Reviewer #1 (Public Review):

Summary:<br /> This publication applies 3D super-resolution STORM imaging to understanding the role of developmental neural activity in the clustering of retinal inputs to the mouse dorsal lateral geniculate nucleus (dLGN). The authors argue that retinal ganglion cell (RGC) synaptic boutons start forming clusters early in postnatal development (P2). They then argue that these clusters contribute to eye-specific segregation of retinal inputs by activity-dependent stabilization of nearby boutons from the same eye. The data provided is N=3 animals for each condition of P2, P4, and P8 animals in wild-type mice and in mice where early patterns of structured retinal activity are blocked.

Strengths:<br /> The 3D storm imaging of pre and postsynaptic elements provides convincing high-resolution localization of synapses.

The experimental design of comparing ipsilateral and contralateral RGC axon boutons in a region of the dLGN that is known to become contralateral is elegant. The design makes it possible to relate fixed time point structural data to a known outcome of activity-dependent remodeling.

Weaknesses:<br /> Based on previous literature, it is known that synapse density, synapse clustering, and synaptic specificity increase during postnatal development. Previous work has also shown that both the changes in synaptic clustering and synaptic specificity are affected by retinal activity. The data and analysis provided by the authors add little unambiguous evidence that advances this understanding.

General problem 1: Most of the statistical analysis is limited to ANOVA comparison of axons from the contralateral and ipsilateral retina in the contralateral dLGN. The hypothesis that ipsilateral and contralateral axons would be statistically identical in the contralateral dLGN is not a plausible hypothesis so rejecting the hypothesis with P < X does not advance the authors' arguments beyond what was already known.

General problem 2: Most of the interpretation of data is qualitative. While error bars are provided, these error bars are not used to draw conclusions. Given the small sample size (N=3), there is a large degree of uncertainty regarding the magnitude of changes (synapse size, number, specificity). The authors base their conclusions on the averages of these values when the likely degree of uncertainty could allow for the opposite interpretation.

General problem 3: Two of the four results sections depend on using the frequency of single active zone vGlut2 clusters near multiple active zone vGlut2 as a proxy for synaptic stabilization of the single active zone vGlut2 clusters by the multiple active zone vGlut2 clusters. The authors argue that the increased frequency of same-eye single active zone clusters relative to opposite-eye single active zone clusters means that multiple active zone vGlut2 clusters are selectively stabilizing single active zone clusters. There are other plausible explanations for this observation that are not eliminated. An increased frequency of nearby single active zone clusters would also occur if RGC axons form more than one synapse in the dLGN. Eye-specific segregation is, by definition, a relative increase in the frequency of nearby boutons from the same eye. The authors were, therefore, guaranteed to observe a non-random relationship between boutons from the same eye. The authors do compare their measures to a random model, but I could not find a description of the model. I would expect that the model would need to account for RGC arbor size, arbor structure, bouton number, and segregation independent of multi-active-zone vGlut2 clusters. The most common randomization for the type of analysis described here, a shift in the positions of single-active zone boutons, would not be adequate.

In discussing the claimed cluster-induced stabilization of nearby boutons, the authors state that the specificity increases with age due to activity-dependent refinement. Their quantification does not support an increase in specificity with age. In fact, the high degree of clustering "specificity" they observe at P2 argues for the trivial same axon explanation.

Analysis of specific claims:

Result Section 1

Most of the figures show mean, error bars, and asterisks, but not the three data points from which these statistics are derived. Large changes in variance from condition to condition suggest that displaying the data points would provide more useful information.

Claim 1: Contralateral density increases more than ipsilateral in the contralateral region over the course of development. This claim is supported by the qualitative comparison of means and error bars in Figure 2D. The argument could be made quantitative by providing a confidence interval for synapse density increase for dominant and non-dominant synapse density. A confidence interval could then be generated for the difference in this change between the two groups. Currently, the most striking effect is a big difference in variance between P4 and P8 for dominant eye complex synapses. Given that N=3, I assume there is one extreme outlier here.

Claim 2: The fraction of multiple-active zone vGlut2 clusters increases with age. This claim is weakly supported by a qualitative reading of panel 1E. The error bars overlap so it is difficult to know what the range of possible increases could be. In the text, the authors report mean differences without confidence intervals (or any other statistics). The reported results should, therefore, be interpreted as a description of their three mice and not as evidence about mice in general.

Figure S1. Panel A makes the point that the study could not be done without STORM by comparing the STORM images to "Conventional" images. The images are over-saturated low-resolution images. A reasonable comparison would be to a high-quality quality confocal image acquired with a high NA objective (~1.4) and low laser power (PSF ~ 0.2 x 0.2 x 0.6 um) that was acquired over the same amount of time it takes to acquire a STORM volume.

Result section 2.

Claim 1: The ipsi/contra (in contra LGN) difference in VGluT2 cluster volume increases with development. While there are many p-values listed, the main point is not directly quantified. A reasonable way to quantify the relative increase in volume could be in the form: the non-dominant volumes were 75%-95%(?) of the dominant volume at P2 and 60%-80% (?) at P8. The difference in change was -5 to 15%(?).

Claim 2: Complex synapses (vGlut2 clusters with multiple active zones) represent clusters of simple synapses and not single large boutons with multiple active zones. The authors argue that because vGlut2 cluster volume scales roughly linearly with active zone number, the vGlut2 clusters are composed of multiple boutons each containing a single active zone. Their analysis does not rule out the (known to be true) possibility that RGC bouton sizes are much larger in boutons with multiple active zones. The correlation of volume and active zone number, by itself, does not resolve the issue. A good argument for multiple boutons might be that the variance is smallest in clusters with 4 active zones (looks like it in the plot) since they would be the average of four active zones to vesicle pool ratios. It is very likely that the multi-active zone vGlut2 clusters represent some clustering and some multi-synaptic boutons. The reference cited by the authors as evidence for the presence of single active zone boutons in young tissue does not rule out the existence of multiple active zone boutons.

Several arguments are made that depend on the interpretation of "not statistically significant" (n.s.) meaning that "two groups are the same" instead of "we don't know if they are different". This interpretation is incorrect and materially impacts the conclusions.

Several arguments are made that interpret statistical significance for one group and a lack of statistical significance for another group meaning that the effect was bigger in the first group. This interpretation is incorrect and materially impacts the conclusions.

Result Section 3.

Claim 1: Complex synapses stabilize simple synapses. There are alternative explanations (mentioned above) for the observed clustering that negate the conclusions. 1) Boutons from the same axon tend to be found near one another. 2) Any form of eye-specific segregation would produce non-random associations in the analysis as performed. The authors compare each observation to a random model, but I cannot determine from the text if the model adequately accounts for alternative explanations.

The authors claim that specificity increases over time. Figure 3b (middle) shows that the number of synapses near complex synapses might increase with time (needs confidence interval for effect size), but does not show that specificity (original relative to randomized) increases with time. The fact that nearby simple synapse density is always (P2) very different from random suggests a primarily non-activity-dependent explanation. The simplest explanation is that same-side boutons could be from the same axon whereas different-side axons could not be.

Claim 2: vGlut2 clusters more than 1.5 um away from multi-active zone vGlut2 clusters are not statistically significantly different in size than vGlut2 clusters within 1.5 um of multi-active zone vGlut2 clusters. Therefore "activity-dependent synapse stabilization mechanisms do not impact simple synapse vesicle pool size". The specific measure of 1.5 um from multi-active zone vGlut2 clusters does not represent all possible synapse stabilization mechanisms.

Result Section 4.

Claim: The proximity of complex synapses with nearby simple synapses to other complex synapses with nearby simple synapses from the same eye is used to argue that activity is responsible for all this clustering.

It is difficult to derive anything from the quantification besides 'not-random'. That is a problem because we already know that axons from the left and right eye segregate during the period being studied. All the measures in Section 4 are influenced by eye-specific segregation. Given this known bias, demonstrating a non-random relationship (P<br /> The results can be stated as: If you are a contralateral complex synapse, contralateral complex synapses that are also close to contralateral simple synapses will, on average, be slightly closer to you than contralateral complex synapses that are not close to contralateral ipsilateral synapses. That would be true if there is any eye-specific segregation (which there is).

It is an overinterpretation of the data to claim that the lack of a clear correlation between vGlut2 cluster volume and distance to vGlut2 clusters with multiple active zones provides support for the claim that "presynaptic protein organization is not influenced by mechanisms governing synaptic clustering".

Reviewer #2 (Public Review):

Summary:<br /> In this manuscript, Zhang and Speer examine changes in the spatial organization of synaptic proteins during eye-specific segregation, a developmental period when axons from the two eyes initially mingle and gradually segregate into eye-specific regions of the dorsal lateral geniculate. The authors use STORM microscopy and immunostain presynaptic (VGluT2, Bassoon) and postsynaptic (Homer) proteins to identify synaptic release sites. Activity-dependent changes in this spatial organization are identified by comparing the β2KO mice to WT mice. They describe two types of presynaptic organization based on Bassoon clustering, the complex and the simple synapse. By analyzing the relative densities and distances between these proteins over age, the authors conclude that the complex synapses promote the clustering of simple synapses nearby to form the future mature glomerular synaptic structure.

Strengths:<br /> The data presented is of good quality and provides an unprecedented view at high resolution of the presynaptic components of the retinogeniculate synapse during active developmental remodeling. This approach offers an advance to the previous mouse EM studies of this synapse because of the CTB label allows identification of the eye from which the presynaptic terminal arises. Using this approach, the authors find that simple synapses cluster close to complex synapses over age, that complex synapse density increases with age.

