing Cylc2. It is interesting that the study identifies a human male that has mutations in both CYLC1 and CYLC2 genes and suffers from infertility, with similar motility and sperm structure defects compared to the mouse models. CYLC1 in the sperm from the infertile patient sperm is absent, providing evidence that in both rodents and primates, Cylicins are essential for male fertility. Evolutionary analysis of two genes adds an interesting point. The authors show that the reason for the loss of Cylc2 being more severe is due to the higher conservation of Cylc2 compared to Cylc1 in rodents and primates.

Overall, the work highlights the relevance and importance of Cylicins in male infertility and advances our understanding of perinuclear theca formation during spermiogenesis.

Joint Public Review:

In this manuscript, Karl et al. explore mechanisms underlying the activation of the receptor tyrosine kinase FGFR1 and stimulation of intracellular signaling pathways in response to FGF4, FGF8, or FGF9 binding to the extracellular domain of FGFR1. The manuscript demonstrates that FGF4, FGF8, and FGF9 exhibit distinct binding modes towards FGFRs. It is also proposed that FGF8 exhibits "biased ligand" characteristics that is manifested via binding and activation FGFR1 mediated by unproven and speculative "structural differences in the FGF-FGFR1 dimers, which impact the interactions of the FGFR1 trans membrane helices, leading to differential recruitment and activation of the downstream signaling adapter FRS2".

Reviewer #1 (Public Review):

Summary:<br /> The authors use insights into the dynamics of the PKA kinase domain, obtained by NMR experiments, to inform MD simulations that generate an energy landscape of PKA kinase domain conformational dynamics.

Strengths:<br /> The authors integrate strong experimental data through the use of state-of-the-art MD studies and derive detailed insights into allosteric communication in PKA kinase. Comparison of wt kinase with a mutant (F100A) shows clear differences in the allosteric regulation of the two proteins. These differences can be rationalized by NMR and MD results.

Weaknesses:<br /> The very detailed insights gained by the authors into allosteric regulation require very specialized techniques in this study. This poses a challenge to communicate the methods, the results, and the meaning of the results to a broader audience. In some places, the authors overcome this challenge better than in others.

Reviewer #1 (Public Review):

Chen and colleagues investigated ZC3H11A as a potential cause of high myopia (HM) in humans through the analysis of exome sequencing in 1,015 adolescents and experiments involving Zc3h11a knock-out mice. The authors showed four possibly pathogenic missense variants in four adolescents with HM. After that, the authors presented the phenotypic features of Zc3h11a knock-out mice, the result of RNA-sequencing, and a comparison of mRNA and protein levels of the functional candidates between wild-type and Zc3h11a knock-out mice. Based on their observations, the authors concluded that ZC3H11A protein contributes to the early onset of myopia.

The strengths of this manuscript include: (1) successful identification of characteristic ophthalmic phenotypes in Zc3h11a knock-out mice, (2) demonstration of biological features related to myopia, such as PI3K-AKT and NF-kB pathways, and (3) inclusion of supporting human genetic data in individuals with HM. On the other hand, the weaknesses of this paper appear to be: (1) the lack of robust evidence from their genomic analysis, and (2) insufficient evidence to support phenotypic similarity between humans with ZC3H11A mutations and Zc3h11a knock-out mice. Given that the biological mechanisms of high myopia are not fully understood, the identification of a novel gene is valuable. As described in the manuscript, it is worth noting that the previous study using myopic mouse model has implicated the role of ZC3H11A in the etiology of myopia (Fan et al. Plos Genet 2012).

Specific comments:<br /> 1. I am concerned about the certainty of similarity in phenotypes between individuals with ZC3H11A mutation and Zc3h11a knock-out mice. A crucial point would be that there are no statistical differences in axial lengths (ALs) between wild-type and Zc3h11a knock-out mice at 8W and 10W, even though ALs in the individuals with ZC3H11A mutation were long. I would also like to note that the phenotypic information of these individuals is not available in the manuscript, although the authors indicated the suppressed b-wave amplitude in Zc3h11a knock-out mice. Considering that the authors described that "Detailed ophthalmic examinations were performed (lines: 321-323)", the detailed clinical features of these individuals should be included in the manuscript.

2. The term "pathogenic variant" should be used cautiously. Please clarify the pathogenicity of the reported variants in accordance with the ACMG guideline.

3. The genetic analysis does not fully support the claim that ZC3H11A is causative for HM. While the authors showed the rare allele frequencies and high CADD scores (> 20) of the identified variants, these were insufficient to establish causality. A helpful way to assess the causality would be performing a segregation analysis. An alternative approach is to show significant association by performing a gene-level association test. Assessing the pathogenicity of the variants using various prediction software, such as SIFT, PolyPhen2, and REVEL may also provide additional supportive evidence.

4. As shown in Figure 2, significant differences in refraction were observed from 4 weeks to 10 weeks. Nevertheless, no differences were observed in AL, anterior/vitreous chamber depth, and lens depth. The author should experimentally clarify what factors contribute to the observed difference in refraction.

5. The gene names should be italicized throughout the manuscript.

6. Table 1: providing chromosomal positions and rs numbers (if available) would be helpful for readers.

7. Figure 5b, c, and d: the results of pathway analysis and GO enrichment analysis are difficult to interpret due to the small font size. It would be preferable to present these results in tables. Moreover, the authors should set a significant threshold in the enrichment analyses.

Joint Public Review:

The authors explored previously developed pan-resolution x-ray tomographic imaging pipelines for quantitative analysis of thousands of blood cells within 4 and 5 dpf zebrafish. By performing automatic segmentation of individual cells within the zebrafish embryo, the authors tried to demonstrate the applicability of x-ray tomography to quantitative analysis of cell phenotypes at the tissue level. The combination of random forest classification and automatic segmentation based on cell pose is promising, especially considering the open access and the general applicability of these tools. However, the key features claimed by the authors, that is, visualisation of all blood cells in the embryo and quantitative analysis of blood cell phenotypes, were not sufficiently supported by the presented data. Additionally, I see limitations in applicability to other cell types, as mentioned by authors as well, and similar analysis on other organisms due to differences in cell size, packing, and tissue background.

When supported by additional data, the manuscript has the potential to be a useful pipeline for cell phenotype analysis and an impactful method for the zebrafish community and beyond.

Major points:<br /> 1. The authors report that pan-resolution x-ray tomography enables visualisation of blood cells in the whole zebrafish embryo. These observations are based on a comparative analysis of EM data and histology with x-ray tomography. Not EM, nor histology shows the distribution of all blood cells (or comparable volume) as in x-ray tomography. At this point, it would be important to supplement the work with the 3D distribution of blood cells visualized by complementary methods, for example, light-sheet microscopy. Such data can be compared to the cells visualized by x-ray tomography like in Figure 6 in terms of cell numbers and distribution throughout the organs. Without such comparative analysis, it is unclear whether X-ray tomography visualizes all blood cells in the organism.

2. Some critical information is missing for the optimisation of automatic segmentation. For example, how was the manual segmentation performed? For example, how cells of 3 pixels in diameter were segmented (Figure 8)? On how many cells? Taking that the F1 score is often biologically not meaningful, see Lena Maier-Hein, Bjoern Menze, et al. it would be important to make careful evaluation of segmentation results. For example, in Figure 2 it would be important to add the histogram of volume distribution in these datasets not just one mean value. The same type of histogram would be important to add to Figure 5 and compare these results to Figure 2.

3. For the comparison of blood cell shape between different samples, there is a lack of statistics and validation. How many embryos per condition were used? Considering that blood cells should be possible to obtain from zebrafish embryos. It would be important to see something like FACs data on blood cells from the same type of specimens. Would the size distribution obtained by FACs be comparable to X-ray tomography data? Without validation by other methods and statistically meaningful analysis, the results from x-ray tomography are simply not substantiated.

Minor points:<br /> 1. Please put some details on the parameters and usage of Cellpose.

2. The claim in the Discussion on 'was able to show differences between data sets sufficient to classify new, unknown blood cells into these groups' is not supported by the data.

3. The key resource table should include all reagents, including sample preparation. This resource table should also include data sets as a resource, which are currently in the 'Data availability statement'.

4. Provide tables with the results on manual segmentation, automatic segmentation, and analysis of cellular phenotypes used for LDA.

Reviewer #1 (Public Review):

Using a combination of structural biology methods, this report aims to describe the auto-inhibited architecture of kinesin 1 either as homodimers or hetero-tetramers. Hence, the multiple contacts between the protein domains and their folding pattern are addressed using cross-linking mass spectrometry (XL-MS), negative stain electron microscopy and Alpha Fold-based structure prediction. Based on the existing literature, the key domains and amino acids responsible for kinesin-1 inhibited state were not clearly deciphered. The synergetic use of different methods now seems to describe in detail the molecular cues that could induce kinesin-1 refolding and opening. Multiple interactions between the different domains seem to induce the folded conformation.

The combination of methodologies is an efficient way to unravel details that could not be addressed previously. The paper is well written. The methods for generating the electron microscopy data and its relevance and quality, for instance, are much better described after revision. In addition, the conclusions are now more convincing because similar investigations are carried out for all isoforms (KIF5B and FIF5C) in parallel.

This article raises the potential strength and power of deep learning structure prediction methods combined simultaneously with other structural biology methods to answer specific questions. In the present context, this study will certainly be helpful in revealing and understanding the activation mechanism of kinesin motor proteins.

Reviewer #1 (Public Review):

Summary<br /> This article by Zhai et al, investigates sterol transport in bacteria. Synthesis of sterols is rare in bacteria but occurs in some, such as M capsulatus where the sterols are found primarily in the outer membrane. In a previous paper the authors discovered an operon consisting of five genes, with two of these genes encoding demethylases involved in sterol demethylation. In this manuscript, the authors set out to investigate the functions of the other three genes in the operon. Interestingly, through a bioinformatic analysis, they show that they are an inner membrane transporter of the RND family, a periplasmic binding protein, and an outer membrane-associated protein, all potentially involved with lipid transport, so providing a means of transporting the lipids to the outer membrane. These proteins are then extensively investigated through lipid pulldowns, binding analysis on all three, and X-ray crystallography and docking of the latter two.

Strengths<br /> The lipid pulldowns and associated MST binding analysis are convincing, clearly showing that sterols are able to bind to these proteins. The structures of BstB and BstC are high resolution with excellent maps that allow docking studies to be carried out. These structures are distinct from sterol-binding proteins in eukaryotes.

Weaknesses<br /> While the docking and molecular dynamics studies are consistent with the binding of sterols to BstB and BstC, this is not backed up particularly well. The MST results of mutants in the binding pocket of BstB have relatively little effect, and while I agree with the authors this may be because of the extensive hydrophobic interactions that the ligand makes with the protein, it is difficult to make any firm conclusions about binding.

The authors also discuss the possibility of a secondary binding site in BstB based on a slight cavity in domain B next to a flexible loop. This is not backed up in any way and seems unlikely.

Reviewer #1 (Public Review):

In this manuscript, the authors report a molecular mechanism for recruiting syntaixn 17 (Syn17) to the closed autophagosomes through the charge interaction between enriched PI4P and the C-terminal region of Syn17. How to precisely control the location and conformation of proteins is critical for maintaining autophagic flux. Particularly, the recruitment of Syn17 to autophagosomes remains unclear. In this paper, the author describes a simple lipid-protein interaction model beyond previous studies focusing on protein-protein interactions. This represents conceptual advances.

Reviewer #1 (Public Review):

Summary:<br /> The organization of cell surface receptors in membrane nanodomains is important for signaling, but how this is regulated is poorly understood. In this study, the authors employ TIRFM single-molecule tracking combined with multiple analyses to show that ligand exposure increases the diffusion of the immune receptor FLS2 in the plasma membrane and its co-localization with remorin REM1.3 in a manner dependent on the phosphosite S938. They additionally show that ligand increases the dwell time of FLS2, and this is linked to FLS2 endocytosis, also in a manner dependent on S938 phosphorylation. The study uncovers a regulatory mechanism of FLS2 localization in the nanodomain crucial for signaling.

Strengths:<br /> TIRFM single-molecule tracking, FRAP, FRET, and endocytosis experiments were nicely done. The role of S938 phosphorylation is convincing.

Weaknesses:<br /> 1. The model suggests that S938 is phosphorylated upon flg22 treatment. This is actually not known. In addition, the S938D mutant does not show constitutively increased diffusion and co-localization with remorin. It is necessary to soften the tone in the conclusion.

2. The introduction (only two paragraphs) and discussion are not properly written in the context of the current understanding of plant receptors in nanodomains. The authors basically just cited a few publications of their own, and this is not acceptable.

Reviewer #1 (Public Review):

In recent years, these investigators have been engaged in a debate regarding the classification of the sacral parasympathetic system as "sympathetic" rather than "parasympathetic," based on shared developmental ontogeny of spinal preganglionic neurons. In this current study, these investigators conducted single-cell RNAseq analyses of four groups of autonomic neurons: paravertebral sympathetic neurons (stellate and lumbar train ganglia), prevertebral sympathetic neurons (coeliac-mesenteric ganglia), rostral parasympathetic ganglia (sphenopalatine ganglia), and the caudal pelvic ganglia (containing traditionally recognized sacral "parasympathetic cholinergic neurons," which the investigators sought to challenge in terms of nomenclature). The authors argued that the pelvic ganglionic neurons shared the expression of more genes with sympathetic ganglia, as opposed to parasympathetic ganglia. Additionally, the pelvic neurons did not express a set of genes observed in the rostral parasympathetic sphenopalatine ganglia. Based on these findings, they claimed that the sacral autonomic system should be considered sympathetic rather than parasympathetic. However, these arguments face significant challenges.

Firstly, among the P1-4 clusters of pelvic neurons, the P3 cluster predominantly represents noradrenergic sympathetic neurons, known to be present in pelvic ganglia. These neurons share gene expression patterns typically found in sympathetic neurons and lack the key cholinergic features identified in the P1, P2, and P4 clusters. Consistently, the P3 cluster of neurons is located close to sympathetic neuron clusters on the map, echoing the conventional understanding that the pelvic ganglia are mixed, containing both sympathetic and parasympathetic neurons.

Secondly, as mentioned above, the P1, P2, and P4 clusters are cholinergic neurons, expressing ChAT (and VIP). The authors claimed that these neurons shared a large set of genes expressed in sympathetic neurons (class I genes shown in Figure 1B). A closer look at the expression showed that some genes are expressed at higher levels in sympathetic neurons and in P2 cluster neurons, but much weaker in P1, P2, and P4 neurons, such as Islet1 and GATA2, and the opposite is true for SST. Another set of genes is expressed weakly across clusters, like HoxC6, HoxD4, GM30648, SHISA9, and TBX20. Since the pelvic ganglia are in a caudal body part, it is not surprising to have genes expressed in pelvic ganglia, but not in rostral sphenopalatine ganglia, and vice versa (to have genes expressed in sphenopalatine ganglia, but not in pelvic ganglia), according to well recognized rostro-caudal body patterning, such as nested expression of hox genes.

Thirdly, noradrenergic sympathetic neurons and cholinergic neurons, by virtue of expressing different neurotransmitters, could have distinct roles. It is true that some cholinergic neurons reside in the sympathetic train ganglia as well, such as those innervating the sweat gland and some vascular systems; in this sense, the pelvic ganglia share some features with sympathetic ganglia, except that the pelvic ganglia contain a much higher percentage of cholinergic neurons compared with sympathetic ganglia. It is much simpler and easier to divide the autonomic nervous system into sympathetic neurons that release noradrenaline versus parasympathetic neurons that release acetylcholine, and these two systems often act in antagonistic manners, though in some cases, these two systems can work synergistically. It also does not matter whether or not pelvic cholinergic neurons could receive inputs from thoracic-lumbar preganglionic neurons (PGNs), not just sacral PGNs; such occurrence only represents a minor revision of the anatomy. In fact, it makes much more sense to call those cholinergic neurons located in the sympathetic chain ganglia parasympathetic. Thus, from the functionality point of view, it is not justified to claim that "pelvic organs receive no parasympathetic innervation".

Reviewer #1 (Public Review):

Summary: Seizure stimuli has long been recognized to exhibit potent effects on adult neurogenesis, from depletion of the NSC pool to promoting aberrant migration of adult-born neurons. However, the identity and source of extrinsic signals is still incompletely understood. The work by Noguchi et al., demonstrates that Shh from mossy cells is a major source of Shh signaling after KA-mediated acute seizures. This work is interesting because mossy cells undergo hyperactivation during seizures, so this study provides a mechanistic link between mossy cell neuronal activity control of neurogenesis through Shh signaling. Weaknesses are that only male mice were analyzed in the seizure induction experiments and several control groups are missing for seizure induction, tamoxifen induction, and the DREADD experiment.

Strengths:

1. The study uses rigorous and specific genetic approaches (e.g., GliLacZ/+ mice; ShhEGFP-Cre/+ mice; mossy cell selective conditional Shh knockout using Crlr-Cre mice) to demonstrate Shh signaling is activated by seizures in mossy cells and contributes to aberrant neurogenesis.

2. Use of DREADDs (Crlr-Cre; hM3Dq) to show mossy cells control adult neurogenesis through Shh in an activity-dependent manner.

3. Demonstration that Shh deletion in mossy cells leads to reduction of the NSC pool uses stringent methods and analysis, including BrdU pulse-chase and co-labeling with NSC markers.

Weaknesses:

1. The analysis of Shh deletion in mossy cells and influences of aging related NSC pool decline is not well connected with the rest of the study on the expression/requirement of Shh in mossy cells to regulate seizure-induced neurogenesis. To promote cohesion, the authors should examine/discuss what happens to mossy cells during aging - it is similar or different to what happens to mossy cell neuronal activity during seizures?

2. Only male mice were analyzed in the seizure induction experiments, leaving open the possibility of sex differences since previous reports suggest sex differences in adult neurogenesis.

3. Several control groups are missing:<br /> -For seizure induction: missing vehicle (instead of no KA treatment).<br /> -For TAM induction: missing corn oil only to check leakiness and specificity of transgene.<br /> -For DREADD experiment: missing vehicle (to control for hM3 non-specific effects)

Reviewer #1 (Public Review):

In this paper, the authors evaluate the utility of brain-age-derived metrics for predicting cognitive decline by performing a 'commonality' analysis in a downstream regression that enables the different contribution of different predictors to be assessed. The main conclusion is that brain-age-derived metrics do not explain much additional variation in cognition over and above what is already explained by age. The authors propose to use a regression model trained to predict cognition ("brain-cognition") as an alternative suited to applications of cognitive decline. While this is less accurate overall than brain age, it explains more unique variance in the downstream regression.

Comments on revised version:

I thank the authors for addressing many of my concerns with this revision. However, I do not feel they have addressed them all. In particular I think the authors could do more to address the concern I raised about the instability of the regression coefficients and about providing enough detail to determine that the stacked regression models do not overfit.

In considering my responses to the authors revision, I also must say that I agree with Reviewer 3 about the limitations of the brain age and brain cognition methods conceptually. In particular that the regression model used to predict fluid cognition will by construction explain more variance in cognition than a brain age model that is trained to predict age. To be fair, these conceptual problems are more widespread than this paper alone, so I do not believe the authors should be penalised for that. However, I would recommend to make these concerns more explicit in the manuscript.