Weaknesses:<br /> From these data, the authors conclude that the complex synapse serves to "promote clustering of like-eye synapses and prohibit synapse clustering from the opposite eye". However, the authors show no causal data to support these ideas. There are a number of issues that the authors should consider:

1. Clustering of retinal synapses is in part due to the fact that retinal inputs synapse on the proximal dendrites. With increased synaptogenesis, there will be increased density of retinal terminals that are closely localized. And with development, perhaps simple synapses mature into complex synapses. Simple synapses may also represent ones that are in the process of being eliminated as previously described by Campbell and Shatz, JNeurosci 1992 (consider citing). Can the authors distinguish these scenarios from the ones that they conclude?

2. The argument that "complex" synapses are the aggregate of "simple" synapses (Fig 2, S2) is not convincing.

3. The authors use of the β2KO mice to assess changes in the organization of synaptic proteins in retinal terminals that have disrupted retinal waves. However, β2-nAChRs are also expressed in the dLGN and other areas of the brain and glutamatergic synapse development has been reported in the CNS independent of the disruption in retinal waves. This issue should be considered when interpreting the total reduced retinal synapse density in the dLGN of the mutant.

4. Outside of a total synapse density difference between WT and β2KO mice, the changes in the spatial organization of synaptic proteins over development do not seem that different. In fact % simple synapses near complex synapses from the non-dominant eye in the mutant is not that different from WT at P8 (Fig 3C), an age when eye-specific segregation is very different between the genotypes. Can the authors explain this discrepancy?

5. The authors use nomenclature that has been previously used and associated with other aspects of retinogeniculate properties. For example, the phrases "simple" and "complex" synapses have been used to describe single boutons or aggregates of boutons from numerous retinal axons, whereas in this manuscript the phrases are used to describe vesicle clusters/release sites with no knowledge of whether they are from single or multiple boutons. Likewise, the use of the word "glomerulus" has been used in the context of the retinogeniculate synapse to refer to a specific pattern of bouton aggregates that involves inhibitory and neuromodulatory inputs. It is not clear how the release sites described by the authors fit in this picture. Finally the use of the word "punishment" is associated with a body of literature regarding the immune system and retinogeniculate refinement-which is not addressed in this study. This double use of the phrases can lead to confusion in the field and should be clarified by clear definitions of how they are used in the current study.

Reviewer #3 (Public Review):

Summary:<br /> This manuscript is a follow-up to a recent study of synaptic development based on a powerful data set that combines anterograde labeling, immunofluorescence labeling of synaptic proteins, and STORM imaging (Cell Reports 2023). Specifically, they use anti-Vglut2 label to determine the size of the presynaptic structure (which they describe as the vesicle pool size), anti-Bassoon to label a number of active zones, and anti-Homer to identify postsynaptic densities. In their previous study, they compared the detailed synaptic structure across the development of synapses made with contra-projecting vs ipsi-projecting RGCs and compared this developmental profile with a mouse model with reduced retinal waves. In this study, they produce a new analysis on the same data set in which they classify synapses into "complex" vs. "simple" and assess the number and spacing of these synapses. From these measurements, they make conclusions regarding the processes that lead to synapse competition/stabilization.

Strengths:<br /> This is a fantastic data set for describing the structural details of synapse development in a part of the brain undergoing activity-dependent synaptic rearrangements. The fact that they can differentiate eye of origin is also a plus.

Weaknesses:<br /> The lack of details provided for the classification scheme as well as the interpretation of small effect sizes limit the interpretations that can be made based on these findings.

1. The criteria to classify synapses as simple vs. complex is critical for all of the analysis in this study. Therefore this criteria for classification should be much more explicit and tested for robustness. As stated in the methods, it is based on the number of active zones which are designated by the number of Bassoon clusters associated with a Vglut2 cluster (line 697). A second part of the criteria is the size of the presynaptic terminal as assayed by "greater Vglut2 signal" (line 116). So how are these thresholds determined? For Bassoon clusters, is one voxel sufficient? Two? If it's one, how often do they see a Bassoon positive voxel with no Vglut2 cluster and therefore may represent "noise"? There is no distribution of Bassoon volumes that is provided that might be the basis for selecting this number of sites. Unfortunately, the images are not helpful. For example, does P8 WT in Figure 1B have 7 or 2? According to Figure 2C, it appears the numbers are closer to 2-4.

The Vglut volume measurements also do not seem to provide a clear criterion. Figure 2 shows that the distributions of Vglut2 cluster volumes for complex and for simple synapses are significantly overlapping.

The authors need to clarify the quantitative approach used for this classification strategy and test how sensitive the results of the study are to how robust this strategy is

2. Effect sizes are quite small and all comparisons are made on medians of distributions. This leads to an n=3 biological replicates for all comparisons. Hence this small n may lead to significant results based on ANOVAS/t-tests, but the statistical power of these effects is quite weak. To accurately represent the variance in their data, the authors should show all three data points for each category (with a SD error bar when possible). They should also include the number of synapses in each category (e.g. the numerators in Figure 1D and the denominators for Figure 1E). For other figures, there are additional statistical questions described below.

3. The authors need to add a caveat regarding their classification of synapses as "complex" vs. "simple" since this is a terminology that already exists in the field and it is not clear that these STORM images are measuring the same thing. For example, in EM studies, "complex" refers to multiple RGCs converging on the same single postsynaptic site. The authors here acknowledge that they cannot assign different AZs to different RGCs so this comparison is an assumption. In Figure 2 they argue this is a good assumption based on the finding that the Vglut column/active zone is constant and therefore each represents a single RGC. However, the authors should acknowledge that they are actually seeing quite different percentages than those in EM studies. For example, in Monavarfeshani et al, eLife 2018, there were no complex synapses found at P8. (Note this study also found many more complex vs. simple synapses in the adult - 70% vs. the 20% found in the current study - but this difference could be a developmental effect). In the future, the authors may want to take another data set in the adult dLGN to make a direct comparison based on numbers and see if their classification method for complex/simple maps onto the one that currently exists in the literature.

4. Figure 3 assays the relative distribution of simple vs. complex synapses. They found that a larger percentage of simple synapses were within 1.5 microns of complex synapses than you would expect by chance for both ipsi and contra projecting RGCs, and hence conclude that complex synapses are sites of synaptic clustering. In contrast, there was no clustering of ipsi-simple to contra-complex synapses and vice versa. The authors also argue that this clustering decreases between P4 and P8 for ipsi projecting RGCs.

This analysis needs much more rigor before any conclusions can be drawn. First, the authors need to justify the 1.5-micron criteria for clustering and how robust their results are to variations in this distance. Second, these age effects need to be tested for statistical significance with an ANOVA (all the stats presented are pairwise comparisons to means expected by random distributions at each age). Finally, the authors should consider what n's to use here - is it still grouped by biological replicate? Why not use individual synapses across mice? If they do biological replicates, then they should again show error bars for each data point in their biological replicates. And they should include the number of synapses that went into these measurements in the caption.

5. Line 211-212 - the authors conclude that the absence of clustered ipsi-simple synapses indicates a failure to stabilize (Figure 3). Yet, the link between this measurement and synapse stabilization is not clear. In particular, the conclusion that "isolated" synapses are the ones that will be eliminated seems to be countered by their finding in Figure 3D/E which shows that there is no difference in vesicle pool volume between near and far synapses. If isolated synapses are indeed the ones that fail to stabilize by P8, wouldn't you expect them to be weaker/have fewer vesicles? Also, it's hard to tell if there is an age-dependent effect since the data presented in Figures 3D/E are merged across ages.

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 #2 (Public Review):

Summary:<br /> This manuscript examines how humans walk over uneven terrain using vision to decide where to step. There is a huge lack of evidence about this because the vast majority of locomotion studies have focused on steady, well-controlled conditions, and not on decisions made in the real world. The author team has already made great advances in this topic, but there has been no practical way to map 3D terrain features in naturalistic environments. They have now developed a way to integrate such measurements along with gaze and step tracking, which allows quantitative evaluation of the proposed trade-offs between stepping vertically onto vs. stepping around obstacles, along with how far people look to decide where to step.

Strengths:<br /> 1. I am impressed by the overarching outlook of the researchers. They seek to understand human decision-making in real-world locomotion tasks, a topic of obvious relevance to the human condition but not often examined in research. The field has been biased toward well-controlled studies, which have scientific advantages but also serious limitations. A well-controlled study may eliminate human decisions and favor steady or periodic motions in laboratory conditions that facilitate reliable and repeatable data collection. The present study discards all of these usually-favorable factors for rather uncontrolled conditions, yet still finds a way to explore real-world behaviors in a quantitative manner. It is an ambitious and forward-thinking approach, used to tackle an ecologically relevant question.

2. There are serious technical challenges to a study of this kind. It is true that there are existing solutions for motion tracking, eye tracking, and most recently, 3D terrain mapping. However most of the solutions do not have turn-key simplicity and require significant technical expertise. To integrate multiple such solutions together is even more challenging. The authors are to be commended on the technical integration here.

3. In the absence of prior studies on this issue, it was necessary to invent new analysis methods to go with the new experimental measures. This is non-trivial and places an added burden on the authors to communicate the new methods. It's harder to be at the forefront in the choice of topic, technical experimental techniques, and analysis methods all at once.

Weaknesses:<br /> 1. I am predisposed to agree with all of the major conclusions, which seem reasonable and likely to be correct. Ignoring that bias, I was confused by much of the analysis. There is an argument that the chosen paths were not random, based on a comparison of probability distributions that I could not understand. There are plots described as "turn probability vs. X" where the axes are unlabeled and the data range above 1. I hope the authors can provide a clearer description to support the findings. This manuscript stands to be cited well as THE evidence for looking ahead to plan steps, but that is only meaningful if others can understand (and ultimately replicate) the evidence.