Reviewer #1 (Public Review):

Referring to previous research findings, the authors explain the connection between NINJ1 and MVs. Additional experiments and clarifications will strengthen the conclusions of this study.

Below are some comments I feel could strengthen the manuscript:

1. The authors mentioned their choice of using heterozygous NINJ1+/- mice on page 4, because of lethality and hydrocephalus. Nonetheless, there is a substantial number of references that use homozygous NINJ1-/- mice. Could there be any other specific reasons for using heterozygous mice in this study?

2. Figure S2 clearly shows the method of pyroptosis induction by flagellin. It is also necessary as a prerequisite for this paper to show the changes in flagellin-induced pyroptosis in heterozygous NINJ1+/- mice.

3. IL-1ß levels controlled by GSDMD were not affected by NINJ1 expression according to previous studies (Ref 37, 29, Nature volume 618, pages 1065-1071 (2023)). GSDMD also plays an important role in TF release in pyroptosis. Are GSDMD levels not altered in heterozygous NINJ1 +/- mice?

4. In Fig 1 F, the authors used a fibrin-specific monoclonal antibody for staining fibrin, but it's not clearly defined. There may be some problem with the quality of antibody or technical issues. Considering this, exploring alternative methods to visualize fibrin might be beneficial. Fibrin is an acidophil material, so attempting H&E staining or Movat's pentachrome staining might help for identify fibrin areas.

Reviewer #1 (Public Review):

Summary:<br /> The study conducted on mice establishes a noteworthy connection between dietary protein intake and resistance exercise impact on metabolic health and muscle development. In sedentary mice, a diet rich in protein resulted in excessive fat accumulation and compromised blood sugar regulation in comparison to a diet low in protein. Intriguingly, when mice followed the high protein diet alongside progressive resistance training, they exhibited protection against surplus fat gain, though blood glucose regulation remained impaired. The research also revealed that resistance training notably enhanced muscle hypertrophy induced by exercise, particularly in mice on the high protein diet. Although the maximum strength achieved was similar across diets, this highlights the potential synergy between high protein consumption and resistance exercise in promoting skeletal muscle growth.

Strengths:<br /> The study possesses several significant strengths. Firstly, it combines controlled dietary manipulations with resistance exercise, providing a comprehensive understanding of their combined effects on metabolic health and muscle growth. The use of mouse models, while not directly translatable to humans, offers a controlled experimental environment, enabling precise measurements and observations. Moreover, the study reveals nuanced outcomes such as the differential impact of high protein intake on adiposity and muscle hypertrophy. The emphasis on both positive and negative findings lends balance to the conclusions, enhancing the overall credibility of the study. Additionally, the clear delineation of diet-exercise interactions contributes to the broader understanding of dietary and exercise recommendations for metabolic health and muscle development.

Weaknesses:<br /> Certain limitations warrant consideration. Firstly, the study's exclusive reliance on mice might limit the generalizability of the findings to humans due to inherent physiological differences. Additionally, the absence of direct investigation into the underlying molecular mechanisms responsible for the observed outcomes leaves room for speculation. Moreover, the research's concentration on male and young mice raises questions about the applicability of these findings to female and older subjects. Lastly, the study's duration and the specific resistance exercise protocol utilized might not fully reflect long-term human scenarios, underscoring the need for further research in more diverse populations and over extended timeframes.

Reviewer #1 (Public Review):

Building on previous work from the Tansey lab, here Howard et al. characterize transcriptional and translational changes upon WIN site inhibition of WDR5 in MLL-rearranged cancer cells. They first analyze whether C16, a newer generation compound, has the same cellular effects as C6, an early generation compound. Both compounds reduce the expression of WDR5-bound RPGs in addition to the unbound RPG RPL22L1. They then investigate differential translation by ribo-seq and observe that WIN site inhibition reduces the translational RPGs and other proteins related to biomass accumulation (spliceosome, proteasome, mitochondrial ribosome). Interestingly, this reduction adds to the transcriptional changes and is not limited to RPGs whose promoters are bound by WDR5. Quantitative proteomics at two-time points confirmed the downregulation of RPGs. Interestingly, the overall effects are modest, but RPL22LA is strongly affected. Unexpectedly, most differentially abundant proteins seem to be upregulated 24 h after C6 (see below). A genetic screen showed that loss of p53 rescues the effect of C6 and C16 and helped the authors to identify pathways that can be targeted by compounds together with WIN site inhibitors in a synergistic way. Finally, the authors elucidated the underlying mechanisms and analyzed the functional relevance of the RPL22, RPL22L1, p53, and MDM4 axis.

While this work is not conceptually new, it is an important extension of the observations of Aho et al. The results are clearly described and, in my view, very meaningful overall.

Major points:<br /> 1. The authors make statements about the globality/selectivity of the responses in RNA-seq, ribo-seq, and quantitative proteomics. However, as far as I can see, none of these analyses have spike-in controls. I recommend either repeating the experiments with a spike-in control or carefully measuring transcription and translation rates upon WIN site inhibition and normalizing the omics experiments with this factor.

2. Why are the majority of proteins upregulated in the proteomics experiment after 24 h in C6 (if really true after normalization with general protein amount per cell)? This is surprising and needs further explanation.

3. The description of the two CRISPR screens (GECKO and targeted) is a bit confusing. Do I understand correctly that in the GECKO screen, the treated cells are not compared with non-treated cells of the same time point, but with a time point 0? If so, this screen is not very meaningful and perhaps should be omitted. Also, it is unclear to me what the advantages of the targeted screen are since the targets were not covered with more sgRNAs (data contradictory: 4 or 10 sgRNAs per target?) than in Gecko. Also, genome-wide screens are feasible in culture for multiple conditions. Overall, I find the presentation of the screening results not favorable.

4. Can Re-expression of RPL22 rescue the growth arrest of C6?.

Reviewer #1 (Public Review):

Summary:<br /> In the manuscript titled "Disease modeling and pharmacological rescue of autosomal dominant Retinitis Pigmentosa associated with RHO copy number variation" the authors describe the use of patient iPSC-derived retinal organoids to evaluate the pathobiology of a RHO-CNV in a family with dominant retinitis pigmentosa (RP). They find significantly increased expression of rhodopsin, especially within the photoreceptor cell body, and defects in photoreceptor cell outer segment formation/maturation. In addition, they demonstrate how an inhibitor of NR2E3 (a rod transcription factor required for inducing rhodopsin expression), can be used to rescue the disease phenotype.

Strengths:<br /> The manuscript is very well written, the illustrations and data presented are compelling, and the authors' interpretation/discussion of their findings is logical.

Weaknesses:<br /> A weakness, which the authors have addressed in the discussion section, is the lack of an isogenic control, which would allow for direct analysis of the RHO-CNV in the absence of the other genetic sequence contained within the duplicated region. As the authors suggest, CRISPR correction of a large CNV in the absence of inducing unwanted on-target editing events in patient iPSCs is often very challenging. Given that they have used a no-disease iPSC line obtained from a family member, controlled for organoid differentiation kinetics/maturation state, and that no other complete disease-causing gene is contained within the duplicated region, it is unlikely that the addition of an isogenic control would yield significantly different results.

Aims and conclusions:<br /> This reviewer is of the opinion that the authors have achieved their aims and that their results support their conclusions.

Discussion:<br /> The authors have provided adequate discussion on the utility of the methods and data as well as the impact of their work on the field.

Reviewer #1 (Public Review):

Summary:<br /> Spinal cord injury (SCI) causes immediate and prolonged bladder dysfunction, for which there are poor treatments. Following up on evidence that AMPA glutamatergic receptors play a key role in bladder function, the authors induced spinal cord injury and its attendant bladder dysfunction and examined the effects of graded doses of allosteric AMPA receptor activators (ampakines). They show that ampakines ameliorate several prominent derangements in bladder function resulting from SCI, improving voiding intervals and pressure thresholds for voiding and sphincter function.

Strengths:<br /> Well-performed studies on a relevant model system. The authors induced SCI reproducibly and showed that they had achieved their model. The drugs revealed clear and striking effects. Notably, in some mice that had such bad SCI that they could not void, the drug appeared to restore voiding function.

Weaknesses:<br /> The studies are well conducted, but it would be helpful to include information on the kinetics of the drugs used, their half-life and how long they are present in rats after administration. What blood levels of the drugs are achieved after infusion? How do these compare with blood levels achieved when these drugs are used in humans?

Reviewer #1 (Public Review):

The process of EMT is a major contributor to metastasis and chemoresistance in breast cancer. By using a modified PyMT model that allows the identification of cells undergoing EMT and their decedents via S100A4-Cre mediated recombination of the mTmG allele, Ban et al. tackle a very important question of how tumor metastasis and therapy resistance by EMT can be blocked. They identified that pathways associated with ribosome biogenesis (RiBi) are activated during transition cell states. This finding represents a promising therapeutic target to block any transition from E to M (activated during cell dissemination and invasion) as well as from M to E (activated during metastatic colonization). Inhibition of RiBi-blocked EMT also reduced the establishment of chemoresistance that is associated with an EMT phenotype. Hence, RiBi blockage together with standard chemotherapy showed synergistic effects, resulting in impaired colonization/metastatic outgrowth in an animal model. The study is of great interest and of high clinical relevance as the authors show that blocking the transition from E to M or vice versa targets both aspects of metastasis, dissemination from the primary tumor, and colonization in distant organs.

The study is done with high skill using state-of-the-art technology and the conclusions are convincing and solid, but some aspects require some additional experimental support and clarification. It remains elusive whether blocking of EMT/MET is necessary for the synergistic effect of standard chemotherapy together with RiBi blockage or whether a general growth disadvantage of RiBi-treated cells independent of blocking transition is responsible. How can specific effects on state transition by RiBI block be separated from global effects attributed to overall reduced protein biosynthesis, proliferation etc.? Some other aspects are misleading or need extension.

Reviewer #1 (Public Review):

Summary: This study presents fundamental new insights into vesicular monoamine transport and the binding pose of the clinical drug tetrabenazine (TBZ) to the mammalian VMAT2 transporter. Specifically, this study reports the first structure for the mammalian VMAT (SLC18) family of vesicular monoamine transporters. It provides insights into the mechanism by which this inhibitor traps VMAT2 into a 'dead-end' conformation. The structure also provides some evidence for a novel gating mechanism within VMAT2, which may have wider implications for understanding the mechanism of transport in the wider SLC18 family.

Strengths: The structure is high quality, and the method used to determine the structure via fusing mVenus and the anti-GFP nanobody to the amino and carboxyl termini is novel. The binding and transport data are convincing, although limited. The binding position of TBZ is of high value, given its role in treating Huntington's chorea and for being a 'dead-end' inhibitor for VMAT2.

Weaknesses: The lack of additional mutational data and/or analyses on the impact of pH on ligand binding reduces the insights from these experiments. This reduces the strength of the conclusions that can be drawn about the mechanism of binding and transport or the novelty of the gating mechanism discussed above.

Joint Public Review:

Bull et al aimed to use data from observational studies and mendelian randomisation to explore if changes in circulating metabolites are associated with colorectal cancer development. As Mendelian randomisation uses information on genetic variations which are fixed at birth, it is less vulnerable to confounding than standard observational studies.

Overall, a major strength of the study is that it uses data from large cohort studies, one from childhood, adolescence, and early adulthood when the incidence of colorectal cancer is very low (reducing the likelihood of reverse causation) and before medication (such as statins which have the potential to affect metabolite levels) has been initiated.

This study has some weaknesses which have been acknowledged by the authors. Although the findings of this study indicate the potentially significant role that polyunsaturated fatty acids may have in colorectal cancer risk, the genes and therefore also the genetic variations (SNPs) associated with fatty acids often produce an effect for more than one fatty acid which may introduce bias. This together with the fact that there was limited information available on many specific fatty acids which are known causative metabolites for colorectal cancer, makes it difficult to establish with confidence which specific classes of fatty acids could potentially play a causative role in these associations. Also, the study populations are majority white European descent which may limit the generalizability of these findings to other populations.

The methodology used was largely acceptable to achieve the aims set out and the findings have shown an association between polyunsaturated fat levels and genetic liability to colorectal cancer.<br /> Overall, this is an important piece of work which has the potential to contribute to our understanding of the causal relationship between circulating metabolites at different stages of the life cycle and colorectal cancer risk as it would be extremely difficult to gather such evidence using other study designs. It opens the door for future research aiming to better understand the role that these metabolites could play in colorectal cancer risk prediction and in turn help identify groups of individuals who would benefit most from prevention and early detection interventions.

This work will be of interest not only to epidemiologists working in the area of GI tract cancers but also those interested in the different applications for mendelian randomisation within cancer epidemiology research.

Reviewer #1 (Public Review):

Summary: The authors seek to establish what aspects of nervous system structure and function may explain behavioral differences across individual fruit flies. The behavior in question is a preference for one odor or another in a choice assay. The variables related to neural function are odor responses in olfactory receptor neurons or in the second-order projection neurons, measured via calcium imaging. A different variable related to neural structure is the density of a presynaptic protein BRP. The authors measure these variables in the same fly along with the behavioral bias in the odor assays. Then they look for correlations across flies between the structure-function data and the behavior.

Strengths: Where behavioral biases originate is a question of fundamental interest in the field. In an earlier paper (Honegger 2019) this group showed that flies do vary with regard to odor preference, and that there exists neural variation in olfactory circuits, but did not connect the two in the same animal. Here they do, which is a categorical advance, and opens the door to establishing a correlation. The authors inspect many such possible correlations. The underlying experiments reflect a great deal of work, and appear to be done carefully. The reporting is clear and transparent: All the data underlying the conclusions are shown, and associated code is available online.

Weaknesses: The results are overstated. The correlations reported here are uniformly small, and don't inspire confidence that there is any causal connection. The main problems are<br /> 1. The target effect to be explained is itself very weak. Odor preference of a given fly varies considerably across time. The systematic bias distinguishing one fly from another is small compared to the variability. Because the neural measurements are by necessity separated in time from the behavior, this noise places serious limits on any correlation between the two.<br /> 2. The correlations reported here are uniformly weak and not robust. In several of the key figures, the elimination of one or two outlier flies completely abolishes the relationship. The confidence bounds on the claimed correlations are very broad. These uncertainties propagate to undermine the eventual claims for a correspondence between neural and behavioral measures.<br /> 3. Some aspects of the statistical treatment are unusual. Typically a model is proposed for the relationship between neuronal signals and behavior, and the model predictions are correlated with the actual behavioral data. The normal practice is to train the model on part of the data and test it on another part. But here the training set at times includes the testing set, which tends to give high correlations from overfitting. Other times the testing set gives much higher correlations than the training set, and then the results from the testing set are reported. Where the authors explored many possible relationships, it is unclear whether the significance tests account for the many tested hypotheses. The main text quotes the key results without confidence limits.

Reviewer #1 (Public Review):

Erbacher and colleagues provide further evidence for the function of epithelial cells as major contributors to the transduction of sensory stimuli. This technically advanced imaging study of human skin advances support for the anatomical and functional association of nerve fibers and skin keratinocytes. With combined high-resolution imaging and immunolabeling, the authors also advance the idea that gap junctions are at least one means by which direct neurochemical (e.g., ATP) communication from stimulated keratinocytes to nerve fibers can be achieved.

A major strength of the study is the combined use of super-resolution array tomography (srAT), expansion microscopy, structured illumination microscopy and immunolabeling to analyze human skin in situ as well as co-cultures of human neurons and keratinocytes. High resolution static and video imaging of skin clearly supports the ensheathment by keratinocytes of nerve fiber projections as they traverse layers of the epidermis. Another strength of this study is the srAT imaging combined with connexin Cx43 immunolabeling that focus on sites of nerve fiber-keratinocyte contact zones. Imaging of Cx43+ plaques support these sites as regions of direct epithelial-neural contact and as such, of communication.

Although imaging data support Cx43+/connexin plaques and neural ensheathment as regions of direct epithelial-neural communication, e.g., via keratinocyte release of ATP, this relationship remains correlative and lacking in quantification.

The conclusion of this paper regarding the anatomical relationship between nerves and keratinocytes is well supported. Data also support the proposal of connexin plaques as sites of communication, although analyses that validate this relationship, using experimental models and in human samples, remain for future studies.

Reviewer #1 (Public Review):

The authors provide compelling evidence that the activation of distinct populations of NTS neurons provides stronger decreases in eating/body weight when co-activated. Avoidance is not necessarily linked to the extent of the effects but seems to depend on specific neurons which when activated, not only reduce eating but also induce avoidance reactions. The results of this study provide strong data promoting multi-targeted approaches to reduce eating and body weight in obesity. Interestingly, none of the pathways identified is necessary for the weight-reducing effect of vertical sleeve gastrectomy. Future studies will hopefully shed light on the type of neurotransmitters released by these distinct populations of NTS neurons.

Reviewer #1 (Public Review):

Retinal ganglion cells are diverse. In recent years it was recognized that several subtypes are intrinsically photoresponsive (ipRGCs). In earlier work, it was suggested that hyperpolarization-activated channels (HCN) were the main responsive element contributing to generating the photocurrents that activate signaling by these cells. Other groups, including the authors, have shown evidence that other ionic mechanisms might be in play.

In the current manuscript, the authors present a thorough and careful characterization of the electrophysiology of two types of ipRGCs, M2, and M4. Both pharmacological and genetic ablation of specific ion channels in mice were employed along with posthoc identification of cell types. The authors identify an important experimental problem with one of the drugs employed previously to suggest the participation of HCN channels. This discovery leads the authors to suggest that in M4 ipRGCs, the depolarization induced by light is produced by activation of TRPC channels and inhibition of a leak of potassium channels. Importantly, prolonged application of the HCN channel blocker produced off-target (non-HCN related) effects that can explain previous results.

The authors go on to explore the responses of M2-type ganglion cells and also uncover the important participation of TRPC channels as well as a previously unrecognized role for T-type calcium channels. Since the authors also use pharmacological tools to uncover the participation of calcium channels in M2 cells, they make sure that the drugs employed do not produce off-target effects in cells where the ionic basis of the photocurrent is better established, namely the M1 type.<br /> The author's evidence as a whole is convincing, and should be a major contribution to understanding the physiology of ipRGCs, but should be confirmed by other groups with different experimental approaches.

Reviewer #1 (Public Review):

In this study, Chi et al. present a study on ctDNA profiling to predict the prognosis and treatment response of mTNBC patients. The authors report that ctDNA+ status and baseline ctDNA-related markers (MATH score and ctDNA%) are associated with the survival and treatment response. The data are well presented. However, some questions related to the association between ctDNA and clinical outcomes, and a lack of an external cohort to validate the predictive value of ctDNA need to be addressed. The Methods section also needs to be detailed.

Reviewer #1 (Public Review):

This study set out to test the causal involvement of the OFC in detecting auditory prediction errors at two levels of abstraction. The authors recorded EEG in patients with OFC damage and healthy age matched controls while they listened for deviations in sequences of tones in the Local-Global paradigm. This task can tease apart prediction errors at a local level (ie. within a sequence) and a global level (ie. between sequences). Focusing on the Mismatch Negativity (MMN) ERP component and the P3, which have both been previously linked to detecting violations in expectation and predictions, the study examined differences between neural responses elicited by patients and control subjects in four core conditions 1. standard sequences of tones (XXXXX XXXXX XXXXX XXXXX) that can be predicted both at local and global levels and should result in no prediction errors 2. Local deviations (XXXXY XXXXY XXXXY XXXXY) in which the final tone in the last sequence can only be predicted at the global level and which results in low-level prediction errors 3. Global deviations (XXXXY XXXXY XXXXY XXXXX) in which the final tone of the last sequence can be predicted only at the local level and results in higher level prediction errors. 4. Local+Global deviations (XXXXX XXXXX XXXXX XXXXY) in which the final tone of the last sequence is neither predicted at the global or local level and results in low and high prediction errors.

The timely and well designed study combines casual and correlative experimental methods. This unique strength allows the authors to identify differences in neural processing and link them directly to a specific region of the brain. The task is simple and intuitive, having been well characterized in previous literature. Its use here to investigate prediction errors beyond the typical reward-guided paradigms is particularly novel. As is the focus on the OFC which is often understudied relative to nearby ACC more commonly associated with prediction error coding. These strengths ensure the paper will likely have a wide impact across a number of fields.

The results suggest that OFC patients showed attenuated MMN to violations in local predictions as well as reduced and delayed MMN/P3a complex to combined violations in local and global predictions. By contrast, violations of prediction purely at the global level were preserved in the OFC group. No differences in processing local or global auditory prediction errors were observed in a brain damaged control group with lesions to the LPFC relative to controls. As these results stand they show a clear role of the OFC in the detection of prediction errors. This is particularly clear at the local level of processing.

However, as with many patient lesion studies, while the comparison directly against the healthy age matched controls is critical it would have strengthened the authors claims if they could show differences between the brain damaged control group. Given the previous literature that also links lateral PFC with prediction error detection, I understand that this region is potentially not the clearest brain damaged control group and therefore another lesion group might have strengthened claims of specificity. Furthermore, the authors do not offer an explanation for why no differences between lateral PFC and control groups were found when others have previously reported them. Identifying those differences would strengthen our understanding of the involvement of different structures in this task/function.

Furthermore, I believe it is important for the authors to clarify how the time frames to test for group differences of ERP components were defined. Were the components defined based on a grand average across lesions and controls or based or on the maximum range for both groups? As the paper is written currently this is unclear to me. It is also unclear why the group comparisons between controls and lateral PFC group were based only on the control group. To ensure no inadvertent biases towards the larger control group were introduced and ensure the studies findings were reliable, it would be appreciated if the authors could clarify this.

An additional potential weakness of the paper, and one that if addressed would increase our confidence that neural differences arise because of the specific lesion effect, is the lack of evidence that the lesion and control groups do not differ on measures that could inadvertently bias the neural data. For example, while the groups did not differ on demographics and a range of broad cognitive functions, were there any differences between the number or distribution of bad/noisy channels in each subject between the two groups? Were there differences in the number of blinks/saccades or distribution of blinks or saccades across the conditions in each subject across the two groups. On a similar note, while I appreciate this is a well established task could the authors clarify whether task difficulty is balanced across the different conditions? The authors appear to have used the counting task to ensure equal attention is paid across conditions although presumably the blocks differ in the number of deviant tones and therefore in the task difficulty. Typically, tasks to maintain attention are orthogonal to the main task and equally challenging across the different blocks. Is there a way to reassure readers that this has not affected the neural results.

Finally, one remaining weakness, which plagues all patient studies, is that of anatomical specificity. The authors have analysed what is, for the field, a large group of patients, and while the lesions appear to be relatively focused on the OFC the individuals vary in the degree to which different subregions within the OFC are damaged. This is increasingly important as evidence over the last 10 years has identified functional roles of these specific structures (Rushworth et al 2011, Neuron, Rudebeck et al 2017 Neuron). It would be important to ultimately know whether the detection of prediction errors was specific to a particular OFC subregion, a general mechanism across this area of cortex, or whether different subregions were more involved during different contexts or types of stimuli/contexts/tasks etc. Some comments on this would be appreciated.

In spite of the concerns raised above I believe that the authors have achieved their aims. I hope that by expanding and clarifying the sections outlined above the authors can be even more confident that their results support their conclusions.

As noted above, given the combination of methods and generalisability of the results the study will have a significant impact in a number of fields. I believe the use of an auditory paradigm will remind the community of the value of examining the generalisability of mechanisms across other sensory domains beyond vision. Unfortunately, though the data can not easily be shared (as is typical of patient data). However the authors explain in detail how permission could be sought by individual members of the community if needed.

Finally, while the authors have already cited widely across multiple fields, again speaking to the likely large impact the study will make, there does appear to be an unexplored conceptual link between the conclusions here that the OFC supports "the formation of predictions that define the current task by using context and temporal structure to allow old rules to be disregarded so that new ones can be rapidly acquired" and that lesions of the lateral portions of the OFC disrupt the assignment of credit or value to a stimuli that occurred temporally close to the outcome (Walton et al 2010, Noonan et al 2010, PNAS, Rudebeck et al 2017 Neuron, Noonan et al 2017, JON, Wittmann et al 2023 PlosB, note the wider imaging literature in line with this work Jocham et al 2014 Neuron and Wang et al bioRxiv). Without the OFC monkeys and humans appear to rely on an alternative, global learning mechanism that spreads the reinforcing properties of the outcome to stimuli that occurred further back in time. Could the authors speculate on how these two strains of evidence might converge? For example, does the OFC only assign credit in the event of a prediction error or does one mechanism subsume another?

Reviewer #1 (Public Review):

As central molecular scaffolds, Cullin ring ubiquitin ligases proteins play critical roles in the post-translational modification of cellular proteins. Since cyclin D1 is a pivotal regulator to form the CDK4/6 complex during cell cycle progression, understanding if additional cullin-associated E3 ligases participate in the regulation of cyclin D1 protein stability is interesting. The current study used an NIH3T3 cells-based siRNA library to screen 156 cullin-associated ubiquitin ligases genes. The results indicated that cullins are required for cyclin D1 degradation, and cullin-induced cyclin D1 degradation is ubiquitin-dependent and is mediated by multiple E3 ligases (Keap1, DDB2, WSB2, and Rbx1 subunits). Overall, this is a well-designed experimental study and the quality of the data collection and analysis are high and rigorous. The manuscript is well written. The conclusion stated by the authors is supported by their data logically.

Reviewer #1 (Public Review):

This relatively small-scale cohort trial has demonstrated ideal efficacy and safety of combinatory immunotherapy, radiotherapy and chemotherapy. The study design is straightforward and the major findings are held back by solid clinical data. However, the correlation between the primary endpoint selection and long term benefit is lacking, and the current adverse events are not yet comprehensively exhibited.

Reviewer #1 (Public Review):

This manuscript provides a comprehensive investigation of the effects of the genetic ablation of three different transcription factors (Srf, Mrtfa, and Mrtfb) in the inner ear hair cells. Based on the published data, the authors hypothesized that these transcription factors may be involved in the regulation of the genes essential for building the actin-rich structures at the apex of hair cells, the mechanosensory stereocilia and their mechanical support - the cuticular plate. Indeed, the authors found that two of these transcription factors (Srf and Mrtfb) are essential for the proper formation and/or maintenance of these structures in the auditory hair cells. Surprisingly, Srf- and Mrtfb- deficient hair cells exhibited somewhat similar abnormalities in the stereocilia and in the cuticular plates even though these transcription factors have very different effects on the hair cell transcriptome. Another interesting finding of this study is that the hair cell abnormalities in Srf-deficient mice could be rescued by AAV-mediated delivery of Cnn2, one of the downstream targets of Srf. However, despite a rather comprehensive assessment of the novel mouse models, the authors do not have yet any experimentally testable mechanistic model of how exactly Srf and Mrtfb contribute to the formation of actin cytoskeleton in the hair cells. The lack of any specific working model linking Srf and/or Mrtfb with stereocilia formation decreases the potential impact of this study.

Major comments:

Figures 1 & 3: The conclusion on abnormalities in the actin meshwork of the cuticular plate was based largely on the comparison of the intensities of phalloidin staining in separate samples from different groups. In general, any comparison of the intensity of fluorescence between different samples is unreliable, no matter how carefully one could try matching sample preparation and imaging conditions. In this case, two other techniques would be more convincing: 1) quantification of the volume of the cuticular plates from fluorescent images; and 2) direct examination of the cuticular plates by transmission electron microscopy (TEM).

In fact, the manuscript provides no single TEM image of the F-actin abnormalities either in the cuticular plate or in the stereocilia, even though these abnormalities seem to be the major focus of the study. Overall, it is still unclear what exactly Srf or Mrtfb deficiencies do with F-actin in the hair cells.

Figures 2 & 4 represent another example of how deceiving could be a simple comparison of the intensity of fluorescence between the genotypes. It is not clear whether the reduced immunofluorescence of the investigated molecules (ESPN1, EPS8, GNAI3, or FSCN2) results from their mis-localization or represents a simple consequence of the fact that a thinner stereocilium would always have a smaller signal of the protein of interest, even though the ratio of this protein to the number of actin filaments remains unchanged. According to my examination of the representative images of these figures, loss of Srf produces mis-localization of the investigated proteins and irregular labeling in different stereocilia of the same bundle, while loss of Mrtfb does not. Obviously, a simple quantification of the intensity of fluorescence conceals these important differences.

Reviewer #1 (Public Review):

The work by Yijun Zhang and Zhimin He at al. analyzes the role of HDAC3 within DC subsets. Using an inducible ERT2-cre mouse model they observe the dependency of pDCs but not cDCs on HDAC3. The requirement of this histone modifier appears to be early during development around the CLP stage. Tamoxifen treated mice lack almost all pDCs besides lymphoid progenitors. Through bulk RNA seq experiment the authors identify multiple DC specific target gens within the remaining pDCs and further using Cut and Tag technology they validate some of the identified targets of HDAC3.<br /> Collectively the study is well executed and shows the requirement of HDAC3 on pDCs but not cDCs, in line with the recent findings of a lymphoid origin of pDC.

While the authors provide extensive data on the requirement of HDAC3 within progenitors, the high expression of HDAC3 in mature pDCs may underly a functional requirement. Have you tested INF production in CD11c cre pDCs? Are there transcriptional differences between pDCs from HDAC CD11c cre and WT mice?

A more detailed characterization of the progenitor compartment that is compromised following depletion would be important, as also suggested in the specific points.

Reviewer #1 (Public Review):

This is a very exciting manuscript from Meng Wang's lab on lysosomal proteomics. They used several different protein tags to identify the lysosomal proteome. The exciting findings include A) specific lysosomal proteins exist in a tissue-specific manner B) lipl-4 overexpression and daf-2 extend life span using different mechanisms C) identification of novel lysosomal proteins D) demonstration of the function of several lysosomal proteins in regulation lysosome abundance and function.

Joint Public Review:

Summary:

This concise review provides a clear and instructive picture of the state-of-the-art understanding of protein kinases' activity and sets of approaches and tools to analyse and regulate it.

Strengths:

Three major parts of the work include: methods to map allosteric communications, tools to control allostery, and allosteric regulation of protein kinases. The work provides an important and timely view of the current status of our understanding of the function of protein kinases and state-of-the-art methods to study its allosteric regulation and to develop allosteric approaches to control it.

Weaknesses:

The authors may wish to consider first discussing the allosteric regulation of kinases, which can be further considered from the perspective of computational approaches to map and experimental methods to control it.

Reviewer #1 (Public Review):

Summary: The goal of this project is to test the hypothesis that individual differences in experience with multiple languages relate to differences in brain structure, specifically in the transverse temporal gyrus. The approach used here is to focus specifically on the phonological inventories of these languages, looking at the overall size of the phonological inventory as well as the acoustic and articulatory diversity of the cumulative phonological inventory in people who speak one or more languages. The authors find that the thickness of the transverse temporal gyrus (either the primary TTG, in those with one TTG, or in the second TTG, in people with multiple gyri) was related to language experience, and that accounting for the phonological diversity of those languages improved the model fit. Taken together, the evidence suggests that learning more phonemes (which is more likely if one speaks more than one language) leads to experience-related plasticity in brain regions implicated in early auditory processing.

Strengths: This project is rigorous in its approach--not only using a large sample, but replicating the primary finding in a smaller, independent sample. Language diversity is difficult to quantify, and likely to be qualitatively and quantitatively distinct across different populations, and the authors use a custom measure of multilingualism (accounting for both number of languages as well as age of acquisition) and three measures of phonological diversity. The team has been careful in discussion of these findings, and while it is possible that pre-existing differences in brain structure could lead to an aptitude difference which could drive one to learn more than one language, the fine-grained relationships with phonological diversity seem less likely to emerge from aptitude rather than experience.

Weaknesses: It is a bit unclear how the measures of phonological diversity relate to one another--they are partially separable, but rest on the same underlying data (the phonemes in each language). It would be helpful for the reader to understand how these measures are distributed (perhaps in a new figure), and the degree to which they are correlated with one another. Further, as the authors acknowledge, it is always possible that an unseen factor instead drives these findings--if typological lexical distance measures are available, it would be helpful to enter these into the model to confirm that phonological factors are the specific driver of TTG differences and not language diversity in a more general sense. That said, the relationship between phonological diversity and TTG structure is intuitive.

One curious aspect of this paper relates to the much higher prevalence of split or duplicate TTG in the sample. The authors do a good job speculating on how features of the TASH package might lead to this, but it is unclear where the ground truth lies--some discussion of validation of TASH against a gold standard would be useful.

Reviewer #1 (Public Review):

The authors demonstrate that reactivation of mild vs strong aversive contextual associations produces dissociable effects on fos expression across a wide network of relevant brain regions. Mild, 2-shock memory recruits a 'small-world' network in which amygdalar regions are functionally connected to other regions that modulate their activity and behavioral output, whereas strong, 10-shock memory isolates amygdalar nuclei from the rest of the network. These different patterns of correlated neural activity correspond with functional/behavioral differences - the authors confirm that weak, 2-shock memory is more effectively extinguished and is susceptible to reconsolidation relative to strong, 10-shock memory.

One major drawback of the manuscript is the fact that the data were collected from male subjects only. One might expect similar behavioral outcomes from male and female rats receiving 2-shock and 10-shock training. However, increasing attention to sex as a biological variable has revealed an interesting truth, namely that males and females can engage distinct neural pathways to arrive at the same behavioral destination. It should not be taken for granted that retrieval of aversive contextual associations would reproduce the same networks in females, and, as such, the manuscript does not give a complete accounting of the phenomenon under study.

Reviewer #1 (Public Review):

Bolumar et al. isolated and characterized EV subpopulations, apoptotic bodies (AB), Microvesicles (MV), and Exosomes (EXO), from endometrial fluid through the female menstrual cycle. By performing DNA sequencing, they found the MVs contain more specific DNA sequences than other EVs, and specifically, more mtDNA were encapsulated in MVs. They also found a reduction of mtDNA content in the human endometrium at the receptive and post-receptive period that is associated with an increase in mitophagy activity in the cells, and a higher mtDNA content in the secreted MVs was found at the same time. Last, they demonstrated that the endometrial Ishikawa cell-derived EVs could be taken by the mouse embryos and resulted in altered embryo metabolism.

This is a very interesting study and is the first one demonstrating the direct transmission of maternal mtDNA to embryos through EVs.

Reviewer #1 (Public Review):

Summary:<br /> Previously, researchers targeting certain brain areas in mice have relied on manual reconstruction of 3D trajectories based on published atlases of 2D sections in standardized anatomical planes. Over a decade ago, Leica's AngleTwo software provided an early proprietary software interface to rodent atlases based on 2D graphics. However, the more recent advent of open-source 3D gaming engines and CAD software (here the authors used Unity) and the adoption of a common 3D atlas framework (the Common Coordinate Framework, or CCF, from the Allen Institute) by the neuroscience community have enabled more advanced targeting based on 3D anatomy, as primate researchers and human clinicians have done previously with MRI data using bespoke and commercial software solutions. The Neuropixels Trajectory Explorer (https://github.com/petersaj/neuropixels_trajectory_explorer, by Andy Peters) pioneered a software interface to the 3D mouse atlas for electrode insertions, and here Birman et al. have built on the aforementioned previous efforts to provide the most comprehensive trajectory planning software in mice to date, which they call Pinpoint. The most critical improvement lies in the ability to model the experimental rig and instruments in the same 3D environment as the atlas, since previously researchers needed to iteratively guess and check whether instruments physically fit with each other and the other constraints imposed by the rig. Other key features include coordinate transforms to map the CCF to more accurate in vivo anatomical data, as well as an API and hardware interface to commonly used micromanipulators.

Strengths:<br /> The feature set in Pinpoint makes it the best available software for planning instrument trajectories given geometrical constraints. Additionally, the documentation and open-source nature of the software should allow many extensions and improvements in the future, and as the authors note, it can also be used as a powerful teaching tool. Especially as researchers continue to push the boundaries of concurrent electrodes and optical fibers or other instruments within a single brain, this software will be of great use for neuroscience.

Weaknesses:<br /> Although Pinpoint enables instrument insertion planning with geometrical constraints for the first time and has many other novel features, it remains to be quantified how useful it is in terms of time/efficiency gains and accuracy of planned trajectories. For instance, although using a coordinate transform to MRI anatomical data is more accurate than the CCF alone in principle, users will need to verify how much this improved planning ability translates to time saved and/or improved trajectories as reconstructed from histology of dyed electrode tracks. The utility of the hardware interface for automating experiments versus the risk of damaging instruments with such an approach also remains to be quantified. Researchers using experimental subjects other than adult mice will have to wait for future integration of their atlases of choice, although the open-source nature of the project invites others to try adding this and other desired features themselves.

Reviewer #1 (Public Review):

Summary:<br /> Mice can learn to associate sensory cues (sound and light) with a reward or activation of dopamine neurons in the ventral tegmental area (VTA), and then anticipate the reward from the sensory cue only. Using this paradigm, Harada et al. showed that after learning, the cue is able to induce dopamine release in the projection targets of the VTA, namely the nucleus accumbens and lateral hypothalamus (LH). Within the LH, dopamine release from VTA neurons (either by presentation of the cue or direct optical stimulation of VTA neurons) activates orexin neurons, measured as an increase in intracellular calcium levels.

Strengths:<br /> This study utilized genetically encoded optical tools to selectively stimulate dopamine neurons and to monitor dopamine release in target brain areas and the calcium response of orexin neurons. This allowed a direct assessment of the relationship between the behavioral response of the animals, the release of a key neurotransmitter in select brain areas, and its effect on target cells, with a precision previously not possible. The results shed light on the mechanism underlying reward-related learning and expectation.

Weaknesses:<br /> • The Ca increase in orexin neurons in response to optical stimulation of VTA DA neurons is convincing. However, there is an accumulated body of literature indicating that dopamine inhibits orexin neurons through D2 receptors, particularly at high concentrations both directly and indirectly (PMID 15634779, 16611835, 26036709, 30462527; but note that synaptic effects at low conc are excitatory - PMID 30462527, 26036709). There should be a clear acknowledgment of these previous studies and a discussion directly addressing the discrepancy. Furthermore, there are in-vivo studies that investigated the role of dopamine in the LH involving orexin neurons in different behavioral contexts (e.g. PMID 24236888). The statement found in the introduction "whether and how dopamine release modulates orexin neuronal activity has not been investigated vigorously" (3rd para of Introduction) is an understatement of these previous reports.