2. I wish a bit more and simpler data could be provided. It is great that step parameter distributions are shown, but I am left wondering how this compares to level walking. The distributions also seem to use absolute values for slope and direction, for understandable reasons, but that also probably skews the actual distribution. Presumably, there should be (and is) a peak at zero slope and zero direction, but absolute values mean that non-zero steps may appear approximately doubled in frequency, compared to separate positive and negative. I would hope to see actual distributions, which moreover are likely not independent and probably have a covariance structure. The covariance might help with the argument that steps are not random, and might even be an easy way to suggest the trade-off between turning and stepping vertically. This is not to disregard the present use of absolute values but to suggest some basic summary of the data before taking that step.

3. Along these same lines, the manuscript could do more to enable others to digest and go further with the approach, and to facilitate interpretability of results. I like the use of a neural network to demonstrate the predictiveness of stepping, but aside from above-chance probability, what else can inform us about what visual data drives that? Similarly, the step distributions and height-turn trade-off curves are somewhat opaque and do not make it easy to envision further efforts by others, for example, people who want to model locomotion. For that, clearer (and perhaps) simpler measures would be helpful.

I am absolutely in support of this manuscript and expect it to have a high impact. I do feel that it could benefit from clarification of the analysis and how it supports the conclusions.

Reviewer #3 (Public Review):

Summary:<br /> The systematic way in which path selection is parametrically investigated is the main contribution.

Strengths:<br /> The authors have developed an impressive workflow to study gait and gaze in natural terrain.

Weaknesses:<br /> 1. The training and validation data of the CNN are not explained fully making it unclear if the data tells us anything about the visual features used to guide steering.

It is not clear how or on what data the network was trained (training vs. validation vs. un-peeked test data), and justification of the choices made. There is no discussion of possible overfitting. The network could be learning just e.g. specific rock arrangements. If the network is overfitting the "features" it uses could be very artefactual, pixel-level patterns and not the kinds of "features" the human reader immediately has in mind.

2. The use of descriptive terminology should be made systematic.

Specifically, the following terms are used without giving a single, clear definition for them: path, step, step location, foot plant, foothold, future foothold, foot location, future foot location, foot position.

I think some terms are being used interchangeably. I would really highly recommend a diagrammatic cartoon sketch, showing the definitions of all these terms in a single figure, and then sticking to them in the main text.

3. More coverage of different interpretations / less interpretation in the abstract/introduction would be prudent

The authors discuss the path selection very much on the basis of energetic costs and gait stability. At least mention should be given to other plausible parameters the participants might be optimizing (or that indeed they may be just satisficing).

That is, it is taken as "given" that energetic cost is the major driver of path selection in your task, and that the relevant perception relies on internal models. Neither of these is a priori obvious nor is it as far as I can tell shown by the data (optimizing other variables, satisficing behavior, or online "direct perception" cannot be ruled out).

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 #2 (Public Review):

Summary:<br /> Seignette et al. investigated the potential roles of axo-axonic (chandelier) cells (ChCs) in a sensory system, namely visual processing. As introduced by the authors, the axo-axonic cell type has remained (and still is) somehow mysterious in its function. Seignette and colleagues leveraged the development of a transgenic mouse line selective for ChC, and applied a very wide range of techniques: transsynaptic rabies tracing, optogenetic input activation, in vitro electrophysiology, 2-photon recording in vivo, behavior and chemogenetic manipulations, to precisely determine the contribution of ChCs to the primary visual cortex network.

The main findings are 1) the identification of synaptic inputs to ChC, with a majority of local, deep layer principal neurons (PN), 2) the demonstration that ChC is strongly and synchronously activated by visual stimuli with low specificity in naive animals, 3) the recruitment of ChC by arousal/visuomotor mismatch, 4) the induction of functional and structural plasticity at the ChC-PN module, and, 5) the weak disinhibition of PNs induced by ChCs silencing. All these findings are strongly supported by experimental data and thoroughly compared to available evidence.

Strengths:<br /> This article reports an impressive range of very demanding experiments, which were well executed and analyzed, and are presented in a very clear and balanced manner. Moreover, the manuscript is well-written throughout, making it appealing to future readers. It has also been a pleasure to review this article.

In sum, this is an impressive study and an excellent manuscript, that presents no major flaws.

Notably, this study is one of the first studies to report on the activities and potential roles of axo-axonic cells in an active, integrated brain process, beyond locomotion as reported and published in V1. This type of research was much awaited in the fields of interneuron and vision research.

Weaknesses:<br /> There are no fundamental weaknesses; the latter mainly concern the presentation of the main results.

The main weakness may be that the different sections appear somehow disconnected conceptually.

Additionally, some parts deserve a more in-depth clarification/simplification of concepts and analytic methods for scientists outside the subfield of V1 research. Indeed, this paper will be of key interest to researchers of various backgrounds.

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 #2 (Public Review):

Summary:<br /> The work by Klaassen & Rasch investigates the influence of word learning difficulty on sleep-associated consolidation and reactivation. They elicited reactivation during sleep by applying targeted memory reactivation (TMR) and manipulated word learning difficulty by creating words more similar (easy) or more dissimilar (difficult) to our language. In one group of participants, they applied TMR of easy words and in another group of participants, they applied TMR of difficult words (between-subjects design). They showed that TMR leads to higher memory benefits in the easy compared to the difficult word group. On a neural level, they showed an increase in spindle power (in the up-state of an evoked response) when easy words were presented during sleep.

Strengths:<br /> The authors investigate a research question relevant to the field, that is, which experiences are actually consolidated during sleep. To address this question, they developed an innovative task and manipulated difficulty in an elegant way.

Overall, the paper is clearly structured, and results and methods are described in an understandable way. The analysis approach is solid.

Weaknesses:<br /> 1.Sample size<br /> For a between-subjects design, the sample size is too small (N = 22). The main finding (also found in the title "Difficulty in artificial word learning impacts targeted memory reactivation") is based on an independent samples t-test with 11 participants/group.

The authors explicitly mention the small sample size and the between-subjects design as a limitation in their discussion. Nevertheless, making meaningful inferences based on studies with such a small sample size is difficult, if not impossible.

2.Choice of task<br /> Even though the task itself is innovative, there would have been tasks better suited to address the research question. The main disadvantage the task and the operationalisation of memory performance (d') have is that single-trial performance cannot be calculated. Consequently, choosing individual items for TMR is not possible.

Additionally, TMR of low vs. high difficulty is conducted between subjects (and independently of pre-sleep memory performance) which is a consequence of the task design.

The motivation for why this task has been used is missing in the paper.

Reviewer #3 (Public Review):

Summary:<br /> In this study, the authors investigated the effects of targeted memory reactivation (TMR) during sleep on memory retention for artificial words with varying levels of phonotactical similarity to real words. The authors report that the high phonotactic probability (PP) words showed a more pronounced EEG alpha decrease during encoding and were more easily learned than the low PP words. Following TMR during sleep, participants who had been cued with the high PP TMR, remembered those words better than 0, whilst no such difference was found in the other conditions. Accordingly, the authors report higher EEG spindle band power during slow-wave up-states for the high PP as compared to low PP TMR trials. Overall, the authors conclude that artificial words that are easier to learn, benefit more from TMR than those which are difficult to learn.

Strengths:<br /> 1. The authors have carefully designed the artificial stimuli to investigate the effectiveness of TMR on words that are easy to learn and difficult to learn due to their levels of similarity with prior word-sound knowledge. Their approach of varying the level of phonotactic probability enables them to have better control over phonotactical familiarity than in a natural language and are thus able to disentangle which properties of word learning contribute to TMR success.

2. The use of EEG during wakeful encoding and sleep TMR sheds new light on the neural correlates of high PP vs. low PP both during wakeful encoding and cue-induced retrieval during sleep.

Weaknesses:<br /> 1. The present analyses are based on a small sample and comparisons between participants. Considering that the TMR benefits are based on changes in memory categorization between participants, it could be argued that the individuals in the high PP group were more susceptible to TMR than those in the low PP group for reasons other than the phonotactic probabilities of the stimuli (e.g., these individuals might be more attentive to sounds in the environment during sleep). While the authors acknowledge the small sample size and between-subjects comparison as a limitation, a discussion of an alternative interpretation of the data is missing.

2. While the one-tailed comparison between the high PP condition and 0 is significant, the ANOVA comparing the four conditions (between subjects: cued/non-cued, within-subjects: high/low PP) does not show a significant effect. With a non-significant interaction, I would consider it statistically inappropriate to conduct post-hoc tests comparing the conditions against each other. Furthermore, it is unclear whether the p-values reported for the t-tests have been corrected for multiple comparisons. Thus, these findings should be interpreted with caution.

3. With the assumption that the artificial words in the study have different levels of phonotactic similarity to prior word-sound knowledge, it was surprising to find that the phonotactic probabilities were calculated based on an American English lexicon whilst the participants were German speakers. While it may be the case that the between-language lexicons overlap, it would be reassuring to see some evidence of this, as the level of phonotactic probability is a key manipulation in the study.

4. Another manipulation in the study is that participants learn whether the words are linked to a monetary reward or not, however, the rationale for this manipulation is unclear. For instance, it is unclear whether the authors expect the reward to interact with the TMR effects.