• Along these lines, previous reports of concentration-dependent bidirectional dopaminergic modulation of orexin neurons suggest that high and low levels of DA would affect orexin neurons differently. Is there any way to estimate the local concentration of DA released by the laser stimulation protocol used in this study? Could there be a dose dependency in the intensity of laser stimulation and orexin neuron response?

• The transient dip in DA signal during omission sessions in Fig2C (approx 1% decrease from baseline) is similar in amplitude compared to the decrease seen in non-laser trails shown in Fig 1C right panel (although the time course of the latter is unknown as the data is truncated). The authors should clarify whether those dips are a direct effect of the cue itself or indeed reward prediction error.

• There seem to be orexin-negative-GCaMP6 positive cells (Fig. 4B), suggesting that not all cells were phenotypically orexin+ at the time of imaging. The proportion of GCaMP6 cells that were ORX+ or negative and whether they responded differently to the stimuli should be indicated.

• Laser stimulation of DA neurons at the level of cell bodies (in VTA) induces an increase in DA release within the LH (Fig. 3C, D), however, there is no corresponding Ca signal in orexin neurons (Fig.4C). In contrast, stimulating DA terminals within the LH induces a robust, long-lasting Ca signal (> 30s) in orexin neurons (Fig. 5). The initial peak is blocked by raclopride but the majority of Ca signal is insensitive to DA antagonists (please add a positive control or cite references indicating that the dose of antagonists used was sufficient; also the timing of antagonist administration should be indicated). Taken together, these results seem to suggest that DA does not directly increase Ca signal in orexin neurons. What could be mediating the remaining component?

• Similarly, there is an elevation of Ca signal in orexin neurons that remains significantly higher after the cue/laser stimulation (Fig. 4F). It appears that it is this sustained component that is missing in omission trials. This can be analyzed further.

• Mice of both sexes were used in this study; it would be interesting to know whether sex differences were observed or not.

Reviewer #1 (Public Review):

Summary:<br /> Willems and colleagues test whether unexpected shock omissions are associated with reward-related prediction errors by using an axiomatic approach to investigate brain activation in response to unexpected shock omission. Using an elegant design that parametrically varies shock expectancy through verbal instructions, they see a variety of responses in reward-related networks, only some of which adhere to the axioms necessary for prediction error. In addition, there were associations between omission-related responses and subjective relief. They also use machine learning to predict relief-related pleasantness, and find that none of the a priori "reward" regions were predictive of relief, which is an interesting finding that can be validated and pursued in future work.

Strengths:<br /> The authors pre-registered their approach and the analyses are sound. In particular, the axiomatic approach tests whether a given region can truly be called a reward prediction error. Although several a priori regions of interest satisfied a subset of axioms, no ROI satisfied all three axioms, and the authors were candid about this. A second strength was their use of machine learning to identify a relief-related classifier. Interestingly, none of the ROIs that have been traditionally implicated in reward prediction error reliably predicted relief, which opens important questions for future research.

Weaknesses:<br /> To ensure that the number of omissions is similar across conditions, the task employs inaccurate verbal instructions; i.e. 25% of shocks are omitted, regardless of whether subjects are told that the probability is 100%, 75%, 50%, 25%, or 0%. Given previous findings on interactions between verbal instruction and experiential learning (Doll et al., 2009; Li et al., 2011; Atlas et al., 2016), it seems problematic a) to treat the instructions as veridical and b) average responses over time. Based on this prior work, it seems reasonable to assume that participants would learn to downweight the instructions over time through learning (particularly in the 100% and 0% cases); this would be the purpose of prediction errors as a teaching signal. The authors do recognize this and perform a subset analysis in the 21 participants who showed parametric increases in anticipatory SCR as a function of instructed shock probability, which strengthened findings in the VTA/SN; however given that one-third of participants (n=10) did not show parametric SCR in response to instructions, it seems like some learning did occur. As prediction error is so important to such learning, a weakness of the paper is that conclusions about prediction error might differ if dynamic learning were taken into account. Lastly, I think that findings in threat-sensitive regions such as the anterior insula and amygdala may not be adequately captured in the title or abstract which strictly refers to the "human reward system"; more nuance would also be warranted.

Reviewer #1 (Public Review):

Strengths:<br /> The authors introduced a new adapted paradigm from continuous flash suppression (CFS). The new CFS tracking paradigm (tCFS) allowed them to measure suppression depth in addition to breakthrough thresholds. This innovative approach provides a more comprehensive understanding of the mechanisms underlying continuous flash suppression. The observed uniform suppression depth across target types (e.g., faces and gratings) is novel and has new implications for how the visual system works. The experimental manipulation of the target contrast change rate, as well as the modeling, provided strong support for an early interocular suppression mechanism. The authors argue that the breakthrough threshold alone is not sufficient to infer about unconscious processing.

Weaknesses:<br /> A major finding in the current study is the null effect of the image categories on the suppression depth measured in the tCFS paradigm, from which the authors infer an early interocular mechanism underlying CFS suppression. This is not strictly logical as an inference based on the null effect. The authors may consider statistical evaluation of the null results, such as equivalence tests or Bayesian estimation.

More importantly, since limited types of image categories have been tested, there may be some exceptional cases. According to "Twofold advantages of face processing with or without visual awareness" by Zhou et al. (2021), pareidolia faces (face-like non-face objects) are likely to be an exceptional case. They measured bidirectional binocular rivalry in a blocked design, similar to the discrete condition used in the current study. They reported that the face-like non-face object could enter visual awareness in a similar fashion to genuine faces but remain in awareness in a similar fashion to common non-face objects. We could infer from their results that: when compared to genuine faces, the pareidolia faces would have a similar breakthrough threshold but a higher suppression threshold; when compared to common objects, the pareidolia faces would have a similar suppression threshold but a low breakthrough threshold. In this case, the difference between these two thresholds for pareidolia faces would be larger than either for genuine faces or common objects. Thus, it would be important for the authors to discuss the boundary between the findings and the inferences.

Reviewer #1 (Public Review):

This paper studies how amacrine cells influence retinal output signals. The approach taken is unusually direct. First, the amacrine light response is characterized. Second, the properties of signaling between the amacrine cell and ganglion cells is characterized by injecting current into the amacrine cell while measuring ganglion cell spiking. Third, the ganglion cell light response is analyzed in terms of components produced by signaling pathways that go through the amacrine cell and those that do not. Interpretation of the results relies on several important and largely untested assumptions. If some of the concerns that this dependence produces can be reduced the paper would be substantially stronger.

Linear vs. nonlinear and direct vs. indirect<br /> Influences of an amacrine cell on the ganglion cell response are separated into direct effects - in which the amacrine cell directly produces a component of the ganglion cell response - and indirect effects - in which the amacrine cell modulates component(s) of the ganglion cell response (e.g. lines 97-99). In various places direct and indirect are equated with linear and nonlinear. Importantly, this assumption forms the basis of the analysis in the paper. It is not clear why a direct pathway through the amacrine cell should be linear. For example, it seems entirely possible that nonlinear models would capture the amacrine cell light response better than linear models. Similarly, nonlinear models may better capture the transmission of signals from amacrine cells to ganglion cells. Clarity on this issue is essential to interpret the results in the paper. One example of this issue comes up in the sentence on line 233. The definition of modulation is precise but only in the context of the above assumptions.

Components of oSTA<br /> The set of pre-spike stimuli that are orthogonal to the "direct" STA is used to characterize the "indirect" pathways conveying signals to a ganglion cell. For the reasons noted above, it is not clear that this is accurate. In addition, the text describes the PCs of this orthogonal stimulus ensemble as features. This is introduced in the paragraph starting on line 177, and this paragraph has the disclaimer that these features do not correspond to neural pathways. That important caveat to interpretation could be reiterated in the following text - particularly in discussing the different forms of modulation.

Related to this point, the analysis of Figures 3 and 4 relies on the PCs of this orthogonal stimulus ensemble. Since the PCs themselves do not map onto pathways or mechanisms, it is not clear how to interpret some of the results. For example, when you see a polarity shift along one of the PCs, what happens along others (for example, could they also be shifting polarity such that the net effect is a change in kinetics but not a change in polarity)? This also comes up in the paragraph on line 236, as it is not clear how the separation works given the way the components used as the basis of the separation are defined.

Some of these issues are clarified in Figure 4D, and perhaps it would help to start with that description. I think this section would be much clearer if two types of modulation were noted and then it was laid out how that conclusion was reached.

Reviewer #1 (Public Review):

In this systematic and elegant structure-function analysis study, the authors delve into the intricate involvement of syntaxin 1 in various pivotal stages of synaptic vesicle priming and fusion. The authors use an original and fruitful approach based on the side-by-side comparison of the specific contributions of the two isoforms syntaxin 1 and syntaxin 2, and their respective SNARE domains, in priming, spontaneous, and Ca2+-dependent glutamate release. The experimental approach, mastered by the authors, offers an ideal means of unraveling the molecular roles played by syntaxins. Although it is not easy to come up with a model explaining all the observed phenotypes, the authors carefully restrict their conclusions to the role of the C-terminal half of the syntaxin1 C-terminal SNARE domain in the maintenance of the RRP and the clamping of neurotransmitter release. The study is carefully carried out, the conclusions are supported by high-quality data, and the manuscript is clearly written. In addition, the study clearly sets new questions that open new paths for future experimental work.

Reviewer #1 (Public Review):

Summary:<br /> In this paper, the effects of two sensory stimuli (visual and somatosensory) on fMRI responsiveness during absence seizures were investigated in GEARS rats with concurrent EEG recordings. SPM analysis of fMRI showed a significant reduction in whole-brain responsiveness during the ictal period compared to the interictal period under both stimuli, and this phenomenon was replicated in a structurally constrained whole-brain computational model of rat brains.

The conclusion of this paper is that whole-brain responsiveness to both sensory stimuli is inhibited and spatially impeded during seizures.

I also suggest the manuscript should be written in a way that is more accessible to readers who are less familiar with animal experiments. In addition, the implementation and interpretation of brain simulations need to be more careful and clear.

Strengths:<br /> 1. ZTE imaging sequence was selected over traditional EPI sequence as the optimal way to perform fMRI experiments during absence seizures.

2. A detailed classification of stimulation periods is achieved based on the relative position in time of the stimulation period with respect to the brain state.

3. A whole-brain model embedded with a realistic rat connectome is simulated on the TVB platform to replicate fMRI observations.

Weaknesses:<br /> 1. The analysis in this paper does not directly answer the scientific question posed by the authors, which is to explore the mechanisms of the reduced brain responsiveness to external stimuli during absence seizures (in terms of altered information processing), but merely characterizes the spatial involvement of such reduced responsiveness. The same holds for the use of mean-field modeling, which merely reproduces experimental results without explaining them mechanistically as what the authors have claimed at the head of the paper.

2. The implementations of brain simulations need to be more specific.

Contribution:<br /> The contribution of this paper is performing fMRI experiments under a rare condition that could provide fresh knowledge in the imaging field regarding the brain's responsiveness to environmental stimuli during absence seizures.

Reviewer #1 (Public Review):

Summary:<br /> Very systematic generation of phosphosite-specific antisera to monitor FFA2 phosphorylation in native cells and tissues. Provides evidence that FFA2 phosphorylation is tissue-specific.

Strengths:<br /> Technical tour de force, rigorous experimental approaches taking advantage of wt and DREADD versions of FFA2 to make sure that ligand-and receptor-dependent phosphorylations are indeed specific to FFA2.

Weaknesses:<br /> In this reviewer's opinion, the only shortcoming is that the implications of tissue-selective phosphorylation barcoding remain unexplored. However, I understand that tool development is required before tools are used to provide insight into the functional outcomes of receptor regulation by phosphorylation. The study is a technical tour de force to generate highly valuable tools. I have no major criticisms but suggest adding an additional aspect to the discussion as specified below.

Arrestins are highly flexible and dynamic phosphate sensors. If two arrestins have to recognize 800 different phosphorylated GPCRs, is it possible that any barcode serves the same purpose: arrestin recognition followed by signal arrest and internalization? Because phosphorylation barcoding is linked to G protein-independent signaling, which is claimed by some but is experimentally unsupported, and because arrestins don't transduce receptor signals on their own (they only scaffold signaling components and shuttle receptors within cellular compartments), I would also include this option in the discussion, i.e. that the different barcodes are a way nature may have chosen to regulate the location of 800 GPCRs by only 2 arrestins.

Reviewer #1 (Public Review):

Summary:

A description of a modern protocol for cervical screening that likely could be used in any country of the world, based on self-sampling, extended HPV genotyping and AI-assisted visual inspection - which is probably the best available combination today.

Strengths:

Modern, optimised protocol, designed for global use. Innovative.

Weaknesses:

The protocol is not clear. I could not even find how many women were going to be enrolled, the timelines of the study, the statistical methods ("comparing" is not statistics) or the power calculations.

Tables 2 and 3 are too schematic - surely the authors must have an approximate idea of what the actual numbers are behind the green, red and yellow colors.

Figure 1 comparing screening and vaccination is somewhat misleading. They screen 20 birth cohorts but vaccinate only 5 birth cohorts. Furthermore, the theoretical gains of screening has not really been attained in any country in practice. Modelling can be a difficult task and the commentary does not provide any detail on how to evaluate what was done. It just seems unnecessary to attack vaccination as a motivation on why screening needs to be modernised.

Reviewer #1 (Public Review):

Summary:<br /> In this manuscript the authors use ATAC-seq to find regions of the genome of rat embryonic striatal neurons in culture that show changes in regulatory element accessibility following stimulation by KCl-mediated membrane depolarization. The authors compare 1hr and 4hr transcriptomes to see both rapid and late response genes. When they look at ATAC-seq data they see no changes in accessibility at 1hr but strong changes at 4hr. The differentially accessible sites were enriched for the AP-1 site, suggesting regulation by Fos-Jun family members, and consistent with the requirement for IEG expression, anisomycin blocked the increase in accessibility. To test the functional importance of this regulation the authors focus on a putative enhancer 45kb upstream of the activity-induced gene encoding the neuromodulator dynorphin (Pdyn). To test the function of this region, the authors recruited CRISPRi to the site, which blocked KCL-dependent Pdyn induction, or CRISPRa, which selectively increased Pdyn expression in the absence of KCl. Finally the authors reanalyze other human and rat datasets to show cell-type specific function of this enhancer correlated to Pdyn expression.

The idea that stimuli that induce expression of Fos in neurons can change accessibility of regulatory elements bound from Fos has been shown before, but almost all the data are from hippocampal neurons so it is nice to see the different cell type used here. The most interesting part of the study is the identification of the Pdyn enhancer because of the importance of this gene product in the function of striatal neurons. Overall the conclusions appear to be well supported by the data.

Joint Public Review:

In this study the authors confirm that one of the genes classified as essential in a Tn-mutagenesis study in A. baumannii is in fact an essential gene. It is also present in other closely related Gram negative bacteria and the authors designated it Aeg1.

The strength of the work is that it discovered that the depletion of Aeg1 leads to cell filamentation and that the requirement for Aeg1 can be suppressed by activation mutations in various cell division genes. These results suggest that Aeg1 plays an important role in cell division.

The weakness of the work is that it lacks convincing evidence to define Aeg1 place or role in the divisome assembly pathway. It is unclear what proteins are at the division site when Aeg1 is depleted and what proteins are required for Aeg1 to localize to the division site.

Reviewer #1 (Public Review):

In this manuscript the authors performed experiments and simulations which showed that substrate evaporation is the main driver of early construction in termites. Additionally, these experiments and simulations were designed taking into account several different works, so that the current results shine a light on how substrate evaporation is a sufficient descriptor of most of the results seen previously.

Through simulations and ingenious experiments the authors have shown how curvature is extremely correlated with evaporation, and therefore, how results coming from these 2 environmental factors can be explained through evaporation alone. The authors have continued to use their expertise of numerical simulations and a previously developed model for termite construction, to highlight and verify their findings. On my first pass of the manuscript I felt the authors were missing an experiment: an array of humidity probes to measure evaporation in the three spatial dimensions and over time. Technologically such an experiment is not out of reach, but the author's alternative (a substrate made with a saline solution and later measuring the salt deposits on the surface) was a very ingenious low tech solution to the problem.

The authors agree that future experiments should tackle finely controlled humidity levels and curvature in order to have a more quantitative measure termite behaviour, but the work done so far is more than sufficient to justify their current claims.

The results presented here are so far the best attempt on characterizing multiple cues that induce termite construction activity, and that possibly unifies the different hypothesis presented in the last 8 years into a single factor. More importantly, even if these results come from different species of termites than some of the previous works, they are relatable and seem to be mostly consistent, improving the strength of the author's claims.

Joint Public Review:

This concise review provides a clear and instructive picture of the state-of-the-art understanding of protein kinases' activity and sets of approaches and tools to analyse and regulate it.

Three major parts of the work include: methods to map allosteric communications, tools to control allostery, and allosteric regulation of protein kinases. The work provides an important and timely view of the current status of our understanding of the function of protein kinases and state-of-the-art methods to study its allosteric regulation and to develop allosteric approaches to control it.

Reviewer #1 (Public Review):

This work describes a structural analysis of the tripartite HipBST toxin-antitoxin (TA) system, which is related to the canonical two-component HipBA system composed of the HipA serine-threonine kinase toxin and the HipB antitoxin. The crystal structure of the kinase-inactive HipBST complex of the Enteropathogenic E. coli O127:H6 was solved and revealed that HipBST forms a hetero-hexameric complex composed of a dimer of HipBST heterotrimers that interact via the HipB subunit. The HipS antitoxin shows a structural resemblance to HipA N-terminal region and the HipT toxin represents to the core kinase domain of HipA, indicating that in HipBST the hipA toxin gene was likely split in two genes, namely hipS and hipT.<br /> -The structure also reveals a conserved and essential Trp residue within the HipS antitoxin, which likely prevents the conserved "Gly-rich loop" of HipT from adopting an inward conformation needed for ATP binding. This work also shows that the regulating Gly-rich loop of the HipT toxin contains conserved phosphoserine residues essential for HipT toxicity that are key players within the HipT active site interacting network and which likely control antitoxin binding and/or activity.

Strengths:

The manuscript is well written and the experimental work well executed. It shows that major features of the classical two-component HipAB TA system have somehow been rerouted in the case of the tripartite HipBST. This includes the N-terminal domain of the HipA toxin, which now functions as bona fide antitoxin, and the partly relegated HipB antitoxin, which could only function as a transcription regulator. In addition, this work shows a new mode of inhibition of a kinase toxin and highlights the impact of the phosphorylation state of key toxin residues in controlling the activity of the antitoxin.

Weaknesses:

The authors have convincingly addressed the previously raised weaknesses in their revised version of the manuscript.

Reviewer #1 (Public Review):

The authors develop reporter constructs in E. coli where gene expression, presumably translation, is repressed by MSI-1. This is a potentially useful tool for synthetic biologists, with the advantage over transcriptional regulation that one gene in an operon could be targeted. That being said, an important caveat of translational regulation that is not addressed in the manuscript is the potential for downstream effects on RNA stability and/or transcription termination. The authors' MSI-1-regulated reporter constructs could also be useful for mechanistic studies of MSI-1.