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 #3 (Public Review):

The present study presents a comprehensive exploration of the distinct impacts of Isoflurane and Ketamine on c-Fos expression throughout the brain. To understand the varying responses across individual brain regions to each anesthetic, the researchers employ principal component analysis (PCA) and c-Fos-based functional network analysis. The methodology employed in this research is both methodical and expansive. Notably, the utilization of a custom software package to align and analyze brain images for c-Fos positive cells stands out as an impressive addition to their approach. This innovative technique enables effective quantification of neural activity and enhances our understanding of how anesthetic drugs influence brain networks as a whole.

The primary novelty of this paper lies in the comparative analysis of two anesthetics, Ketamine and Isoflurane, and their respective impacts on brain-wide c-Fos expression. The study reveals the distinct pathways through which these anesthetics induce loss of consciousness. Ketamine primarily influences the cerebral cortex, while Isoflurane targets subcortical brain regions. This finding highlights the differing mechanisms of action employed by these two anesthetics-a top-down approach for Ketamine and a bottom-up mechanism for Isoflurane. Furthermore, this study uncovers commonly activated brain regions under both anesthetics, advancing our knowledge about the mechanisms underlying general anesthesia.

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 #2 (Public Review):

Summary:<br /> The authors describe the structure-functional relationship of domains in S. pombe CAF-1, which promotes DNA replication-coupled deposition of histone H3-H4 dimer. The authors nicely showed that the ED domain with an intrinsically disordered structure binds to histone H3-H4, that the KER domain binds to DNA, and that, in addition to a PIP box, the KER domain also contributes to the PCNA binding. The ED and KER domains as well as the WHD domain are essential for nucleosome assembly in vitro. The ED, KER domains, and the PIP box are important for the maintenance of heterochromatin.

Strengths:<br /> The combination of structural analysis using NMR and Alphafold2 modeling with biophysical and biochemical analysis provided strong evidence on the role of the different domain structures of the large subunit of SpCAF-1, spPCF-1 in the binding to histone H3-H4, DNA as well as PCNA. The conclusion was further supported by genetic analysis of the various pcf1 mutants. The large amounts of data provided in the paper support the authors' conclusion very well.

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 #2 (Public Review):

The manuscript deals with an interesting topic in metabolism: the so-called underground metabolism enabled by enzymes with broad substrate specificity. This is mainly relevant in secondary metabolisms. The authors deal, in particular, with the conversion of flavonoids, which have health-promoting effects. They present an algorithm for predicting the moonlight activities of enzymes, which must be given as inputs. Moreover, the authors performed experiments on the antioxidant activities of the flavonoids under study.

My focus was on the bioinformatics part. Overall, the bioinformatics part is not a major scientific achievement in my eyes, or it is too poorly described to see its merits. There may be difficulties understanding the presented algorithm.

Comments:

The prediction algorithm should be explained much better. Although the manuscript is quite long, it does not describe the approaches sufficiently well. It is quite hard to read.

As far as I can see, the method was only tested with a small sample of different flavonoid substances.

Major comments<br /> (1) I see the following contradiction. Line 18/19: "As flavonoids are not natural substrates of gut bacterial enzymes" and lines 76/77: "commensal gut microorganisms do not have specialized enzymes that utilize flavonoids as their native substrates" versus lines 72-74: "flavonoids ..., which makes them available to be metabolized". How can they be metabolized given what is said in the first two phrases?<br /> (2) It should be explained better what is meant by "reaction class" (e.g. in lines 97 and 99). Is this the same as the EC number (in the Enzyme Catalogue)? The term "reaction class" is indeed used in the KEGG database. On the webpage<br /> https://www.genome.jp/brite/br08204<br /> it seems indeed as if the terms "reaction class" and EC number are somehow equivalent. However, the term "RClass RC00392" in line 557 of the manuscript points to a difference in meaning.<br /> (3) The prediction algorithm should be explained much better. For example, in the Figure showing the workflow, it is shown that an EC number should be given as input. However, if we search for enzymes which could potentially degrade a given flavonoid, we may not know any suitable EC number. Line 122: "To match a given enzyme with its non-native polyphenolic substrates..." However, where can we take the enzyme name/EC number from? Moreover, given that it is assumed that the reaction is performed by underground metabolism, should the enzyme given as input come from another organism, for example, a plant?<br /> (4) Lines 521-523: Our prediction tool can take either a single enzyme in the form of Enzyme Commission (EC) number (e.g. "ec:2.1.1.75"), or a KEGG organism-identifier (e.g. "cpv") or a consortium, a list of different organism-identifiers, as input." I do not understand the wording "or a consortium". According to the Figure showing the workflow, it should read "and a consortium".<br /> (5) In the Materials and Methods section, the KEGG PATHWAY database is mentioned. This comes somewhat out of the blue. What is the connection to the "reaction class" concept in KEGG? Or is the PATHWAY database only used for extracting the negative controls?<br /> (6) Line 142,143. "Our analysis shows that RClass-based similarity can predict the correct reactions for known flavonoid-metabolizing enzymes". How do the authors know that the results are correct? If it is easy to check, then I assume the test whether a given enzyme is able to catalyze reactions with flavonoids can be done manually in KEGG, so that a computer algorithm is unnecessary.<br /> (7) Elaborating on the previous point - I have the impression that the algorithm is a rather simple search routine for finding reactions in the KEGG database that match certain criteria. This might be a helpful tool to save time in comparison to doing the search manually. However, at least the bioinformatics part of the paper is not a major scientific achievement as far as I can see.<br /> (8) It is not sufficiently clear whether the prediction algorithm only works for the example shown in the top figure (tilianin, acacetin etc), which would be quite a restricted application, or for many or even all flavonoids. In line 565, the authors say: "our tabulated 312 unique flavonoids", while in the upper part of the MS, e.g. in lines 26 and 109, only the pathway starting from tilianin is mentioned.<br /> (9) In which programming language was the algorithm implemented?<br /> (10) The connection between the theoretical and experimental parts of the paper is not fully clear. Some of the experiments serve to test the predictions, which is fine. The experiments on free radicals, however, seem to be somewhat unrelated.

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 #2 (Public Review):

Summary:<br /> The study is titled "Leading an urban invasion: risk-sensitive learning is a winning strategy", and consists of three different parts. First, the authors analyse data on initial and reversal learning in Grackles confronted with a foraging task, derived from three populations labeled as "core", "middle" and "edge" in relation to the invasion front. The suggested difference between study populations does not surface, but the authors do find moderate support for a difference between male and female individuals. Secondly, the authors confirm that the proposed mechanism can actually generate patterns such as those observed in the Grackle data. In the third part, the authors present an evolutionary model, in which they show that learning strategies as observed in male Grackles do evolve in what they regard as conditions present in urban environments.

Strengths:<br /> The manuscript's strength is that it combines real learning data collected across different populations of the Great-tailed grackle (Quiscalus mexicanus) with theoretical approaches to better understand the processes with which grackles learn and how such learning processes might be advantageous during range expansion. Furthermore, the authors also take sex into account revealing that males, the dispersing sex, show moderately better reversal learning through higher reward-payoff sensitivity. I also find it refreshing to see that the authors took the time to preregister their study to improve transparency, especially regarding data analysis.

Weaknesses:<br /> One major weakness of this manuscript is the fact that the authors are working with quite low sample sizes when we look at the different populations of edge (11 males & 8 females), middle (4 males & 4 females), and core (17 males & 5 females) expansion range. Although I think that when all populations are pooled together, the sample size is sufficient to answer the questions regarding sex differences in learning performance and which learning processes might be used by grackles but insufficient when taking the different populations into account.

Another weakness of this manuscript is that it does not set up the background well in the introduction. Firstly, are grackles urban dwellers in their natural range and expand by colonising urban habitats because they are adapted to it? The introduction also fails to mention why urban habitats are special and why we expect them to be more challenging for animals to inhabit. If we consider that one of their main questions is related to how learning processes might help individuals deal with a challenging urban habitat, then this should be properly introduced.

Also, the authors provide a single example of how learning can differ between populations from more urban and more natural habitats. The authors also label the urban dwellers as the invaders, which might be the case for grackles but is not necessarily true for other species, such as the Indian rock agama in the example which are native to the area of study. Also, the authors need to be aware that only male lizards were tested in this study. I suggest being a bit more clear about what has been found across different studies looking at: (1) differences across individuals from invasive and native populations of invasive species and (2) differences across individuals from natural and urban populations.

Finally, the introduction is very much written with regard to the interaction between learning and dispersal, i.e. the 'invasion front' theme. The authors lay out four predictions, the most important of which is No. 4: "Such sex-mediated differences in learning to be more pronounced in grackles living at the edge, rather than the intermediate and/or core region of their range." The authors, however, never return to this prediction, at least not in a transparent way that clearly pronounces this pattern not being found. The model looking at the evolution of risk-sensitive learning in urban environments is based on the assumption that urban and natural environments "differ along two key ecological axes: environmental stability 𝑢 (How often does optimal behaviour change?) and environmental stochasticity 𝑠 (How often does optimal behaviour fail to pay off?). Urban environments are generally characterised as both stable (lower 𝑢) and stochastic (higher 𝑠)". Even though it is generally assumed that urban environments differ from natural environments the authors' assumption is just one way of looking at the differences which have generally not been confirmed and are highly debated. Additionally, it is not clear how this result relates to the rest of the paper: The three populations are distinguished according to their relation to the invasion front, not with respect to a gradient of urbanization, and further do not show a meaningful difference in learning behaviour possibly due to low sample sizes as mentioned above.

In conclusion, the manuscript was well written and for the most part easy to follow. The format of having the results before the methods makes it a bit harder to follow because the reader is not fully aware of the methods at the time the results are presented. It would, therefore, be important to more clearly delineate the different parts and purposes. Is this article about the interaction between urban invasion, dispersal, and learning? Or about the correct identification of learning mechanisms? Or about how learning mechanisms evolve in urban and natural environments? Maybe this article can harbor all three, but the borders need to be clear. The authors need to be transparent about what has and especially what has not been found, and be careful to not overstate their case.