The author's initial construct design led to only weak regulation by MSI-1, presumably because the MSI-1 binding sites were not suitably positioned to repress translation initiation. A more rationally designed construct led to considerably greater repression. One weakness of the paper is that the authors did not use their redesigned construct that is more strongly repressed to demonstrate allosteric regulation by oleic acid using a comparable assay (e.g., flow cytometry) to that used in other experiments. The potential for allosteric regulation is a major strength of the MSI-1 system, so this is a significant gap. Similarly, the authors use the weakly regulated constructs to assess the effect of MSI-1 binding site mutations and for their mathematical modeling; these experiments would be better suited to the more strongly regulated construct.

Reviewer #1 (Public Review):

Muscle models are important tools in the fields of biomechanics and physiology. Muscle models serve a wide variety of functions, including validating existing theories, testing new hypotheses, and predicting forces produced by humans and animals in health and disease. This paper attempts to provide an alternative to Hill-type muscle models that includes contributions of titin to force enhancement over multiple time scales. Due to the significant limitations of Hill-type models, alternative models are needed and therefore the work is important and timely.

The effort to include a role for titin in muscle models is a major strength of the methods and results. The results clearly demonstrate the weaknesses of Hill models and the advantages of incorporating titin into theoretical treatments of muscle mechanics. Another strength is to address muscle mechanics over a large range of time scales. Weaknesses include the decision to use a MTU model to simulate experiments from single muscle fibers, and failure to systematically address the limitations of the model, including equations for activation dynamics with no length dependence. It would also be useful for readers if the authors provided a discussion of the types of data that can be simulated using the model, along with potential pitfalls and how to determine model parameters.

The authors succeed in demonstrating the need to incorporate titin in muscle models. However, it remains unclear whether it will be practical for others to use this particular model for different types of data. Several ad hoc modifications were described in the paper, and the degree to which the model requires parameter optimization for different muscles, preparations and experiment types is also unclear.

Reviewer #1 (Public Review):

Aiming at the problem that Staphylococcus aureus can cause apoptosis of macrophages, the author found and verified that drug (R)-DI-87 can inhibit mammalian deoxycytidine kinase (dCK), weaken the killing effect of staphylococcus aureus on macrophages, and reduce the apoptosis of macrophages. And increase the infiltration of macrophages to the abscess, thus weakening the damage of Staphylococcus aureus to the host. This work provides new insights and ideas for understanding the effects of Staphylococcus aureus infection on host immunity and discovering corresponding therapeutic interventions.

The logic of the study is commendable, and the design is reasonable.

Some data related to the conclusion of the paper need to be supplemented, and some experimental details need to be described.

Reviewer #1 (Public Review):

Despite numerous studies on quinidine therapies for epilepsies associated with GOF mutant variants of Slack, there is no consensus on its utility due to contradictory results. In this study Yuan et al. investigated the role of different sodium selective ion channels on the sensitization of Slack to quinidine block. The study employed electrophysiological approaches, FRET studies, genetically modified proteins and biochemistry to demonstrate that Nav1.6 N- and C-tail interacts with Slack's C-terminus and significantly increases Slack sensitivity to quinidine blockade in vitro and in vivo. This finding inspired the authors to investigate whether they could rescue Slack GOF mutant variants by simply disrupting the interaction between Slack and Nav1.6. They find that the isolated C-terminus of Slack can reduce the current amplitude of Slack GOF mutant variants co-expressed with Nav1.6 in HEK cells and prevent Slack induced seizures in mouse models of epilepsy. This study adds to the growing list of channels that are modulated by protein-protein interactions, and is of great value for future therapeutic strategies.

Reviewer #1 (Public Review):

Summary:<br /> In this work the authors provide evidence that impairment of cell envelope protein homeostasis through blocking the machinery for disulfide bond formation restores the efficacy of antibiotics including beta-lactam drugs and colistin against AMR in Gram-negative bacteria.

Strengths:

The authors employ a thorough approach to showcase the restoration of antibiotic sensitivity through inhibition of the DSB machinery, including the evaluation of various antibiotics on both normal and Dsb-deficient pathogenic bacteria (i.e. Pseudomonas and Stenotrophomonas). The authors corroborate these findings by employing Dsb inhibitors in addition to delta dsbA strains. The methodology is appropriate and includes measuring MICs as well as validating their observations in vivo using the Galleria model.

Weaknesses:

The study would benefit from presenting raw data in some cases, such as MIC values and SDS-PAGE gels, by clarifying the number of independent experiments used, as well as further clarification on statistical significance for some of the data.

Reviewer #1 (Public Review):

Nitrogen metabolism is of fundamental importance to biology. However, the metabolism and biochemistry of guanidine and guanidine containing compounds, including arginine and homoarginine, have been understudied over the last few decades. Very few guanidine forming enzymes have been identified. Funck et al define a new type of guanidine forming enzyme. It was previously known that 2-oxogluturate oxygenase catalysis in bacteria can produce guanidine via oxidation of arginine. Interestingly, the same enzyme that produces guanidine from arginine also oxidises 2-oxogluturate to give the plant signalling molecule ethylene. Funck et al show that a mechanistically related oxygenase enzyme from plants can also produce guanidine, but instead of using arginine as a substrate, it uses homoarginine. The work will stimulate interest in the cellular roles of homoarginine, a metabolite present in plants and other organisms including humans and, more generally, in the biochemistry and metabolism of guanidines.

1. Significance<br /> Studies on the metabolism and biochemistry of the small nitrogen rich molecule guanidine and related compounds including arginine have been largely ignored over the last few decades. Very few guanidine forming enzymes have been identified. Funck et al define a new guanidine forming enzyme that works by oxidation of homoarginine, a metabolite present in organisms ranging from plants to humans. The new enzyme requires oxygen and 2-oxogluturate as cosubstrates and is related, but distinct from a known enzyme that oxidises arginine to produce guanidine, but which can also oxidise 2-oxogluturate to produce the plant signalling molecule ethylene.

Overall, I thought this was an exceptionally well written and interesting manuscript. Although a 2-oxogluturate dependent guanidine forming enzyme is known (EFE), the discovery that a related enzyme oxidises homoarginine is really interesting, especially given the presence of homoarginine in plant seeds. There is more work to be done in terms of functional assignment, but this can be the subject of future studies. I also fully endorse the authors' view that guanidine and related compounds have been massively understudied in recent times. I would like to see the possibility that the new enzyme makes ethylene explored. Congratulations to the authors on a very nice study.

Reviewer #1 (Public Review):

Summary:<br /> Cincotta et al set out to investigate the presence of glucocorticoid receptors in the male and female embryonic germline. They further investigate the impact of tissue-specific genetically induced receptor absence and/or systemic receptor activation on fertility and RNA regulation. They are motivated by several lines of research that report inter and transgenerational effects of stress and or glucocorticoid receptor activation and suggest that their findings provide an explanatory mechanism to mechanistically back parental stress hormone exposure-induced phenotypes in the offspring.

Strengths:<br /> - A chronological immunofluorescent assessment of GR in fetal and early life oocyte and sperm development.<br /> - RNA seq data that reveal novel cell type specific isoforms validated by q-RT PCR E15.5 in the oocyte.<br /> - 2 alternative approaches to knock out GR to study transcriptional outcomes. Oocytes: systemic GR KO (E17.5) with low input 3-tag seq and germline-specific GR KO (E15.5) on fetal oocyte expression via 10X single cell seq and 3-cap sequencing on sorted KO versus WT oocytes - both indicating little impact on polyadenylated RNAs<br /> - 2 alternative approaches to assess the effect of GR activation in vivo (systemic) and ex vivo (ovary culture): here the RNA seq did show again some changes in germ cells and many in the soma.<br /> - They exclude oocyte-specific GR signaling inhibition via beta isoforms.<br /> - Perinatal male germline shows differential splicing regulation in response to systemic Dex administration, results were backed up with q-PCR analysis of splicing factors.

Weaknesses:<br /> - The presence of a protein cannot be entirely excluded based on IF data (staining of spermatids is referred to but not shown).<br /> - The authors do not consider post-transcriptional level a) modifications also trigged by GR activation b) non-coding RNAs (not assessed by seq).<br /> - Sequencing techniques used are not total RNA but either are focused on all polyA transcripts (10x) or only assess the 3' prime end and hence are not ideal to study splicing, The number of replicates in the low input seq is very low and hence this might be underpowered. Since Dex treatment showed some (modest) changes in oocyte RNA - effects of GR depletion might only become apparent upon Dex treatment as an interaction.<br /> - Effects in oocytes following systemic Dex might be indirect due to GR activation in the soma.<br /> - Even though ex vivo culture of ovaries shows GR translocation to the nucleus it is not sure whether the in vivo systemic administration does the same.

The conclusion that fetal oocytes are "intrinsically buffered to GR signalling" is very strong, given that "only" poly A sequencing and few replicates of 3-prime sequencing have been analyzed and information is lacking on whether GR is activated in germ cells in the systemically dex-injected animals.

This work is a good reference point for researchers interested in glucocorticoid hormone signaling fertility and RNA splicing. It might spark further studies on germline-specific GR functions and the impact of GR activation on alternative splicing.

While the study provides a characterization of GR and some aspects of GR perturbation, and the negative findings in this study do help to rule out a range of specific roles of GR in the germline, there is still a range of other potential unexplored options. The introduction of the study eludes to implications for intergenerational effects via epigenetic modifications in the germline, however, it does not mention that the indirect effects of reproductive tissue GR signaling on the germline have indeed already been described in the context of intergenerational effects of stress. Also, the study does not assess epigenetic modifications.

The conclusion that the persistence of a phenotype for up to three generations suggests that stress can induce lasting epigenetic changes in the germline is misleading. For the reader who is unfamiliar with the field, it is important to define much more precisely what is referred to as "a phenotype". Furthermore, this statement evokes the impression that the very same epigenetic changes in the germline have been observed across multiple generations.

The evidence of the presence of GR in the germline is also somewhat limited - since other studies using sequencing have detected GR in the mature oocyte and sperm.

The discussion ends again on the implications of sex-specific differences of GR signaling in the context of stress-induced epigenetic inheritance. It states that the observed differences might relate to the fact that there is more evidence for paternal lineage findings, without considering that maternal lineage studies in epigenetic inheritance are generally less prevalent due to some practical factors - such as more laborious study design making use of cross-fostering or embryo transfer. Since the authors comment on RNA-mediated inheritance it seems inevitable to again consider indirect effects.

Reviewer #1 (Public Review):

This is a well-designed study that explores the BEF relationships in fragmented landscapes. Although there are massive studies on BEF relationships, most of them were conducted at local scales, few considered the impacts of landscape variables. This study used a large dataset to specifically address this question and found that habitat loss weakened the BEF relationships. Overall, this manuscript is clearly written and has important implications for BEF studies as well as for ecosystem restoration.

My only concern is that the authors should clearly define habitat loss and fragmentation. Habitat loss and fragmentation are often associated, but they are different terms. The authors consider habitat loss a component of habitat fragmentation, which is not reasonable. Please see my specific comments below.

Joint Public Review:

This work by Liu CSC et al. is an extension of the author's previous work on the role of Piezo1 mechano-sensor in human T cell activation. In this study, the authors address whether Piezo1 plays a role in T-cell chemotactic migration.

The authors used CD4+ T cells or Jurkat T cells to test the effects of siRNA-mediated depletion of Piezo1 on chemotactic migration. They establish that Piezo1 is implicated in chemotactic migration, although the effects of depletion are relatively moderate.

They show that Piezo1 is redistributed to the leading edge of T-cells.

They identify that relocation of Piezo1 to the leading edge follows an increase in membrane tension.

In Piezo-1 depleted cells, they observe a moderate reduction of LFA-1 polarity. With the use of specific inhibitors, they propose Piezo1 activation to be downstream of focal adhesion formation and upstream of calpain-mediated LFA-1, integrin alpha L beta 2, or CD11a/CD18 recruitment at the leading edge.

Strengths:<br /> Together with their 2018 paper, this study presents Pieszo1 as a regulator of T-cell activation, implicating it as a player in the coordination of the chemotactic immune response.

Weaknesses:<br /> Most of the effects observed are relatively modest. The authors did not challenge the cells with various physico-mechanical conditions to see when Piezo-1 might become really important. For instance, there are no experiments that expose T cells to varying counter-acting forces to see how piezo1 might affect migration.

Technical weaknesses:<br /> The authors state that "these high tension edges are usually further emphasized at later time points", but after ten minutes the median tension and tension (Figure 2C and Supplementary Figure 2C respectively) reduce down to the pretreatment time point. It would be clearer if the author stated within which timeframe the tension edges are "further emphasised".

Figures 3 and 4 - The author states the number of cells quantified from the images, but it is not clear whether the data is actually from 3 biological replicates.

Some of the data has no representative images or videos included. there is no video in the supplementary for Figures 1 A and B. There are no representative images of transwell migration assay in Figures 1 D and E.

Reviewer #1 (Public Review):

In 'Systems analysis of miR-199a/b-5p and multiple miR-199a/b-5p targets during chondrogenesis', Patel et al. present a variety of analyses using different methodologies to investigate the importance of two miRNAs in regulating gene expression in a cellular model of cartilage development. They first re-analysed existing data to identify these miRNAs as one of the most dynamic across a chondrogenesis development time course. Next, they manipulated the expression of these miRNAs and showed that this affected the expression of various marker genes as expected. An RNA-seq experiment on these manipulations identified putative mRNA targets of the miRNAs which were also supported by bioinformatics predictions. These top hits were validated experimentally and, finally, a kinetic model was developed to demonstrate the relationship between the miRNAs and mRNAs studied throughout the paper.

I am convinced that the novel relationships reported here between miR-199a/b-5p and target genes FZD6, ITGA3, and CAV1 are likely to be genuine. It is important for researchers working on this system and related diseases to know all the miRNA/mRNA relationships but, as the authors have already published work studying the most dynamic miRNA (miR-140-5p) in this biological system I was not convinced that this study of the second miRNA in their list provided a conceptual advance on their previous work.

I was also concerned with the lack of reporting of details of the manipulation experiments. The authors state that they have over-expressed miR-199a-5p (Figure 2A) and knocked down miR-199b-5p (Figure 2B) but they should have reported their proof that these experiments had worked as predicted, e.g. showing the qRT-PCR change in miRNA expression. Similarly, I was concerned that one miRNA was over-expressed while the other was knocked down - why did the authors not attempt to manipulate both miRNAs in both directions? Were they unable to achieve a significant change in miRNA expression or did these experiments not confirm the results reported in the manuscript?

I had a number of issues with the way in which some of the data was presented. Table 1 only reported whether a specific pathway was significant or not for a given differential expression analysis but this concealed the extent of this enrichment or the level of statistical significance reported. Could it be redrawn to more similarly match the format of Figure 3A? The various shades of grey in Figure 2 and Figure 4 made it impossible to discriminate between treatments and therefore identify whether these data supported the conclusions made in the text. It also appeared that the same results were reported in Figure 3B and 3C and, indeed, Figure 3B was not referred to in the main text. Perhaps this figure could be made more concise by removing one of these two sets of panels.

Overall, while I think that this is an interesting and valuable paper, I think its findings are relatively limited to those interested in the role of miRNAs in this specific biomedical context.

Reviewer #1 (Public Review):

Summary:

In this work, Frank, Bergamasco, Mlodzianoski et al study two microcephaly-associated patient variants in TRABID to identify and characterize a previously unrecognized role of this deubiquitylation enzyme during neurodevelopment. The authors generate TRABID p.R438W and p.A451V knock in mice, which exhibit smaller neuronal and glial cell densities as well as motor deficits, phenotypes that are consistent with the congenital defects observed in the patients. Through in vitro and cellular immunoprecipitation assays, the authors demonstrate that the p.R438W variant impairs the K29- and K63-chain cleavage activity of TRABID, while the p.A451V variant reduces binding to the STRIPAK complex, a previously identified TRABID interactor with established functions in cytoskeletal organization and neural development. Ubiquitylation assays performed in HEK293T cells further reveal that the hypomorphic patient variants are deficient in deubiquitylating APC, a previously identified substrate of TRABID that has been shown to control the neuronal cortical cytoskeleton during neurite outgrowth. Ex vivo experiments provide evidence that axonal APC trafficking and neurite outgrowth is disturbed in differentiating neural progenitors isolated from mouse embryos carrying Trabid patient alleles. From these experiments the authors propose a model in which TRABID- and STRIPAK-dependent APC deubiquitylation regulates its axonal trafficking to ensure faithful neurite outgrowth and misregulation of this function leads to neurodevelopmental phenotypes in TRABID/ZRANB1 patients.

Strengths:

This study describes a previously unrecognized function of TRABID in neurodevelopment and establishes knock in mice as model to study congenital defects of TRABID/ZRANB1 patients. In addition, the authors identify control of axonal trafficking of APC by deubiquitylation as a potential mechanism through which TRABID regulates neurite outgrowth and whose dysregulation could be the molecular basis of the neurodevelopmental phenotypes observed in TRABID/ZRANB1 patients.

Weaknesses:

While the proposed underlying mechanism of how hypomorphic TRABID mutations lead to the patient phenotypes is conceivable and supported by the author's data, there is no functional evidence provided that the mouse phenotypes (reduced neuron/glia densities or motor deficits) are indeed due to aberrant APC deubiquitylation and trafficking. In addition, some aspects of the proposed mechanism, i.e. the claim that APC deubiquitylation is STRIPAK-dependent, should be strengthened by orthogonal approaches.

Reviewer #1 (Public Review):

Summary:

This paper shows that E. coli exhibits a chemotactic response to potassium by measuring both the motor response (using a bead assay) and the intracellular signaling response (CheY phosporylation level via FRET) to step changes in potassium concentration. They find increase in potassium concentration induces a considerable attractant response, with an amplitude larger than aspartate, and cells can quickly adapt (but possibly imperfectly). The authors propose that the mechanism for potassium response is through modifying intracellular pH; they find both that potassium modifies pH and other pH modifiers induce similar attractant responses. It is also shown, using Tar- and Tsr-only mutants, that these two chemoreceptors respond to potassium differently. Tsr has a standard attractant response, while Tar has a biphasic response (repellent-like then attractant-like). Finally, the authors use computer simulations to study the swimming response of cells to a periodic potassium signal secreted from a biofilm and find a phase delay that depends on the period of oscillation.

Strengths:

The finding that E. coli can sense and adapt to potassium signals and the connection to intracellular pH is quite interesting and this work should stimulate future experimental and theoretical studies regarding the microscopic mechanisms governing this response. The evidence (from both the bead assay and FRET) that potassium induces an attractant response is convincing, as is the proposed mechanism involving modification of intracellular pH.

Weaknesses:

The authors show that changes in pH impact fluorescent protein brightness and modify the FRET signal; this measurement explains the apparent imprecise adaptation they measured. However, this effect reduces confidence in the quantitative accuracy of the FRET measurements. For example, part of the potassium response curve (Fig. 4B) can be attributed to chemotactic response and part comes from the pH modifying the FRET signal. Measuring the full potassium response curve of the no-receptor mutants as a control would help quantify the true magnitude of the chemotactic response and the adaptation precision to potassium.

The measured response may also be impacted by adaptation. For other strong attractant stimuli, the response typically shows a low plateau before it recovers (adapts). However, in the case of Potassium, the FRET signal does not have an obvious plateau following the stimuli. Do the authors have an explanation for that? One possibility is that the cells may have already partially adapted when the response reaches its minimum, which could indicate a different response and/or adaptation dynamics from that of a regular chemo-attractant? In any case, directly measuring the response to potassium in mutants without adaptation enzymes (CheR, CheB) and with the receptors in different methylation levels would shed more light on the problem.

There seems to be an inconsistency between the FRET and bead assay measurements, the CW bias shows over-adaptation, while the FRET measurement does not. The small hill coefficient of the potassium response curve and the biphasic response of the Tar-only strain, while both very interesting, require further explanation since these are quite different than responses to more conventional chemoattractants.

Reviewer #1 (Public Review):

This study addresses the temporal patterning of a specific Drosophila CNS neuroblast lineage, focusing on its larval development. They find that a temporal cascade, involving the Imp and Syb genes changes the fate of one daughter cell/branch, from glioblast (GB) to programmed cell death (PCD), as well as gates the decommissioning of the NB at the end of neurogenesis.

Reviewer #1 (Public Review):

Summary:

A novel serine protease and an inhibitor pair regulate cell migration in the neural crest. This is a very important study that describes a novel pathway controlling neural crest migratory behavior through a pair of protease and inhibitor regulators that act in the extracellular space. Using very high technical standards in Xenopus embryos they show that knockdown of the inhibitor SerpinE2 prevents cell migration and that this is restored by simultaneous knockdown of the serine protease HtrA1.

Strengths:

The reproduction of classical cranial neural crest extirpations and their phenocopy by SerpinE2 morpholino is remarkable. The experiments provided must represent many years of work, and the paper is written in a very scholarly fashion. The data is of the highest quality.

Weaknesses:

The paper is very long and contains many years of experiments, making it at times difficult to read. The paper contains so much data that it would help the readership if the present version were revised in order to make it more digestible.

Reviewer #1 (Public Review):

Pathogenic mutations of mTOR pathway genes have been identified in patients with malformation of cortical development and intractable epilepsy. Nguyen et al., established an in vivo rodent model to investigate the impact of different mTOR pathway gene dysfunction on neuronal intrinsic membrane excitability and cortical network activity. The results demonstrate that activation of mTORC1 activators or inactivation of mTORC1 repressors leads to convergent mTOR pathway activation and alterations of neuronal morphology, the key pathological feature of human FCD and hemimegalencephaly. However, different mTOR pathway gene mutations also exhibited variations in modulating Ih current and synaptic activity in rodent cortical neurons. These findings provide novel insights into the mechanism of seizure generation associated with cortical malformation.

1. The authors found differences in the initial spike doublet of action potentials between cortical neurons in experimental and control conditions (Figure 2e). The action potential firing frequency of the first two APs (instant firing frequency) of recorded neurons shall be quantified to investigate whether there are statistical differences between the action potential firing frequency in cortical neurons in different experimental groups versus control conditions.

2. The mTORS12215Y induced the largest changes in Ih current amplitudes in cortical neurons compared with other experimental conditions. Whether the HCN4 channel expression is regulated by mTOR pathway activation, or could there be possible interactions between the HCN channel and mTORS12215Y mutant protein?

3. A comparison of the electrophysiological characteristics of cortical neurons in different experimental conditions in the present study and pathological neurons in human FCD reported in previous literature could be interesting. Inducing pathological gene mutations or knocking out key genes in mTOR pathway in the rodent cortex - which approach could better model human FCD?

Reviewer #1 (Public Review):

Summary:

The authors study the appearance of oscillations in motifs of linear threshold systems, coupled in specific topologies. They derive analytical conditions for the appearance of oscillations, in the context of excitatory and inhibitory links. They also emphasize the higher importance of the topology, compared to the strength of the links. Finally, the results are confirmed with WC oscillators, which are also linear. The findings are to some extent confirmed with spiking neurons, though here results are less clear, and they are not even mentioned in the Discussion.

Overall, the results are sound from a theoretical perspective, but I still find it hard to believe that they are of significant relevance for biological networks, or in particular for the oscillations of BG-thalamus-cortex loop in PD. I find motifs in general to be too simplistic for multiscale and generally large networks as is the case in the brain. Moreover, the division of regions is more or less arbitrary by definition, and having such a strong dependence on an odd/even number of inhibitory links is far from reality. Another limitation is the fact that the cortex is considered a single node. Similarly, decomposing even such a coarse network in all possible (238 in this case) motifs doesn't seem of much relevance, when I assume that the emergence of pathological rhythms is more of an emergent phenomenon.

Strengths:

From the point of view of nonlinear dynamics, the results are solid, and the intuition behind the proofs of the theorems is well explained.

Weaknesses:

As stated in the summary, I find the work to be too theoretical without a real application in biological systems or the brain, where the networks are generally very large. It is not the problem in the simplicity of the model or of the topology, it is often the case that the phenomena are explained by very reduced systems, but the problem is that the applicability of the finding cannot be extended. E.g. the Kuramoto model uses all-to-all coupling, or similar with QIF neurons which also need to follow a Lorentzian distribution in order to derive a mean field. But in those cases, relaxing the strict conditions that were necessary for the derivations, still conserves the main findings of the analysis, which I don't see being the case here. The odd/even number rule is too strict, and talking about a fixed and definite number of cycles in the actual brain seems too simplistic.

Being linear is another strong assumption, and it is not clear how much of the results are preserved for spiking neurons, even though there is such an analysis, or maybe for other nonlinear types of neuronal masses.

Delays are also mentioned, and their impact on the oscillatory networks is as expected: it reduces the amplitude, but there is no link to the literature, where this is an established phenomenon during synchronization. Finally, the authors should also discuss the time-delays as a known phenomenon to cause or amplify oscillations at different frequencies in a network of coupled oscillators, e.g Petkoski & Jirsa Network Neuroscience 2022, Tewarie et al. NeuroImage 2019, Davis et al. Nat Commun 2021.

Reviewer #1 (Public Review):

Summary:<br /> The Drosophila wing disc is an epithelial tissue, the study of which has provided many insights into the genetic regulation of organ patterning and growth. One fundamental aspect of wing development is the positioning of the wing primordia, which occurs at the confluence of two developmental boundaries, the anterior-posterior and the dorsal-ventral. The dorsal-ventral boundary is determined by the domain of expression of the gene apterous, which is set early in the development of the wing disc. For this reason, the regulation of apterous expression is a fundamental aspect of wing formation.

In this manuscript, the authors used state-of-the-art genomic engineering and a bottom-up approach to analyze the contribution of a 463 base pair fragment of apterous regulatory DNA. They find compelling evidence about the inner structure of this regulatory DNA and the upstream transcription factors that likely bind to this DNA to regulate apterous early expression in the Drosophila wing disc.

Strengths:<br /> This manuscript has several strengths concerning both the experimental techniques used to address the problem of gene regulation and the relevance of the subject. To identify the mode of operation of the 463 bp enhancer, the authors use a balanced combination of different experimental approaches. First, they use bioinformatic analysis (sequence conservation and identification of transcription factors binding sites) to identify individual modules within the 463 bp enhancer. Second, they identify the functional modules through genetic analysis by generating Drosophila strains with individual deletions. Each deletion is characterized by looking at the resulting adult phenotype and also by monitoring apterous expression in the mutant wing discs. They then use a clever method to interfere in a more dynamic manner with the function of the enhancer, by directing the expression of catalytically inactive Cas9 to specific regions of this DNA. Finally, they recur to a more classical genetic approach to uncover the relevance of candidate transcription factors, some of them previously known and others suggested by the bioinformatic analysis of the 463 bp sequence. This workflow is clearly reflected in the manuscript, and constitutes a great example of how to proceed experimentally in the analysis of regulatory DNA.

Weaknesses:<br /> There are several caveats with the data that might be constructed as weaknesses, some of them are intrinsic to this detailed analysis or to the experimental difficulties of dealing with the wing disc in its earliest stages, and others are more conceptual and are offered here in case the authors may wish to consider them.

1) The primordium of the wing region of the wing imaginal disc is defined by the expression of the gen vestigial, which is regulated by inputs coming from the dorsal-ventral boundary (Notch and wg) and from the anterior-posterior boundary (Dpp). Having such a principal role in wing primordium specification and expansion, I am surprised that this manuscript does not mention this gene in the main text and only contains indirect references to it. I consider that the manuscript would have benefited a lot by including vestigial in the analysis, at least as a marker of early wing primordium. This might allow us to visualize directly the positioning of the primordium in the apterous mutants generated in this study, adding more verisimilitude to the interpretations that place this domain based on indirect evidence.

2) The authors place some emphasis on the idea that their work addresses possible coordination between setting the D/V boundary and the A/P boundary:

Abstract: "Thus, the correct establishment of ap expression pattern with respect to en must be tightly controlled", "...challenging the mechanism by which apE miss-regulation leads to AP defects." "Detailed mutational analyses using CRISPR/Cas revealed a role of apE in positioning the DV boundary with respect to the AP boundary"<br /> Introduction: "However, little is known about how the expression pattern of ap is set up with respect that of en. In other words, how is the DV boundary positioned with respect to the AP boundary?"<br /> "How such interaction between ap and the AP specification program arises is unknown."<br /> Results: "Some of these phenotypes are reminiscent of those reported for apBlot (Whittle, 1979) and point towards a yet undescribed crosstalk between ap early expression and the AP specification program."

At the same time, they express the notion, with which this reviewer agrees, that all defects observed in A/P patterning arising as a result of apterous miss-regulation are due to the fact that in their mutants, apterous expression is lost mainly in the posterior dorsal compartment, bringing novel confrontations between the A/P and the D/V boundaries.

To me, the key point is why the expression of apterous in different mutants of the OR463 enhancer affects only the posterior compartment. This should be discussed because it is far from obvious that apterous expression has different regulatory requirements in the anterior and posterior compartments.

3) The description of gene expression in the wing disc of novel apterous mutants is only carried out in late third instar discs (Figs. 2, 3, 5, and 7). This is understandable given the technical difficulties of dealing with early discs, as those shown in the analysis of candidate apterous regulatory transcription factors (Fig. 4F, Fig. 6 C-D). However, because the effects of the mutants on apterous expression are expected to occur much earlier than the time of expression analysis, this fact should be discussed.

Joint Public Review:

In this work Wu, J., et al., highlight the importance of a previously overlooked region on kinases: the αC-β4 loop. Using PKA as a model system, the authors extensively describe the conserved regulatory elements within a kinase and how the αC-β4 loop region integrates with these important regulatory elements. Previous biochemical work on a mutation within the αC-β4 loop region, F100A showed that this region is important for the synergistic high affinity binding of ATP and the pseudo substrate inhibitor PKI. In the current manuscript, the authors assess the importance of the αC-β4 loop region using computational methods such as Local Spatial Pattern Alignment (LSP) and MD simulations. LSP analysis of the F100A mutant showed decreased values for degree centrality and betweenness centrality for several key regulatory elements within the kinase which suggests a loss in stability/connectivity in the mutant protein as compared to the WT. Additionally, based on MD simulation data, the side chain of K105, another residue within the αC-β4 loop region had altered dynamics in the F100A mutant as compared to the WT protein. While these changes in the αC-β4 loop region seem to be consistent with the previous biochemical data, the results are preliminary and the manuscript can be strengthened (as the authors themselves acknowledge) with additional experiments. Specific comments/concerns are listed below.

1. MD simulations were carried out using a binary complex of the catalytic subunit of PKA and ATP/Mg and not the ternary complex of PKA, ATP/Mg and PKI. MD simulations carried out using the ternary complex instead of the binary complex would be more informative, especially on the role of the αC-β3 loop region in the synergistic binding of ATP/Mg and PKI.

2. The LSP analysis shows a decrease in degree centrality for the αC-β4 loop region in the F100A mutant compared to the WT protein which suggests a gain in stability in this region for the F100A mutant (Fig. 8A). These results seem to be contradictory to the MD simulation data which shows the side chain dynamics of K105 destabilizes the αC-β4 loop region in the F100A mutant (Fig. 10B). It would be helpful if the authors could clarify this apparent discrepancy.

3. The foundation for the experiments carried out in this paper are based on previous NMR and computational data for the F100A mutant. However, the specific results and conclusions from these previous experiments are not clearly described.

Reviewer #1 (Public Review):

Summary:<br /> This work seeks to isolate the specific effects of phosphoinositide 3-kinase (PI3K) on the trafficking of the ion channel TRPV1, distinct from other receptor tyrosine kinase-activated effectors. It builds on earlier studies by the same group (Stein et al. 2006; Stratiievska et al. 2018), which described the regulatory relationship between PI3K, nerve growth factor (NGF), and TRPV1 trafficking. A central theme of this study is the development of methods that precisely measure the influence of PI3K on TRPV1 trafficking and vice versa. The authors employ a range of innovative methodologies to explore the dynamics between TRPV1 and PI3K trafficking.

Strengths:<br /> A major strength of this study is the application of innovative methods to understand the interaction between PI3K and TRPV1 trafficking. The key techniques presented include:

1) The optogenetic trafficking system based on phytochrome B, introduced in this research. Its interaction mechanism, dependent on reversible light activation, is comprehensively explained in Figures 1 and 2, with the system's efficacy demonstrated in Figure 3.

2) An extracellular labeling method using click chemistry, which although not exclusive to this study, introduces specific reagents engineered for membrane impermeability.

The central biological insight presented here is the sufficiency of PI3K activation to guide TRPV1 trafficking to the plasma membrane. An additional notable discovery is the potential regulation of insulin receptors via this mechanism.

The paper's strengths are anchored in its innovative methodologies and the valuable collaboration between groups specializing in distinct areas of research.

Weaknesses:<br /> The paper might benefit from a more streamlined structure and a clearer emphasis on its findings. A possible way to enhance its impact might be to focus more on its methodological aspects. The methodological facets stand out as both innovative and impactful. These experiments are well-executed and align with biological expectations. It's evident how these techniques could be tailored for many protein trafficking studies, a sentiment echoed in the manuscript (lines 287-288). When seen through a purely biological lens, some findings, like those concerning the PI3K-TRPV1 interaction, are very similar to previous work (Stratiievska et al. 2018). A biological focus demands further characterization of this interaction through mutagenesis. Also, the incorporation of insights on the insulin receptor feels somewhat tangential. A cohesive approach could be to reshape the manuscript with a primary focus on methodology, using TRPV1 and InsR as illustrative examples.

Reviewer #1 (Public Review):

• A summary of what the authors were trying to achieve.

The authors cultured pre- and Post-vaccine PBMCs with overlapping peptides encoding S protein in the presence of IL-2, IL-7, and IL-15 for 10 days, and extensively analyzed the T cells expanded during the culture; by including scRNAseq, scTCRseq, and examination of reporter cell lines expressing the dominant TCRs. They were able to identify 78 S epitopes with HLA restrictions (by itself represents a major achievement) together with their subset, based on their transcriptional profiling. By comparing T cell clonotypes between pre- and post-vaccination samples, they showed that a majority of pre-existing S-reactive CD4+ T cell clones did not expand by vaccinations. Thus, the authors concluded that highly-responding S-reactive T cells were established by vaccination from rare clonotypes.

• An account of the major strengths and weaknesses of the methods and results.

Strengths<br /> • Selection of 4 "Ab sustainers" and 4 "Ab decliners" from 43 subjects who received two shots of mRNA vaccinations.<br /> • Identification of S epitopes of T cells together with their transcriptional profiling. This allowed the authors to compare the dominant subsets between sustainers and decliners.

Weaknesses<br /> • Fig. 3 provides the epitopes, and the type of T cells, yet the composition of subsets per subject was not provided. It is possible that only one subject out of 4 sustainers expressed many Tfh clonotypes and explained the majority of Tfh clonotypes in the sustainer group. To exclude this possibility, the data on the composition of the T cell subset per subject (all 8 subjects) should be provided.<br /> • S-specific T cells were obtained after a 10-day culture with peptides in the presence of multiple cytokines. This strategy tends to increase a background unrelated to S protein. Another shortcoming of this strategy is the selection of only T cells amenable to cell proliferation. This strategy will miss anergic or less-responsive T cells and thus create a bias in the assessment of S-reactive T cell subsets. This limitation should be described in the Discussion.<br /> • Fig. 5 shows the epitopes and the type of T cells present at baseline. Do they react to HCoV-derived peptides? I guess not, as it is not clearly described. If the authors have the data, it should be provided.<br /> • As the authors discussed (L172), pre-existing S-reactive T cells were of low affinity. The raw flow data, as shown in Fig. S3, for pre-existing T cells may help discuss this aspect.

Reviewer #1 (Public Review):

Drawing on insights from preceding studies, the researchers pinpointed mutations within the spag7 gene that correlate with metabolic aberrations in mice. The precise function of spag7 has not been fully described yet, thereby the primary objective of this investigation is to unravel its pivotal role in the development of obesity and metabolic disease in mice. First, they generated a mice model lacking spag7 and observed that KO mice exhibited diminished birth size, which subsequently progressed to manifest obesity and impaired glucose tolerance upon reaching adulthood. This behaviour was primarily attributed to a reduction in energy expenditure. In fact, KO animals demonstrated compromised exercise endurance and muscle functionality, stemming from a deterioration in mitochondrial activity. Intriguingly, none of these effects was observed when using a tamoxifen-induced KO mouse model, implying that Spag7's influence is predominantly confined to the embryonic developmental phase. Explorations within placental tissue unveiled that mice afflicted by Spag7 deficiency experienced placental insufficiency, likely due to aberrant development of the placental junctional zone, a phenomenon that could impede optimal nutrient conveyance to the developing fetus. Overall, the authors assert that Spag7 emerges as a crucial determinant orchestrating accurate embryogenesis and subsequent energy balance in the later stages of life.

The study boasts several noteworthy strengths. Notably, it employs a combination of animal models and a thorough analysis of metabolic and exercise parameters, underscoring a meticulous approach. Furthermore, the investigation encompasses a comprehensive evaluation of fetal loss across distinct pregnancy stages, alongside a transcriptomic analysis of skeletal muscle, thereby imparting substantial value. However, a pivotal weakness of the study centres on its translational applicability. While the authors claim that "SPAG7 is well-conserved with 97% of the amino acid sequence being identical in humans and mice", the precise role of spag7 in the human context remains enigmatic. This limitation hampers a direct extrapolation of findings to human scenarios. Additionally, the study's elucidation of the molecular underpinnings behind the spag7-mediated anomalous development of the placental junction zone remains incomplete. Finally, the hypothesis positing a reduction in nutrient availability to the fetus, though intriguing, requires further substantiation, leaving an aspect of the mechanism unexplored.

Hence, in order to fortify the solidity of their conclusions, these concerns necessitate meticulous attention and resolution in the forthcoming version of the manuscript. Upon the comprehensive addressing of these aspects, the study is poised to exert a substantial influence on the field, its significance reverberating significantly. The methodologies and data presented undoubtedly hold the potential to facilitate the community's deeper understanding of the ramifications stemming from disruptions during pregnancy, shedding light on their enduring impact on the metabolic well-being of subsequent generations.

Reviewer #1 (Public Review):

The authors start from the premise that neural circuits exhibit "representational drift" -- i.e., slow and spontaneous changes in neural tuning despite constant network performance. While the extent to which biological systems exhibit drift is an active area of study and debate (as the authors acknowledge), there is enough interest in this topic to justify the development of theoretical models of drift.