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 #2 (Public Review):

In their manuscript, Kato et al investigate a key aspect of membrane protein quality control in plant photosynthesis. They study the turnover of plant photosystem II (PSII), a hetero-oligomeric membrane protein complex that undertakes the crucial light-driven water oxidation reaction in photosynthesis. The formidable water oxidation reaction makes PSII prone to photooxidative damage. PSII repair cycle is a protein repair pathway that replaces the photodamaged reaction center protein D1 with a new copy. The manuscript addresses an important question in PSII repair cycle - how is the damaged D1 protein recognized and selectively degraded by the membrane-bound ATP-dependent zinc metalloprotease FtsH in a processive manner? The authors show that oxidative post-translational modification (OPTM) of the D1 N-terminus is likely critical for the proper recognition and degradation of the damaged D1 by FtsH. Authors use a wide range of approaches and techniques to test their hypothesis that the singlet oxygen (1O2)-mediated oxidation of tryptophan 14 (W14) residue of D1 to N-formylkynurenine (NFK) facilitates the selective degradation of damaged D1. Overall, the authors propose an interesting new hypothesis for D1 degradation and their hypothesis is supported by most of the experimental data provided. The study certainly addresses an elusive aspect of PSII turnover and the data provided go some way in explaining the light-induced D1 turnover. However, some of the data are correlative and do not provide mechanistic insight. A rigorous demonstration of OPTM as a marker for D1 degradation is yet to be made in my opinion. Some strengths and weaknesses of the study are summarized below:

Strengths:

1. In support of their hypothesis, the authors find that FtsH mutants of Arabidopsis have increased OPTM, especially the formation of NFK at multiple Trp residues of D1 including the W14; a site-directed mutation of W14 to phenylalanine (W14F), mimicking NFK, results in accelerated D1 degradation in Chlamydomonas; accelerated D1 degradation of W14F mutant is mitigated in an ftsH1 mutant background of Chlamydomonas; and that the W14F mutation augmented the interaction between FtsH and the D1 substrate.

2. Authors raise an intriguing possibility that the OPTM disrupts the hydrogen bonding between W14 residue of D1 and the serine 25 (S25) of PsbI. According to the authors, this leads to an increased fluctuation of the D1 N-terminal tail, and as a consequence, recognition and binding of the photodamaged D1 by the protease. This is an interesting hypothesis and the authors provide some molecular dynamics simulation data in support of this. If this hypothesis is further supported, it represents a significant advancement.

3. The interdisciplinary experimental approach is certainly a strength of the study. The authors have successfully combined mass spectrometric analysis with several biochemical assays and molecular dynamics simulation. These, together with the generation of transplastomic algal cell lines, have enabled a clear test of the role of Trp oxidation in selective D1 degradation.

4. Trp oxidative modification as a degradation signal has precedent in chloroplasts. The authors cite the case of 1O2 sensor protein EXECUTER 1 (EX1), whose degradation by FtsH2, the same protease that degrades D1, requires prior oxidation of a Trp residue. The earlier observation of an attenuated degradation of a truncated D1 protein lacking the N-terminal tail is also consistent with authors' suggestion of the importance of the D1 N-terminus recognition by FtsH. It is also noteworthy that in light of the current study, D1 phosphorylation is unlikely to be a marker for degradation as posited by earlier studies.

Weaknesses:

1. The study lacks some data that would have made the conclusions more rigorous and convincing. It is unclear why the level of Trp oxidation was not analyzed in the Chlamydomonas ftsH 1-1 mutant as done for the var 2 mutant. Increased oxidation of W14 OPTM in Chlamydomonas ftsH 1-1 is a key prediction of the hypothesis. It is also unclear to me what is the rationale for showing D1-FtsH interaction data only for the double mutant but not for the single mutant (W14F). Why is the FtsH pulldown of D2 not statistically significant (p value = {less than or equal to}0.1). Wouldn't one expect FtsH pulls down the RC47 complex containing D1, D2, and RC47. Probing the RC47 level would have been useful in settling this. A key proposition of the authors' is that the hydrogen bonding between D1 W14 and S25 of PsbI is disrupted by the oxidative modification of W14. Can this hypothesis be further tested by replacing the S25 of PsbI with Ala, for example?

2. Although most of the work described is in vivo analysis, which is desirable, some in vitro degradation assays would have strengthened the conclusions. An in vitro degradation assay using the recombinant FtsH and a synthetic peptide encompassing D1 N-terminus with and without OPTM will test the enhanced D1 degradation that the authors predict. This will also help to discern the possibility that whether CP43 detachment alone is sufficient for D1 degradation as suggested for cyanobacteria.

3. The rationale for analyzing a single oxidative modification (W14) as a D1 degradation signal is unclear. D1 N-terminus is modified at multiple sites. Please see Mckenzie and Puthiyaveetil, bioRxiv May 04 2023. Also, why is modification by only 1O2 considered while superoxide and hydroxide radicals can equally damage D1?

4. The D1 degradation assay seems not repeatable for the W14F mutant. High light minus CAM results in Fig. 3 shows a statistically significant decrease in D1 levels for W14F at multiple time points but the same assay in Fig. 4a does not produce a statistically significant decrease at 90 min of incubation. Why is this? Accelerated D1 degradation in the Phe mutant under high light is key evidence that the authors cite in support of their hypothesis.

5. The description of results at times is not nuanced enough, for e.g. lines 116-117 state "The oxidation levels in Trp-14 and Trp-314 increased 1.8-fold and 1.4-fold in var2 compared to the wild type, respectively (Fig. 1c)" while an inspection of the figure reveals that modification at W314 is significant only for NFK and not for KYN and OIA. Likewise, the authors write that CP43 mutant W353F has no growth phenotype under high light but Figure S6 reveals otherwise. The slow growth of this mutant is in line with the earlier observation made by Anderson et al., 2002. In lines 162-163, the authors talk about unchanged electron transport in some site-directed mutants and cite Fig. 2c but this figure only shows chl fluorescence trace and nothing else.

6. The authors rightly discuss an alternate hypothesis that the simple disassembly of the monomeric core into RC47 and CP43 alone may be sufficient for selective D1 degradation as in cyanobacteria. This hypothesis cannot yet be ruled out completely given the lack of some in vitro degradation data as mentioned in point 2. Oxidative protein modification indeed drives the disassembly of the monomeric core (Mckenzie and Puthiyaveetil, bioRxiv May 04 2023).

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.

Reviewer #2 (Public Review):

The ATPase protein machine cohesin shapes the genome by loop extrusion and holds sister chromatids together by topological entrapment. When executing these functions, cohesin is tightly regulated by multiple cofactors, such as Scc2/Nipbl, Pds5, Wapl, and Eco1/Esco1/2, and it undergoes dynamic conformational changes with ATP binding and hydrolysis. The mechanisms by which cohesin extrudes DNA loops and medicates siter-chromatid cohesion are still not understood. A major reason for the lack of understanding of cohesin dynamics and regulation is the failure to capture the structures of intact cohesin in different nucleotide-bound states and in complex with various regulators. So far only the ATP state cohesin bound to NIPBL and DNA have been experimentally determined.

In this manuscript, Nasmyth et al. made use of the powerful protein structure prediction tool, AlphaFold2 (AF), to predict the models of tens of cohesin subcomplexes from different species. The results provide important insight into how the Smc3-Scc1 DNA exiting gate is opened, how Pds5 and Wapl maintain the opened gate, how Pds5 and Scc3/SA recruit different cofactors, how Eco1 and Sororin antagonize Wapl, and how Scc2/Nipbl interacts with Scc3/SA. The models are for the most part consistent with published mutations in these proteins that affect cohesin's functions in vitro and in vivo and raise testable hypotheses of cohesin dynamics and regulation. This study also serves as an example of how to use AF to build models of protein complexes that involve the docking of flexible regions to globular domains.

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 #2 (Public Review):

Summary:<br /> This work performs structural analysis on isolated or purified rootlets.

Strengths:<br /> To date, most studies of this cellular assembly have been from fluorescence microscopy, conventional TEM methods, or through biochemical analysis of constituents. It is clearly a challenging target for structural analysis due to its complexity and heterogeneity. The authors combine observations from cryo-electron tomograms, automated segmentations, subtomogram averaging, and previous data from the literature to present an overall model of how the rootlet is organised.

Their model will serve as a jumping-off point for future studies, and as such it is something of considerable value and interest.

Weaknesses:<br /> It is speculative but is presented as such, and is well-reasoned, plausible, and thorough.

Reviewer #3 (Public Review):

Summary:<br /> The study offers a compelling molecular model for the organization of rootlets, a critical organelle that links cilia to the basal body. Striations have been observed in rootlets, but their assembly, composition, and function remain unknown. While previous research has explored rootlet structure and organization, this study delivers an unprecedented level of resolution, valuable to the centrosome and cilia field. The authors isolated rootlets from mice's eyes. They apply EM to partially purified rootlets (first negative stain, then cryoET). From these micrographs, they observed striations along the membranes along the rootlet but no regular spacing was observed.

The thickness of the sample and membranes prevented good contrast in the tomograms. Thus they further purified the rootlets using detergent, which allowed them to obtain cryoET micrographs of the rootlets with greater details. The tomograms were segmented and further processed to improve the features of the rootlet structures. From their analysis, they described 3 regular cross-striations and amorphous densities, which are connected perpendicularly to filaments along the length of the rootlets. They propose that various proteins provide the striations and rootletin forms parallel coiled coils that run along the rootlet. Overall their data provide a detailed model for the molecular organization of the rootlet.