The contribution of this paper is to claim that drift can reflect a mixture of "directed random motion" as well as "steady state null drift." Thus far, most work within the computational neuroscience literature has focused on the latter. That is, drift is often viewed to be a harmless byproduct of continual learning under noise. In this view, drift does not affect the performance of the circuit nor does it change the nature of the network's solution or representation of the environment. The authors aim to challenge the latter viewpoint by showing that the statistics of neural representations can change (e.g. increase in sparsity) during early stages of drift. Further, they interpret this directed form of drift as "implicit regularization" on the network.

The evidence presented in favor of these claims is concise. Nevertheless, on balance, I find their evidence persuasive on a theoretical level -- i.e., I am convinced that implicit regularization of noisy learning rules is a feature of most artificial network models. This paper does not seem to make strong claims about real biological systems. The authors do cite circumstantial experimental evidence in line with the expectations of their model (Khatib et al. 2022), but those experimental data are not carefully and quantitatively related to the authors' model.

To establish the possibility of implicit regularization in artificial networks, the authors cite convincing work from the machine-learning community (Blanc et al. 2020, Li et al., 2021). Here the authors make an important contribution by translating these findings into more biologically plausible models and showing that their core assumptions remain plausible. The authors also develop helpful intuition in Figure 4 by showing a minimal model that captures the essence of their result.

In Figure 2, the authors show a convincing example of the gradual sparsification of tuning curves during the early stages of drift in a model of 1D navigation. However, the evidence presented in Figure 3 could be improved. In particular, 3A shows a histogram displaying the fraction of active units over 1117 simulations. Although there is a spike near zero, a sizeable portion of simulations have greater than 60% active units at the end of the training, and critically the authors do not characterize the time course of the active fraction for every network, so it is difficult to evaluate their claim that "all [networks] demonstrated... [a] phase of directed random motion with the low-loss space." It would be useful to revise the manuscript to unpack these results more carefully. For example, a histogram of log(tau) computed in panel B on a subset of simulations may be more informative than the current histogram in panel A.

Reviewer #1 (Public Review):

C. elegans is a pre-eminent model for developmental genetics, and its invariant lineage makes it possible in theory to define molecular features such as gene expression comprehensively and at single cell resolution across the organism.

Previously published single-cell RNA-seq studies have mapped gene expression across the lineage through the 16-cell stage (Tintori et al 2017, Hashimshony et al 2016), and at later stages (Packer et al 2019, with good coverage starting at the 100-cell stage and some coverage at the ~50-cell stage). This left the critical period around gastrulation (~28-cell and ~50-cell) without comprehensive transcriptome data. This study covers this gap with a heroic effort involving the manual isolation and analysis of over 800 cells from embryos of known stage, combined with painstaking curation using known markers from small scale studies and larger imaging-based expression atlases. Importantly, the dataset overlaps at early and late stages with data prior studies.

The data quality and overlap with Tintori and Packer datasets both appear high, but to make this inference required additional analysis from Supplemental Table 6 by this reviewer as it is not explored or described in the manuscript. Analyses demonstrating continuity with these datasets would greatly increase the value of the resource.

The authors show that specific lineages and stages preferentially express TFs with different classes of DNA binding domains. This extends previous work implicating homeodomains as preferentially involved in nervous system patterning and as enriched in neural and muscle progenitors in mid-stage embryos.

They also show that C. elegans homologs of Drosophila early embryonic regulators (which function based on spatial position in that system) tend to also be patterned in early C. elegans embryos, but with lineage-specific patterns. This conserved use of regulators would be fairly remarkable given the dramatically different developmental modes in these two species, although this observation is not backed up by quantitative analyses.

Finally, there is an argument that combinations of TFs expressed in lineage-specific patterns give rise to "stripe" patterns. This section is also not based on statistical analyses but suggests the possibility that lineage and positional regulation may be more convoluted than was previously thought.

Reviewer #1 (Public Review):

In this manuscript, the authors have performed extensive imaging analysis of six human histone H1 variants, their enrichment and localization, their differential dynamics during interphase and mitosis, and their association with lamina-associated domains (LADs) or nucleolus-associated domains. The manuscript is well-written with high-quality confocal and super-resolution images. Various interesting observations are made on distribution patterns of H1 variants. H1.2, H1.3, and H1.5 are shown to be universally enriched at the nuclear periphery whereas H1.4 and H1X are found to be distributed throughout the nucleus. Interestingly, H1X was the only H1 variant found to be abundant in nucleoli. Depletion of H1 variants has been shown to affect chromatin structure in a variant-specific manner, with H1.2 knock-down resulting in global chromatin decompaction. Overall, the study presents several interesting insights on H1 variants conducted in a large number of cell lines.

Major Comments:<br /> 1) Though the co-immunostaining of a nucleolar marker (NPM1) is performed with H1X, it would be interesting to explore the localization of H1 variants with respect to some of the proteins critically involved in chromatin organization such as PC4 or HP1alpha. Since the phosphorylated form of PC4 has been shown to interact with H1, which variants specifically interact with PC4 and how their dynamic changes in interphase and mitosis would be worth exploring.

2) The manuscript would be a complete study if any physiological significance with the H1 variant distribution could be shown.

Reviewer #1 Public Review

Summary<br /> This paper presents a new, but simple and low-cost technique for multimodal EM imaging that combines the strengths of both 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 here. The most important feature of ATUM-Tomo, particularly of correlative ATUM-Tomo, is that it can bridge scales, from the cellular to the high-resolution subcellular scale, from micrometer to low nanometer resolution. This is particularly important for ultrastructural analyses of biological regions of interest, which is demonstrated here for focal pathologies or rare cellular and subcellular events. Both imaging modalities are non-destructive, thus allowing re-imaging and hierarchical imaging at the SEM and TEM levels. This is particularly important for precious samples, including human biopsies and samples from complex CLEM experiments. Beyond the demonstrated neuropathology-related application, further use in investigating normal and pathologically altered brains, including human brain tissue samples that require high-resolution SEM and TEM in combination with immunohistochemistry, and virus or tracer injections, would be possible. Thus, ATUM-Tomo provides new possibilities in multimodal volume EM imaging for diverse areas of biological research.

Strengths<br /> This paper is a very nice piece of work, bringing together modern high-end state-of-the-art technology that will allow us to investigate diverse biological questions in different areas of interest and at different scales. The paper is clear and well-written, although some additions are necessary to the methods section and the scientific results as exemplified by investigations of the blood-brain barrier. The discussion would benefit from an expansion of the part dealing with the scientific results. The paper is accompanied by excellent figures, supplemental information, and colored 3D-reconstructions, which makes it easy for the reader to follow the experimental procedure and the scientific context. The authors may consider moving the supplemental figures into the main body of the paper, which would then still contain 'only' eight figures.

Weaknesses<br /> There is some imbalance between the description of the state-of-the-art methodology and the scientific context.

Reviewer #1 (Public Review):

Sun and co-authors have determined the crystal structures of EHEP with/without phlorotannin analog, TNA, and akuBGL. Using the akuBGL apo structure, they also constructed model structures of akuBGL with phlorotannins (inhibitor) and laminarins (substrate) by docking calculation. They clearly showed the effects of TNA on akuBGL activity with/without EHEP and resolubilization of the EHEP-phlorotannin (eckol) precipitate under alkaline conditions (pH >8). Based on this knowledge, they propose the molecular mechanism of the akuBGL-phlorotannin/laminarin-EHEP system at the atomic level. Their proposed mechanism is useful for further understanding of the defensive-offensive association between algae and herbivores.

Reviewer #1 (Public Review):

Gambelli et al. provide a structural study of the SlaA/SlaB S-layer of the archaeon Sulfolobus acidocaldarius. S-layers form an essential component of most archaeal cell envelopes, where their self-assembling properties and activity as cell envelope support structures have raised substantial interest, both from researchers seeking to understand the fundamental biology of archaea, as well as researchers seeking to exploit the biomaterial properties of S-layers in biotechnological applications. Both interests are hampered by the paucity of structural information on archaeal S-layer assembly, structure, and function to date, in large part due to technical difficulties in their study.

In this study, Gambelli and coworkers overcome these difficulties and report the high-resolution 3D cryoEM structures of the purified SlaA monomers at three different pH, as well as the medium resolution 3D cryoET structures of the SlaA/SlyB lattices determined from S-layer fragments isolated from the Sulfolobus cells.

The structural work is generally well executed, although lacks in detail in places to allow a proper review, particularly in the cryoET. A further drawback of the current manuscript is that the structural work remains rather descriptive and speculative, with little validation of the proposed models.

The authors run a plethora of representation, analyses, prediction, and simulation software on their structures resulting in an abundance of Figures that risk overloading the reader and in several cases bring little new insight beyond unsubstantiated speculation.

The structural description of the S. acidocaldarius S-layer will be of high general interest and the authors have made a substantial leap forward, but the current manuscript would benefit from a better validation and basic atomic description of the SlaA/SlaB S-layer.

Specific points.

- It is not possible to review the quality of the SlaA and SlaA/SlaB models in the cryoET reconstruction. No detailed fits of the map and model are shown, and no correlation statistics are given (the latter is also true for the higher resolution 3D reconstructions at pH4, 7, and 10). To be of use to the community, the S-layer model and cryoET maps should also be deposited in PDB and EMDB, and an autodep report and ideally the cryoET maps should be available.

- The authors spend a great deal on the MD simulation of the SlaA glycans and the description of the 'glycan shield' and its possible role in subunit electrostatics and intersubunit contacts. This does not result in testable hypotheses, however, and does not bring much more than vague speculation on the role of the glycans or the subunits contacts in S-layer assembly and stability. For the primary description of the SlaA/B S-layer, more important would be a detailed atomic description and validation of the intermolecular contacts in the proposed lattice model. Given the low resolution of the cryoET, this would require MD simulation of the contacts. Lattice stability during MD simulation and/or the confirmation of lattice contacts by cross-linking mass spectrometry would go a great way in validating the proposed lattice model.

- The discussion of the subunit electrostatics and the role they could play in subunit assembly/disassembly remains superficial and speculative. No real model or hypothesis is put forward, let alone validated.

- The authors solve the cryoEM structure of SlaA released and purified form S. acidocaldarius S-layers by an alkaline pH shift. When shifted back to acidic pH, does this native material self-assemble in vitro? If not, do the authors have an explanation for this? Are components missing or could the solved structures represent SlaA conformations that are no longer assembly competent?

Reviewer #1 (Public Review):

The manuscript by Royall et al. builds on previous work in the mouse that indicates that neural progenitor cells (NPCs) undergo asymmetric inheritance of centrosomes and provides evidence that a similar process occurs in human NPCs, which was previously unknown.

The authors use hESC-derived forebrain organoids and develop a novel recombination tag-induced genetic tool to birthdate and track the segregation of centrosomes in NPCs over multiple divisions. The thoughtful experiments yield data that are concise and well-controlled, and the data support the asymmetric segregation of centrosomes in NPCs. These data indicate that at least apical NPCs in humans undergo asymmetric centrosome inheritance. The authors attempt to disrupt the process and present some data that there may be differences in cell fate, but this conclusion would be better supported by a better assessment of the fate of these different NPCs (e.g. NPCs versus new neurons) and would support the conclusion that younger centriole is inherited by new neurons.

Reviewer #1 (Public Review):

Myelodysplastic syndrome (MDS) represents as a rather complex and serious hematologic malignancy that affects the production of normal blood cells in the bone marrow. Some types of MDS could stay mild for years and other types of MDS could be more serious and progressed into AML. Tremendous efforts have been made to investigate the pathogenesis and treatment of MDS. For instance, a pile of papers has found that iron chelation therapy could benefit the overall survival in low risk MDS patients. Yet, the risk and benefit of this therapy remain in much debate. The authors demonstrated that erythrocyte precursors could re-gain EPO responsiveness after DFP chelation therapy. In addition, the authors investigated iron trafficking in erythroblasts using the MDS mouse model. The paper is rather interesting as it discussed the biological effects and underlying mechanisms of DFP for the treatment of low-risk MDS. More importantly, the paper adds practical values and theoretical evidences for chelation therapy towards low-risk MDS. The paper is overall well-written.

Reviewer #1 (Public Review):

In this manuscript, Kim et al. investigate the molecular basis for hindbrain segmentation by performing combined single cell nucleus RNAseq and ATACseq (scMultiome) on zebrafish embryonic hindbrain tissue. Hindbrain segmentation is fundamental to head development in vertebrate species. Decades of research have provided many insights into the gene regulatory cascades that control the progressive subdivision of the hindbrain territory into segments (rhombomeres). These studies have enabled the formulation of gene regulatory network (GRN) models that depict these regulatory interactions. However, many aspects of the GRN need further clarification, including the early steps of pre-rhombomeric patterning, and the factors that respond to axial signaling pathways such as RA and FGF. The dataset in this study provides a comprehensive view of gene expression and chromatin states during hindbrain segmentation, thus it is a valuable resource for characterizing the underlying GRN. The authors demonstrate the utility of this data by comparing the molecular profiles between different rhombomeres and tracing when and how these profiles arise during development.

Four main findings are presented:

1. Each rhombomere has a unique molecular profile.<br /> 2. There is no clear molecular signature for odd versus even rhombomeres, nor any overt repeating two-segment molecular identities.<br /> 3. The mature rhombomeres emerge through the subdivision of three mixed-identity 'primary hindbrain progenitor domains' (PHPDs) that correspond to r2/r3, r4, and r5/r6, respectively.<br /> 4. RA and FGF signaling control formation of the primary hindbrain progenitor domains.

These findings are well supported by the data but in my opinion they mainly confirm what was already known and do not significantly advance our mechanistic understanding of rhombomere formation, which is the aim of the paper.

Strengths:<br /> This comprehensive dataset will be very valuable to researchers in the field. The authors successfully demonstrate its utility by resolving unique molecular profiles for each rhombomere and identifying some novel markers.

The authors make excellent use of HCR to validate their findings, such as the co-expression of vgll3 and egr2b in r2/r3 cells at 10hpf, which implies mixed identities of PHPD cells.

The performance of scMultiome analysis on tissue from DEAB-treated embryos (depleted RA signaling) is exciting and holds much promise for identifying RA-dependent gene regulatory cascades that govern caudal hindbrain patterning. Assessing the contribution of control versus DEAB-treated cells to the various UMAP clusters is a very nice way to identify the altered cell states in the RA-depleted hindbrain. This confirms a complete absence of r5 and r6 in the DEAB-treated embryos at this developmental stage, as was inferred from in-situ approaches in earlier studies.

Weaknesses:<br /> The major weakness of this work is that it only provides an incremental mechanistic advance to our current understanding of the molecular basis for rhombomere formation. The descriptions of gene expression are useful but for the most part they are rather shallow lines of enquiry that confirm what was already known from previous, less comprehensive studies of gene expression. For example, regarding the identification of PHPDs, it has long been known that r5/r6 share a progenitor domain that is demarcated by mafba expression. Similarly, RA and Fgf signaling have already been shown to be required for anterior-posterior patterning in the pre-rhombomeric hindbrain. The identification of mixed-identity progenitors in PHPDs, and the characterisation of the changes in transcription and chromatin state in response to RA signaling perturbation are really exciting starting points for deeper analysis of the underlying GRN. However, it is a shame that no effort is made to glean mechanistic insights from this dataset by computational GRN inference.

Reviewer #1 (Public Review):

This manuscript by Proskurin, Manakov, and Karpova, posits a unique role for the anterior cingulate cortex (ACC) in the flexible control of learned sequences of motor actions. The authors marshall evidence from behavioral-electrophysiological analyses in support of two major claims: 1) that action encoding by ACC ensembles tracks 1) the current "context", i.e., which behavioral sequence is rewarded, and 2) the "prevalence", i.e., number of repetitions of one specific sequence. An important aspect of this later point is that the authors propose prevalence encoding is not strictly dependent on trial-by-trial reward receipt.

In this work, the authors wish to focus on self-initiated behavior when the correct behavioral sequence, out of four or fewer (mostly two it appears), changes across blocks in an unsignaled manner. Rats learn to enter a left and right nose poke in a sequence of three responses, with a required entry into a central port prior to each intra-sequence response, with correct sequence completion reinforced by a sucrose delivery in the relevant side nose poke port. Extracellular spike activity is acquired from well-trained rats performing this task. The authors' analyses of the behavior of well-trained rats show rats adjust their behavior when the block switches to a different one of the sequences in the known 'library'. The rats also perform non-reinforced responses/sequences within a given block which the authors suggest is exploration likely not triggered by changes in reinforcement in contrast to behavior change after a block switch.

The authors next provide a very rich set of analyses to examine the encoding of responses and sequences by ACC neural activity. Overall, these data provide intriguing support for ACC's integral contributions to flexible behavioral control. However, some of the individual analyses are a bit difficult to follow and could be clarified with greater detail within the results section of the paper, permitting an easier evaluation of the quality of the supporting data. Second, there are some proposals that could be strengthened by fuller analysis, in particular the authors' suggestion that "prevalence" encoding is distinct from reward encoding and/or is not impacted by reward presence or omission. Given the likely rich data set in hand, the authors could do more to demonstrate how "prevalence" encoding interacts with reinforcement parameters or perhaps be more specific in their word choice. More importantly, I was left unclear on how "prevalence" encoding intersects with the decision to repeat the same behavioral sequence on the next trial or not. These issues aside, this work provides further information on the physiology of ACC during flexible behavior and will add importance to this field.

Below are specific issues:

1. Some greater attention to the behavioral parameters could be helpful, especially regarding the impact of reward rate on behavior. For example, looking at some of the figures of individual rat behavior, exploratory sequences seemed triggered by reward omission. Is this just a chance for the examples chosen or is there something systematic here? Upon block switch, how exactly does the switch in sequences emitted by the rat track with reinforcement history? The authors mention that reinforcement probability differed across sessions, and one would thus expect switching behavior would as well. Because of the interesting existence of sometimes quite long 'tails' of performance of the original sequence after a block switch, I am wondering how the length of such tails relates to reinforcement rate parameters.

2. The authors provide strong data indicating that a given L or R response is associated with distinct ACC activity depending on which sequence that response is embedded within, a finding reminiscent of other reports in multiple brain regions. While not a criticism per se, I was interested in the center port responses, also embedded within unique sequences, yet never preceding reward. A key difference in the performance of a given R or L response is that it is sometimes the terminal response, and thus the rat knows a given R or L response to be sometimes reinforced in one of the contexts, but not the other, in each of these comparisons. I wonder if there was an opportunity to cleanly demonstrate the context dependence of a given individual action by comparing center port responses across distinct sequences.

3. In analyzing neural activity accompanying the behavioral persistence of the dominant sequence after a block change, the authors find that the ACC ensemble firing pattern is closer to the original dominant sequence pattern during reinforcement and less like this pattern during exploration. This makes sense and must be the case, as, in the example shown in the figure, the rat does not "know" the block has switched since no reward has yet been delivered that would signal that switch. (As an aside, it would be interesting to know, given a specific reward schedule in a given session, what would be the maximum number of unrewarded trials within the block, and how might that impact the performance/reward expectation during the tails?)<br /> As time, and trials, progress the rat is approaching the point at which it explores another strategy. The authors find strengthened "prevalence" encoding with increasing sequence repetition, but if this parameter is related to behavioral change/flexibility, this was not clear to me. Might there be something unique about the last trials in a tail "predicting" an upcoming switch? Can the authors please expand?<br /> Relatedly, if the prediction of upcoming behavioral change is not observed in the neural activity from sequence steps 2-6, it is notable that these are the steps 'within' the sequence, that leaves out the initiation (first center poke) and termination (reward/reward omission). Thus one could imagine this information is "missed" in the current analysis given that both the reward period and the initiation of a trial at the center are not analyzed. This does lead me to suggest a softening of some claims made of identifying "unifying principles" of ACC function, as the authors state, based on the analyses included in the current report, since the neural activity related to the full unit of behavior is not considered. (I appreciate the motivation behind this focus on within-sequence behavior - the wish to compare time periods with similar movement parameters .)