The major strength is that this high-quality study uses state-of-the-art cryo-electron tomography, sub-tomogram averaging, and image analysis to provide a model of the molecular organization of rootlets. The micrographs are exceptional, with excellent contrast and details, which also implies the sample preparation was well optimized to provide excellent samples for cryo-ET. The manuscript is also clear and accessible.

To further validate their model, it would have been useful to identify some components in the EM maps through complementary approaches (mass spectrometry, mutants disrupting certain features, CLEM). Some potential candidates are mentioned in the discussion.

This research marks a significant step forward in our understanding of rootlets' molecular organization.

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 #2 (Public Review):

Summary:<br /> The manuscript focuses on a persistent question of why germline mutations in BRCA1 which impair homology-directed repair of DNA double-strand breaks predispose to primarily breast and ovarian cancers but not other tissues. The authors propose that replication stress is elevated in the luminal progenitor (LP) cells and apply the gene signature from Dreyer et al as a measure of replication stress in populations of cells selected by FACS previously (published by Lim et al.) and suggest an enrichment of replication stress among the LP cells. This is followed by single-cell RNA seq data from a small number of breast tissues from a small number of BRCA1 mutation carriers but the pathogenic variants are not listed. The authors perform an elegant analysis of the effects of BRCA1 knockdown in MCF10A cells, but these cells are not considered a model of LP cells.

Overall, the manuscript suffers from significant gaps and leaps in logic among the datasets used. The connection to luminal progenitor cells is not adequately established because the models used are not representative of this population of cells. Therefore, the central hypothesis is not sufficiently justified.

Strengths:<br /> The inducible knockdown of BRCA1 provided compelling data pointing to an upregulation of ELF3 in this setting as well as a small number of other genes. It would be useful to discuss the other genes for completeness and explain the logic for focusing on ELF3. Nonetheless, the connection with ELF 3 is reasonable. The authors provide significant data showing a role for ELF3 in breast epithelial cells and its role in cell survival.

Weaknesses:<br /> The initial observations in primary breast cells have small sample sizes. The mutations in BRCA1 seem to be presumed to be all the same, but we know that pathogenic variants differ among individuals and range from missense mutations affecting interactions with one critical partner to large-scale truncations of the protein.

The figure legends are missing critical details that make it difficult for the reader to evaluate the data. The data support the notion that ELF3 may participate in relieving replication stress, but does not appear to be limited to LP cells as proposed in the hypothesis.

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 #2 (Public Review):

Summary:<br /> This study utilizes a large series of neurulation human embryos to address several questions about the similarities and differences between human neurulation and model systems such as the chicken and rodent.

Strengths:<br /> The number of specimens utilized for the analysis provides robustness to the findings.

Weaknesses:<br /> It is not clear how the gestational age of the specimens was determined or how that can be known with certainty. There is no information given in the methods on this. With this in mind, bunching the samples at 2-day intervals in Figure 1J will lead to inaccuracies in assessing the rate of somite formation. This is pointed out as a major difference between specimens and organoids in the abstract but a similar result in the results section. The data supporting either of these statements is not convincing.

Whenever possible, give the numbers of specimens that had the described findings. For example, in Figure 2C - how many embryos were examined with the massive rounded end at CS13? Apoptosis in Figures 3 and 4?

For Figure 2I-K, it would be informative to superimpose the individual data points on the box plots distinguishing males from females, as in Figure 1I.

Is it possible to quantitate apoptosis and proliferation data?

The Tunel staining in Figure 3 is difficult to make out.

Additional improvements to the presentation of figures, writing, and quantization of results are suggested.

Reviewer #2 (Public Review):

Joshi et al. investigated the use of dantrolene, an RyR stabilizing drug, in improving contractile function and slowing pathological progression of pressure-overload heart failure. In a guinea pig model, they found that dantrolene treatment reduced cytosolic Ca2+ levels, improved contractility, reduced the incidence of arrhythmias, reduced fibrosis, and slowed the progression of heart failure. Importantly, delaying treatment until 3 weeks after aortic banding (when heart failure was already established) also resulted in improvements in function and decreased arrhythmogenesis. While some of the mechanistic details remain to be worked out, the data suggest that improving intracellular Ca2+ handling can break the vicious cycle of sympathetic activation, ROS production, and further deterioration of cardiac function.

The functional ECG and echo data are convincing, and very clearly demonstrate the positive effects of dantrolene in heart failure. This is important because dantrolene is already FDA-approved to treat malignant hyperthermia and muscle spasms, so repurposing this drug as a heart failure therapeutic might have a straightforward path to clinical implementation. This also highlights the non-specific nature of dantrolene to interact with RyR1, and therefore, potential side effects. However, this does not detract from the main proof-of-concept demonstrated here.

The guinea pig model employed here is also a strength, as the guinea pig has intracellular Ca2+ handling and ionic currents that are much more similar to human (vs. a murine model, for example).

One weakness is the exclusion of female animals from the study. The authors report more heterogeneity in the progression of HF in the female guinea pig model, however it will be very important to determine effects of dantrolene in the female heart, as there are considerable known sex differences in intracellular Ca2+ handling and contractility. Therefore, it is possible that dantrolene could have sex-dependent effects.

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):

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 #2 (Public Review):

Summary:<br /> This study reports the levels of expression of selected genes implicated in Wnt signaling in trabecular bone from femur heads obtained after surgery from post-menopausal women with (15 women) or without (21 women) type 2 diabetes. They found higher expression levels of SOST and WNT5A, and lower expression levels of LEF-1 and WNT10B in tissues from subjects with T2D, correlating with glycemia and advanced glycation products. No significant differences in bone density were observed. Overall, this is a cross-sectional, observational study measuring a limited set of genes found to vary with glycemia in postmenopausal women undergoing hip surgery.

Strengths:<br /> The study demonstrates the feasibility of measuring gene expression in post-surgical trabecular bone samples, and finds differences associated with glycemia despite a relatively small number of subjects. It can form the basis for further research on the causes and consequences of changes in elements of the WNT signaling pathway in bone biology and disease.

Weaknesses:<br /> The small number of targeted genes does not provide a comprehensive view of the transcriptional landscape within which the effects are observed. The gene expression changes are not associated with cellular or physiological properties of the tissue, raising questions about the biological significance of the observations.

Reviewer #3 (Public Review):

Summary:<br /> The manuscript by Leanza and colleagues explores the regulation of Wnt signaling and its association with advanced glycation end products (AGEs) accumulation in postmenopausal women with type 2 diabetes (T2D). The paper provides valuable insights into the potential mechanisms underlying bone fragility in individuals with T2D. Overall, the manuscript is well-structured, and the methodology is sound. I would suggest some minor revisions to improve clarity.

Strengths:<br /> The study addresses an important and clinically relevant question concerning the mechanisms underlying bone fragility in postmenopausal women with T2D.

The study's methodology appears sound, and the inclusion of postmenopausal women with and without T2D undergoing hip arthroplasty adds to the clinical relevance of the findings. Additionally, measuring gene expression and AGEs in bone samples provides direct insights into the study's objectives.

The manuscript presents data clearly, and the results are well-organized.

Weaknesses:<br /> Title. The title could be more specific to better reflect the content of the study. Also, the abstract should concisely summarize the study's main findings, providing some figures.

Introduction: the introduction would benefit from the addition of a clearer, more focused statement of the research questions or hypotheses guiding this study.

Methods: more information is needed on the hystomorphometry analysis. Surgical samples from 8 T2D and 9 non-diabetic subjects were used for histomorphometry analysis. How did these subjects compare with the other subjects in the T2D and control groups? Were they representative? How were they selected?

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 #2 (Public Review):

In the manuscript by Yang et al titled "Mecp2 fine-tunes quiescent exit by targeting nuclear receptors", the authors found that Mecp, a well-known protein because of its crucial role in neurological disorders, has a cell cycle-dependent ability to negatively regulate quiescent exit by transcriptional activation of metabolic genes while repressing proliferation-related genes. Conceptually, this is an interesting study with very well-executed experiments and controls.

Since the mutation of MeCP2 was identified as the cause of Rett syndrome, the previous reports have been focused on the exhaustive biochemical and functional characterization of this protein. In this study, the authors show that MeCP2 expression is cell-cycle related, and acute reduction of Mecp2 is essential for efficient quiescence exit in cells. They also identified a novel E3 ligase Nedd4 contributes to Mecp2 degradation during G0 exit. These findings are the first description of MeCP2 protein expression during the cell cycle. The variation in MeCP2 levels at different stages of the cell cycle phases should be taken into consideration when examining MeCP2-related disordered disease.

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 #2 (Public Review):

In this study the authors sought to investigate how the metabolic state of iNKT cells impacts their potential pathological role in allergic asthma. The authors used two mouse models, OVA and HDM-induced asthma, and assessed genes in glycolysis, TCA, B-oxidation and FAS. They found that acetyl-coA-carboxylase 1 (ACC1) was highly expressed by lung iNKT cells and that ACC1 deficient mice failed to develop OVA-induced and HDM-induced asthma. Importantly, when they performed bone marrow chimera studies, when mice that lacked iNKT cells were given ACC1 deficient iNKT cells, the mice did not develop asthma, in contrast to mice given wildtype NKT cells. In addition, these observed effects were specific to NKT cells, not classic CD4 T cells. Mechanistically, iNKT cell that lack AAC1 had decreased expression of fatty acid-binding proteins (FABPs) and peroxisome proliferator-activated receptor (PPAR)γ, but increased glycolytic capacity and increased cell death. Moreover, the authors were able to reverse the phenotype with the addition of a PPARg agonist. When the authors examined iNKT cells in patient samples, they observed higher levels of ACC1 and PPARG levels, compared to healthy donors and non-allergic-asthma patients.