4. The variance in neural activity explained by the prevalence models is on average quite low. However, the authors find that the variance explained differs quite dramatically by anatomical coordinate within ACC. Would it make sense to focus the control analyses (vigor, reward history, and so on) on those sessions/ensembles with greater variance explained, ie, perhaps there might be greater sensitivity to detecting interactions among variables within ensembles recorded more rostrally?

5. A very intriguing aspect of this work is the position that (from the abstract): "Prevalence encoding in the ACC is ...independent of reward delivery." This is a novel aspect of the current work. However, I am wondering if the authors can refine and expand upon this. I find it difficult to disentangle prevalence encoding and impacts of reward in the way the data and interpretation are presented in some areas of the text. While neural encoding may not reflect trial-by-trial reward receipt, clearly the rat's decision to repeat a given sequence or initiate a new sequence is impacted by reinforcement parameters and reward expectation. Thus being very exact in the interpretation would be helpful.

Reviewer #1 (Public Review):

Summary:

Fox, Dan, and Loewenstein investigated how people explored six maze-like environments. They show that roughly one-third of their participants make choices now that increase the potential for future information gain and also temporally discount potential information gain based on how far in the future potential gains might be. The authors argue that rather than valuing exploration in its own right, participant behavior is most consistent with using exploration as a way to reduce uncertainty. They then propose a reinforcement learning (RL) model in which agents estimate an "exploration value" (the expected cumulative information gained by taking a given action in a given state) using standard RL techniques for estimating value (expected cumulative reward). They find that this model exhibits several qualitative similarities with human behavior and that it best captures the temporal dynamics of human exploration when propagating information through the entire history of a behavioral episode (as opposed to merely propagating it in a single step as some of the simplest RL models do).

While the core insight and basic method of the paper are compelling, the way in which both the behavioral experiment and computational modeling were conducted raise concerns that mean that, in their present form, the results do not fully justify the conclusions. After resolving these issues, the work would demonstrate how human exploration is sensitive to long-range dependencies in information gain, as well as valuable insights about how best to characterize this behavior computationally. I am not particularly well-versed in the literature on exploration so cannot comment on novelty here.

Strengths:<br /> The entire paper is logically well-motivated. It builds on a valuable basic insight, namely that while bandit tasks are an ideally minimal platform for testing certain questions about decision-making and exploration, richer paradigms are needed to capture the long-range informational dependencies distinguishing between various approaches to exploration.

Even so, the maze navigation paradigm explored here remains simple. Participants navigate a maze with two main branches which are identical save for minimal, theoretically motivated differences. Moreover, the tested differences are designed to clearly and explicitly test well-identified questions. The task, and really the entire paper, is clearly organized, and each component is logically connected to a larger argument.

The proposed model is also simple, clearly presented, and a clever way of applying ideas typically used to reason about reward-motivated behavior to reason here about information-motivated behavior.

One other strength of this work is that it combines behavioral experiments with computational modeling. This approach pairs a detailed and objectively specified theory (i.e. the model) with novel data specifically designed to test that theory and thus in principle presents a particularly strong test of the authors' hypotheses.

Weaknesses:<br /> Despite many strengths in the underlying logic of the paper, the presented evidence does not provide compelling support for the conclusions. In particular:

- The main claims are based on the behavior of 452 participants classed as good explorers, out of 1,052 participants included in the analyses and 1,336 participants who completed the study. That is, the authors' broad claims about human exploration are based on a third of their total sample; the other two-thirds displayed very different behavior, including 20% who performed at or below chance levels. That is, while a significant sub-population may demonstrate the claimed abilities, it is far from clear that they are universal.

- While the experimental manipulations are elegant, the behavioral study seems underpowered. In each of the primary manipulations, key theoretical predictions are not statistically validated. For example, in Experiment 1, the preference for the right door increases from the 4:3 condition to the 5:2 condition, but not when moving from the 5:2 condition to the 6:1 condition, as predicted (Figure 1c). Similar results can be seen for other analyses in Figures 3b and 4b. Relatedly, the experiments comprised just 20 episodes, and it is unclear whether that was sufficiently long for participants to demonstrate asymptotic behavior (e.g. Figure 5b). Either more participants or greater differences between conditions (e.g. testing 9:8, 12:5, and 15:2 conditions in a revised Experiment 1), as well as running a greater number of total episodes, would be needed to resolve this concern.

- The model is presented after the behavioral results, giving the impression that it was perhaps constructed to fit the data. No attempt is made to fit the model to a subset of the data and then validate the rest or give any clear indication as to how the model parameters were set. Moreover, as noted, even where the model is successful, it only explains the behavior of a minority of the total participants. No modeling work is done to explain the behavior of the other two-thirds of the participants.

- The authors helpfully discuss several meaningful alternative models of exploration, such as visit-counting and incorporating an objective function sensitive to information gain. They do not, however, compare their model against these or any other meaningful baselines. Moreover, the comparison between model and human participants is qualitative rather than quantitative. These issues could be resolved by introducing a more rigorous analysis quantitatively comparing a variety of theoretically relevant models as quantitative explanations of the human data.

Reviewer #1 (Public Review):

In this study, the authors utilise different chemical inhibitors and celular markers to examine the roles of macropinocytosis in WNT signalling activation in development (Xenopus), cell culture (3T3 cells) and cancer (CRC sections). Furthermore, they investigate the effect of the inflammation inducer Phorbol-12-myristate-13-acetate (PMA) in WNT signalling activation through macropinocytosis. The authors show 1) that PMA induces macropinocytosis-dependent WNT signalling activation, and 2) that CRC development correlates with increased levels and co-localisation of macropinocytosis components and b-catenin.

I found the analyses and conclusions compelling. Additional epistatic analyses could be done in the future to further disentangle the roles of macropinocytosis during WNT signalling activation, especially upon oncogenic alterations (e.g. in APC). The studies on CRC samples open interesting questions for specialists in tumour progression.

Reviewer #1 (Public Review):

Summary:<br /> Ngoune et al. present compelling evidence that Slender cells are challenged to infect tsetse flies. They explore the experimental context of a recent important paper in the field, Schuster et al., that presents evidence suggesting the proliferative Slender bloodstream T.brucei can infect juvenile tsetse flies. Schuster et al. were disruptive to the widely accepted paradigm that the Stumpy bloodstream-form is solely responsible for tsetse infection and T.brucei transmission potential.

Evidence presented here shows that in all cases, Stumpy form parasites are exponentially more capable of infecting tsetse flies. They further show that Slender cells do not infect mature flies.

However, they raise questions of immature tsetse immunological potential and field transmission potential that their experiments do not address. Specifically, they do not show that teneral tsetse flies are immunocompromised, that tsetse flies must be immunocompromised for Slender infection nor that younger teneral tsetse infection is not pertinent to field transmission.

Strengths:<br /> Experimental Design is precise and elegant, outcomes are convincing. Discussion is compelling and important to the field. This is a timely piece that adds important data to a critical discussion of host: parasite interactions, of relevance to all parasite transmission.

Weaknesses:<br /> As above, the authors dispute the biological relevance of teneral tsetse infection in the wild, without offering evidence to the contrary. Statements need to be softened for claims regarding immunological competence or relevance to field transmission.

Reviewer #1 (Public Review):

DeKraker et al. propose a new method for hippocampal registration using a novel surface-based approach that preserves the topology of the curvature of the hippocampus and boundaries of hippocampal subfields. The surface-based registration method proved to be more precise and resulted in better alignment compared to traditional volumetric-based registration. Moreover, the authors demonstrated that this method can be performed across image modalities by testing the method with seven different histological samples. This work has the potential to be a powerful new registration technique that can enable precise hippocampal registration and alignment across subjects, datasets, and image modalities.

Reviewer #1 (Public Review):

Summary:<br /> Van der Heijden et al perform an ambitious analysis of single-unit activity in the interposed nuclei of multiple mouse models of cerebellar dysfunction. Based on these recordings, they develop a classifier to predict the behavioral phenotype (ataxic, dystonic, or tremor) of each model, suggesting that highly regular spiking is associated with ataxia, irregular spiking is associated with dystonia and rhythmic spiking is associated with tremor. After developing this classifier, they show that activating Purkinje neurons in different patterns that evoke interposed nuclear activity similar to their "ataxic", "dystonic", and "tremor" firing patterns induce similar behaviors in healthy mice. These results show convincingly that specific patterns of cerebellar output are sufficient to cause specific movement abnormalities. The extent to which cerebellar nuclear firing patterns are solely responsible for phenotypes in human disease remains to be established, however.

Strengths:<br /> Major strengths are the recordings across multiple phenotypic models including genetic and pharmacologic manipulations, and the robust phenotypes elicited by Purkinje neuron stimulation.

Weaknesses:<br /> The number of units recorded was small for each model (on the order of 20), limiting the conclusions that can be drawn from the recording/classifier experiments.

Joint Public Review:

Summary<br /> This is a very meticulous and precise anatomical description of the external sensory organs (sensillia) in Drosophila larvae. Extending on their previous study (Rist and Thum 2017) that analyzed the anatomy of the terminal organ, a major external taste organ of fruit fly larva, the authors examined the anatomy of the remaining head sensory organs - the dorsal organ, the ventral organ, and the labial organ-also described the sensory organs of the thoracic and abdominal segments. Improved serial electron microscopy and digital modeling are used to the fullest to provide a definitive and clear picture of the sensory organs, the sensillia, and adjacent ganglia, providing an integral and accurate map, which is dearly needed in the field. The authors revise all the data for the abdominal and thoracic segments and describe in detail, for the first time, the head and tail segments and construct a complete structural and neuronal map of the external larval sensilla.

Strengths<br /> It is a very thorough anatomical description of the external sensory organs of the genetically amenable fruitfly. This study represents a very useful tool for the research community that will definitely use it as a reference paper. In addition to the classification and nomenclature of the different types of sensilla throughout the larval body, the wealth of data presented here will be valuable to the scientific community. It will allow for investigating sensory processing in depth. Serial electron microscopy and digital modeling are used to the fullest to provide a comprehensive, definitive, and clear picture of the sensory organs. The discussion places the anatomical data into a functional and developmental frame. The study offers fundamental anatomical insights, which will be helpful for future functional studies and to understand the sensory strategies of Drosophila larvae in response to the external environment. By analyzing different larval stages (L1 and L3), this work offers some insights into the developmental aspects of the larval sense organs and their corresponding sensory cells.

Weaknesses<br /> There are no apparent weaknesses, although it is not a complete novel anatomical study. It revisits many data that already existed, adding new information. However, the repetitiveness of some data and prior studies may be avoided for easy readability.

Reviewer #1 (Public Review):

Summary:<br /> The authors aimed to infer the trajectories of long range and local neuronal synchrony across the Alzheimer's disease continuum, relative to neurodegeneration and cognitive decline. The trajectories are inferred using event-based models, which infer a set of data-driven disease stages from a given dataset. The authors develop an adapted event-based modelling approach, in which they characterise each stage as a particular biomarker increasing by a particular z-score deviation from controls. Fitting infers the optimal set of z-scores to use for each biomarker and the order in which each biomarker reaches each z-score. The authors apply this approach to data from 148 individuals (70 cognitively unimpaired older adults and 78 individual with mild cognitive impairment or Alzheimer's disease), identifying trajectories in which long-range (amplitude-envolope correlation) and local (regional spectral power) neuronal synchrony in the alpha and beta bands becomes abnormal prior to neurodegeneration (measured as the volume of the parahippocampal gyrus) and cognitive decline (measured using the mini-mental state examination).

Strengths:<br /> - The main strength is that the authors assess two models. In the first they derive a staging system based only on the volume of the parahippocampal gyrus and mini-mental state examination score. They then investigate how neuronal synchrony metrics change compared to this staging system. In the second they derive a staging system that also includes an average (combined long-range and local) neuronal synchrony metric and investigate how long-range and local synchrony metrics change relative to this staging system. This is a strength as the first model provides confidence that there is not overfitting to the neuronal synchrony data, and the second provides more detailed insights into the dynamics of the early neuronal synchrony changes.<br /> - Another strength is that the authors automatically infer the optimal z-scores to choose, rather than having to pre-select them manually, as in previous approaches.

Weaknesses:<br /> - The dataset is small and no external validation is performed.<br /> - A high proportion of the data is from controls (nearly 50%) with no biomarker evidence of Alzheimer's disease, and so the changes may be driven by aging or other non-Alzheimer's effects.<br /> - Inferring the optimal z-scores is a strength, however as different sets of z-scores are allowed per biomarker, there is a concern that the changes reflected are mainly driven by the choice of z-score, rather than the markers themselves (e.g. if lower z-scores are selected for one marker than another, then changes in that marker will appear to be detected earlier, even if both markers change at the same time).<br /> - In equation 2 it is unclear why the gaussian is measured based on a sum over I. The more obvious choice would be to use a multivariate gaussian with no covariance, which would mean taking the product rather than the sum over I.<br /> - In the original event-based model, k is a hidden variable. Presumably that is also the case here, however the notation k=stage(j) makes it seem like each subject is assigned a stage during the sequence optimisation.<br /> - Typically for event-based modelling, positional variance diagrams are created from the markov chain monte carlo samples of the event sequence, enabling visualisation of the uncertainty in the sequence, but these are not included in the study.<br /> - Many of the figures in the manuscript (e.g. Figure 1E/G, Figure 2A/B, Figure 3A/B/E/F/I/J, Figure 4 A/B/E/F/I/J) are based on averages in both the x and the y axis. In the x dimension, individuals have a weighted contribution to the value on the y axis, depending on their stage probability. In the y dimension, the values are averages across those individuals, and the error bars represent the standard error rather than the standard deviation. Whilst the trajectories themselves are interesting, they may not be discriminative at the individual level and may be more heterogeneous than it appears.<br /> - The bootstrapped statistical analyses comparing metrics between the stages do not consider the variability in the sequence.

Reviewer #1 (Public Review):

In this manuscript, Lee et al. compared encoding of odor identity and value by calcium signaling from neurons in the ventral pallidum (VP) in comparison to D1 and D2 neurons in the olfactory tubercle (OT).

Strengths: They utilize a strong comparative approach, which allows the comparison of signals in two directly connected regions. First, they demonstrate that both D1 and D2 OT neurons project strongly to the VP, but not the VTA or other examined regions, in contrast to accumbal D1 neurons which project strongly to the VTA as well as the VP. They examine single unit calcium activity in a robust olfactory cue conditioning paradigm that allows them to differentiate encoding of olfactory identity versus value, by incorporating two different sucrose, neutral and air puff cues with different chemical characteristics. They then use multiple analytical approaches to demonstrate strong, low-dimensional encoding of cue value in the VP, and more robust, high-dimensional encoding of odor identity by both D1 and D2 OT neurons, though D1 OT neurons are still somewhat modulated by reward contingency/value. Finally, they utilize a modified conditioning paradigm that dissociates reward probability and lick vigor to demonstrate that VP encoding of cue value is not dependent on encoding of lick vigor during sucrose cues, and that separable populations of VP neurons encode cue value/sucrose probability and lick vigor.

Weaknesses: The conclusions of the data are mostly well supported by the analyses, but the statistical analysis is somewhat limited and needs to be clarified and extended.

1) The manuscript includes limited direct statistical comparison of the neural populations, and many of the comparisons between the subregions are descriptive, including descriptions of the percentage of neurons having specific response types, or differences in effect sizes or differing "levels" of significance. An additional direct comparison of data from each subpopulation would help to confirm whether the differences reported are statistically meaningful.

2) When hypothesis tests are conducted between the neural populations, it is not clear whether the authors have accounted for the random effect of the subject, or whether individual units were treated as fully independent. For instance, pairwise differences are reported in Figures 4I, 5G/I/L, and others, but the statistical methods are unclear. Assessment of the statistics is further limited by the lack of reporting of degrees of freedom.

Reviewer #1 (Public Review):

Summary:<br /> Ever-improving techniques allow the detailed capture of brain morphology and function to the point where individual brain anatomy becomes an important factor. This study investigated detailed sulcal morphology in the parieto-occipital junction. Using cutting-edge methods, it provides important insights into local anatomy, individual variability, and local brain function. The presented work advances the field and will stimulate future research into this important area.

Strengths:<br /> Detailed, very thorough methodology. Multiple raters mapped detailed sulci in a large cohort. The identified sulcal features and their functional and behavioural relevance are then studied using various complementary methods. The results provide compelling evidence for the importance of the described sulcal features and their proposed relationship to cortical brain function.

Weaknesses:<br /> A detailed description/depiction of the various sulcal patterns is missing. A possible relationship between sucal morphology and individual demographics might provide more insight into anatomical variability. The unique dataset offers to opportunity to provide insights into laterality effects that should be explored.

Reviewer #1 (Public Review):

Summary:<br /> The authors provide very compelling evidence that the lateral septum (LS) engages in theta cycle skipping.

Strengths:<br /> The data and analysis are highly compelling regarding the existence of cycle skipping.

Weaknesses:<br /> The manuscript falls short on describing the behavioral or physiological importance of the witnessed theta cycle skipping, and there is a lack of attention to detail with some of the findings and figures:

More/any description is needed in the article text to explain the switching task and the behavioral paradigm generally. This should be moved from only being in methods as it is essential for understanding the study.

An explanation is needed as to how a cell can be theta skipping if it is not theta rhythmic.

The most interesting result, in my opinion, is the last paragraph of the entire results section, where there is more switching in the alternation task, but the reader is kind of left hanging as to how this relates to other findings. How does this relate to differences in decoding of relative arms (the correct or incorrect arm) during those theta cycles or to the animal's actual choice? Similarly, how does it relate to the animal's actual choice? Is this phenomenon actually behaviorally or physiologically meaningful at all? Does it contribute at all to any sort of planning or decision-making?

The authors state that there is more cycle skipping in the alternation task than in the switching task, and that this switching occurs in the lead-up to the choice point. Then they say there is a higher peak at ~125 in the alternation task, which is consistent. However, in the final sentence, the authors note that "This result indicates that the representations of the goal arms alternate more strongly ahead of the choice point when animals performed a task in which either goal arm potentially leads to reward." Doesn't either arm potentially lead to a reward (but different amounts) in the switching task, not the alternation task? Yet switching is stronger in the alternation task, which is not constant and contradicts this last sentence.

Additionally, regarding the same sentence - "representations of the goal arms alternate more strongly ahead of the choice point when the animals performed a task in which either goal arm potentially leads to reward." - is this actually what is going on? Is there any reason at all to think this has anything to do with reward versus just a navigational choice?

Similarly, the authors mention several times that the LS links the HPC to 'reward' regions in the brain, and it has been found that the LS represents rewarded locations comparatively more than the hippocampus. How does this relate to their finding?