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 #2 (Public Review):

This work provides a new tool (H3-Opt) for the prediction of antibody and nanobody structures, based on the combination of AlphaFold2 and a pre-trained protein language model, with a focus on predicting the challenging CDR-H3 loops with enhanced accuracy than previously developed approaches. This task is of high value for the development of new therapeutic antibodies. The paper provides an external validation consisting of 131 sequences, with further analysis of the results by segregating the test sets into three subsets of varying difficulty and comparison with other available methods. Furthermore, the approach was validated by comparing three experimentally solved 3D structures of anti-VEGF nanobodies with the H3-Opt predictions

Strengths:<br /> The experimental design to train and validate the new approach has been clearly described, including the dataset compilation and its representative sampling into training, validation and test sets, and structure preparation. The results of the in silico validation are quite convincing and support the authors' conclusions.

The datasets used to train and validate the tool and the code are made available by the authors, which ensures transparency and reproducibility, and allows future benchmarking exercises with incoming new tools.

Compared to AlphaFold2, the authors' optimization seems to produce better results for the most challenging subsets of the test set.

Weaknesses:<br /> The scope of the binding affinity prediction using molecular dynamics is not that clearly justified in the paper.

Some parts of the manuscript should be clarified, particularly the ones that relate to the experimental validation of the predictions made by the reported method. It is not absolutely clear whether the experimental validation is truly a prospective validation. Since the methodological aspects of the experimental determination are not provided here, it seems that this may not be the case. This is a key aspect of the manuscript that should be described more clearly.

Some Figures would benefit from a more clear presentation.

Reviewer #3 (Public Review):

Summary:<br /> The manuscript introduces a new computational framework for choosing 'the best method' according to the case for getting the best possible structural prediction for the CDR-H3 loop. The authors show their strategy improves on average the accuracy of the predictions on datasets of increasing difficulty in comparison to several state-of-the-art methods. They also show the benefits of improving the structural predictions of the CDR-H3 in the evaluation of different properties that may be relevant for drug discovery and therapeutic design.

Strengths:<br /> The authors introduce a novel framework, which can be easily adapted and improved. The authors use a well-defined dataset to test their new method. A modest average accuracy gain is obtained in comparison to other state-of-the art methods for the same task while avoiding testing different prediction approaches.

Weaknesses:<br /> The accuracy gain is mainly ascribed to easy cases, while the accuracy and precision for moderate to challenging cases are comparable to other PLM methods (see Fig. 4b and Extended Data Fig. 2). That raises the question: how likely is it to be in a moderate or challenging scenario? For example, it is not clear whether the comparison to the solved X-ray structures of anti-VEGF nanobodies represents an easy or challenging case for H3-OPT. The mutant nanobodies seem not to provide any further validation as the single mutations are very far away from the CDR-H3 loop and they do not disrupt the structure in any way. Indeed, RMSD values follow the same trend in H3-OPT and IgFold predictions (Fig. 4c). A more challenging test and interesting application could be solving the structure of a designed or mutated CDR-H3 loop.

The proposed method lacks a confidence score or a warning to help guide the users in moderate to challenging cases.

The fact that AF2 outperforms H3-OPT in some particular cases (e.g. Fig. 2c and Extended Data Fig. 3) raises the question: is there still room for improvements? It is not clear how sensible is H3-OPT to the defined parameters. In the same line, bench-marking against other available prediction algorithms, such as OmegaFold, could shed light on the actual accuracy limit.

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.

Reviewer #2 (Public Review):

The work presented in this manuscript focuses on the role of Cylicins in spermiogenesis and the consequences of their absence on infertility. The manuscript is presented in two parts: the first part studies the absence of Cylicins from KO mouse models and shows in mice that both isoforms of Cylicins are necessary for normal spermiogenesis. The evaluation of double heterozygotes is particularly useful for the second part which looks at the presence of mutations in these genes in a cohort of infertile men. A patient with two hemizygous/heterozygous mutations in the CYLC1 and 2 genes, respectively, was identified for the first time and the results obtained with the KO models support the hypothesis of the pathogenicity of the mutations.

In general, the experiments are perfectly performed and the results are clear. Numerous techniques in the state of the art in male reproduction are used to obtain high-quality phenotyping of the mouse models.

The discovery of two concomitant mutations in an infertile patient is very interesting and the work carried out on mice allows supporting that an absence of CYLC1 and a heterozygous mutation of CYLC2 could lead to a phenotype of complete infertility. However, as the mutation on CYLC2 is not identified as pathogenic, the pathogenicity of this mutation remains in question (the authors note this point in the discussion). It would be interesting to see if the mutated amino acid is conserved between different species. In mice, the authors have shown the importance of these proteins on the morphology of the acrosome. What about in humans?

Reviewer #3 (Public Review):

The authors tried to study the role of the cylicin gene in sperm formation and male fertility. They used the Crispr/cas 9 to knockout two mouse cylicin genes, cylicin 1 and cylicin 2. They used comprehensive methods to phenotype the mouse models and discovered that the two genes, particularly cylicin 2 are essential for sperm calyx formation. They further compared the evolution of the two genes. Finally, they identified mutations of the genes in a patient. The major strengths are the high quality of data presented, and the conclusion is supported by their findings from the animal models and patients. The major weakness is that the study is rather descriptive without molecular mechanism studies, limiting its impact on the field.

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 #2 (Public Review):

Summary:<br /> In this study, Olivieri & Wang et.al. probe the role of the conserved alphaC-beta4 loop in the allosteric regulation of the PKA catalytic subunit. The authors employ a combination of NMR-restrained molecular dynamics simulations and mutational analysis to uncover the conformational transitions between distinct excited states and identify a pivotal role for the alphaC-beta4 loop in facilitating these conformational transitions. These studies support previous models proposing the alphaC-beta4 loop as a critical element in kinase conformational regulation. Overall, this is a timely and fitting study.

Strengths:<br /> 1. Exciting application of NMR and MD to explore hidden conformation states of kinases.<br /> 2. Novel mechanistic insights into the role of the alphaC-beta4 loop in PKA.

Weaknesses:<br /> 1. While the alphaC-beta4 loop is a conserved feature of protein kinases, the residues within this loop vary across various kinase families and groups, enabling group and family-specific control of activity through cis and trans acting elements. F102 in PKA interacts with co-conserved residues in the C-tail, which has been proposed to function as a cis regulatory element. The authors should elaborate on the conformational changes in the C-tail, particularly in the arginine that packs against F102, in the results and discussion. This would further extend the impact and scope of the manuscript, which is currently confined to PKA.<br /> 2. The MD data and conformational states would be a valuable resource for the community and should be shared via some open-source repositories.<br /> 3. The authors state that ES1 and ES2 states are novel and not observed in previous crystal structures. The authors should quantify this through comparisons with PKA inactive states and with other AGC kinases.<br /> 4. Based on the results, can the authors speculate on the impact of oncogenic mutations in the alphaC-beta4 loop mutations in PKA?

Reviewer #3 (Public Review):

Summary:<br /> Combining several MD simulation techniques (NMR-constrained replica-exchange metadynamics, Markov State Model, and unbiased MD) the authors identified the aC-beta4 loop of PKA kinase as a switch crucially involved in PKA nucleotide/substrate binding cooperatively. They identified a previously unreported excited conformational state of PKA (ES2), this switch controls and characterized ES2 energetics with respect to the ground state. Based on translating the simulations into chemical shits and NMR characterizing of PKA WT and an aC-beta4 mutant, the author made a convincing case in arguing that the simulation-suggested excited state is indeed an excited state observed by NMR, thus giving the excited state conformational details.

Strengths:<br /> This work incorporates extensive simulation works, new NMR data, and in vitro biochemical analysis. It stands out in its comprehensiveness, and I think it made a great case.

Weaknesses:<br /> The manuscript is somewhat difficult to read even for kinase experts, and even harder for the layman. The difficulty partially arises from mixing technical description of the simulations with structural interpretation of the results, which is more intuitive, and partially arises from the assumption that readers are familiar with kinase architecture and its key elements (the aC helix, the APE motif etc).

Reviewer #2 (Public Review):

The authors sought to define the molecular structure of autoinhibited Kinesin-1, which is the major kinesin providing plus-end directed transport on microtubules. The paper reports a structural model of full-length kinesin-1 which builds on the known folded conformation of kinesin-1 and describes its autoinhibitory mechanism using cryo-EM, alphafold structural predictions, cross-linking, and mass spectrometry. The authors study the conformation of dimeric Kinesin Heavy Chain (KHC) and tetrameric KHC bound to the Kinesin Light Chains (KLCs), where KLC stabilizes the autoinhibited conformation. The combination of these various approaches leads to an integrated molecular model of autoinhibited Kinesin-1. Until now, there was some debate over the role of the small coiled-coil 3 (a and b) and where the hinge region of Kinesin-1. The authors resolve this question and present data indicating the hinge is between cc3a and cc3b.

In some places the absence of crosslinks is reported as a lack of interaction, however, it could also be that there are no residues that can be crosslinked in this region. Some crosslinks also are too long to satisfy the model, so it is possible, while most crosslinks occur when Kinesin-1 is inhibited, that a small number of crosslinks arise from when Kinesin-1 adopts another conformation. The structural data are supported by single-molecule motility assays with various mutants of Kinesin-1, which greatly help characterising the domains functionally.

Overall there are some interesting novel data on the autoinhibitory mechanism of Kinesin-1, with well performed and analyzed data with KLC and TRAP. The topic and paper will be of interest to many.

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 #2 (Public Review):

Summary:<br /> In eukaryotes, sterols are crucial for signaling and regulating membrane fluidity, however, the mechanism governing cholesterol production and transport across the cell membrane in bacteria remains enigmatic. The manuscript by Zhai et al. sheds light on this topic by uncovering three potential cholesterol transport proteins. Through comprehensive bioinformatics analysis, the authors identified three genes bstA, bstB, and bstC encoding proteins which share homology with transporters, periplasmic binding proteins, and periplasmic components superfamily, respectively. Furthermore, the authors confirmed the specific interaction between these three proteins and C-4 methylated sterols and determined the structures of BstB and BstC. Combining these structural insights with molecular dynamics simulation, they postulated several plausible substrate binding sites within each protein.

Strengths:<br /> The authors have identified 3 proteins that seem likely to be involved in sterol transport between the inner and outer membrane. The structures are of high quality, and the sterol binding experiments support a role for these proteins in sterol transport.

Weaknesses:<br /> While the author's model is very plausible, direct evidence for a role of BstABC in transport, or that the 3 proteins function together in a single pathway, is limited.

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 #3 (Public Review):

Summary:<br /> The work in this manuscript builds on prior efforts by this team to understand how sterols are biosynthesized and utilized in bacteria. The study reports a new function for three genes encoded near sterol biosynthesis enzymes, suggesting the resulting proteins function as a sterol transport system. Biochemical and structural characterization of the two soluble components of the pathway establishes that both proteins can bind sterols, with a preference for 4-methylated derivatives. High-resolution x-ray structures of the apoproteins reveal hydrophobic cavities of the appropriate size to accommodate these substrates. Docking and molecular dynamics simulations confirm this observation and provide specific insights into residues involved in substrate binding.

Strengths:<br /> The manuscript is comprehensive and well-written. The annotation of a new function in a set of proteins related to bacterial sterol usage is exciting and likely to enable further study of this phenomenon - which is currently not well understood. The work also has implications for improving our understanding of lipid usage in general among bacterial organisms.

Weaknesses:<br /> The authors might consider moving some of the bioinformatics figures to the main text, given how much space is devoted to this topic in the results section.

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.

Reviewer #2 (Public Review):

Summary:<br /> Chong Chen and colleagues reported that mutations were identified in the ZC3H11A gene in four adolescents from 1015 high myopia subjects in their myopia cohort. They further generated Zc3h11a knockout mice utilizing the CRISPR/Cas9 technology. They analyzed the heterozygotes knockout mice compared to control littermates and found refractive error changes, electrophysiological differences, and retinal inflammation-related gene expression differences. They concluded that ZC3H11A may play a role in the early onset of myopia by regulating inflammatory responses.

Strengths:<br /> Data were shown from both clinical cohort and animal models.

Weaknesses:<br /> Their findings are interesting and important, however; they need to resolve several points to make the current conclusion.

1. They described the ZC3H11A gene as a pathogenic variant for high myopia. It should be classified as pathogenic according to the guidelines of the American College of Medical Genetics and Genomics (Richards et al., Genet Med 17(5):405-24, 2015). The modes of inheritance for the families need to be shown. They also described identifying the gene as a "new" candidate. It should be checked in databases such as gnomAD and ClinVar, and any previous publications and be declared as a novel variant.

2. The phenotypes of the heterozygote mice are weak overall. The het mice showed mild to moderate myopic refractive shifts from 4 to 10 weeks of age. However, this cannot be explained by other ocular biometrics such as anterior chamber depth or lens thickness. Some differences are found between het and WT littermates in axial length and vitreous chamber depth but disappear after 8 weeks old. Furthermore, the early differences are not enough to explain the refractive error changes. They mentioned that they did not use homozygotes because of the embryonic lethality. I would strongly suggest employing conditional knockout systems to analyze homozygotes. This will also be able to identify the causative tissues/cells because they assume bipolar cells are functional. The cells in the retinal pigment epithelium and choroid are also important to contribute to myopia development.

3. Their hypothesis regarding inflammatory gene changes and myopic development is not logical. Are the inflammatory responses evoked from bipolar cells? Did the mice show an accumulation of inflammatory cells in the inner retina? Visible retinal inflammation is not generally seen in either early-onset or high-myopia human subjects. Can this be seen in the actual subjects in the cohort? To me, this is difficult to adapt the retina-to-sclera signaling they mentioned in the discussion so far. Egr-1 may be examined as described.

Reviewer #3 (Public Review):

Chen et al have identified a new candidate gene for high myopia, ZC3H11A, and using a knock-out mouse model, have attempted to validate it as a myopia gene and explain a potential mechanism. They identified 4 heterozygous missense variants in highly myopic teenagers. These variants are in conserved regions of the protein, but the authors provide no evidence that these specific variants affect protein function. They then created a knock-out mouse. Heterozygotes show myopia at all ages examined but increased axial length only at very early ages. Unfortunately, the authors do not address this point or examine corneal structure in these animals. They show that the mice have decreased B-wave amplitude on electroretinogram (a sign of retinal dysfunction associated with bipolar cells), and decreased expression of a bipolar cell marker, PKC. They do not address, however, whether there are fewer bipolar cells, or simply decreased expression of the marker protein. On electron microscopy, there are morphologic differences in the outer nuclear layer (where bipolar, amacrine, and horizontal cell bodies reside). Transcriptome analysis identified over 700 differentially expressed genes. The authors chose to focus on the PI3K-AKT and NF-B signaling pathways and show changes in the expression of genes and proteins in those pathways, including PI3K, AKT, IB, NF-B, TGF-1, MMP-2, and IL-6, although there is very high variability between animals. They propose that myopia may develop in these animals either as a result of visual abnormality (decreased bipolar cell function in the retina) or by alteration of NF-B signaling. These data provide an interesting new candidate variant for the development of high myopia, and provide additional data that MMP2 and IL6 have a role in myopia development, but do not support the claim of the title that myopia is caused by an inflammatory reaction.

Reviewer #3 (Public Review):

Summary:<br /> In this study, the authors set out to address the question of how the SNARE protein Syntaxin 17 senses autophagosome maturation by being recruited to autophagosomal membranes only once autophagosome formation and sealing is complete. The authors discover that the C-terminal region of Syntaxin 17 is essential for its sensing mechanism that involves two transmembrane domains and a positively charged region. The authors discover that the lipid PI4P is highly enriched in mature autophagosomes and that electrostatic interaction with Syntaxin 17's positively charged region with PI4P drives recruitment specifically to mature autophagosomes. The temporal basis for PI4P enrichment and Syntaxin 17 recruitment to ensure that unsealed autophagosomes do not fuse with lysosomes is a very interesting and important discovery. Overall, the data are clear and convincing, with the study providing important mechanistic insights that will be of broad interest to the autophagy field, and also to cell biologists interested in phosphoinositide lipid biology. The author's discovery also provides an opportunity for future research in which Syntaxin 17's c-terminal region could be used to target factors of interest to mature autophagosomes.

Strengths:<br /> The study combines clear and convincing cell biology data with in vitro approaches to show how Syntaxin 17 is recruited to mature autophagosomes. The authors take a methodical approach to narrow down the critical regions within Syntaxin 17 required for recruitment and use a variety of biosensors to show that PI4P is enriched on mature autophagosomes.

Weaknesses:<br /> There are no major weaknesses, overall the work is highly convincing. It would have been beneficial if the authors could have shown whether altering PI4P levels would affect Syntaxin 17 recruitment. However, this is understandably a challenging experiment to undertake and the authors outlined their various attempts to tackle this question. In addition, clear statements within the figure legends on the number of independent experimental repeats that were conducted for experiments that were quantitated are not currently present in the manuscript.

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 #2 (Public Review):

Summary:<br /> Syntaxin17 (STX17) is a SNARE protein that is recruited to mature (i.e., closed) autophagosomes, but not to immature (i.e., unclosed) ones, and mediates the autophagosome-lysosome fusion. How STX17 recognizes the mature autophagosome is an unresolved interesting question in the autophagy field. Shinoda and colleagues set out to answer this question by focusing on the C-terminal domain of STX17 and found that PI4P is a strong candidate that causes the STX17 recruitment to the autophasome.

Strengths:<br /> The main findings are: 1) Rich positive charges in the C-terminal domain of STX17 are sufficient for the recruitment to the mature autophagosome; 2) Fluorescence charge sensors of different strengths suggest that autophagic membranes have negative charges and the charge increases as they mature; 3) Among a battery of fluorescence biosensors, only PI4P-binding biosensors distribute to the mature autophagosome; 4) STX17 bound to isolated autophagosomes is released by treatment with Sac1 phosphatase; 5) By dynamic molecular simulation, STX17 TM is shown to be inserted to a membrane containing PI4P but not to a membrane without it. These results indicate that PI4P is a strong candidate that STX17 binds to in the autophagosome.

Weaknesses:<br /> • It was not answered whether PI4P is crucial for the STX17 recruitment in cells because manipulation of the PI4P content in autophagic membranes was not successful for unknown reasons.<br /> • The molecular simulation study did not show whether PI4P is necessary for the STX17 TM insertion or whether other negatively charged lipids can play a similar role.<br /> • The question that the authors posed in the beginning, i.e., why is STX17 recruited to the mature (closed) autophagosome but not to immature autophagic membranes, was not answered. The authors speculate that the seemingly gradual increase of negative charges in autophagic membranes is caused by an increase in PI4P. However, this was not supported by the PI4P fluorescence biosensor experiment that showed their distribution to the mature autophagosome only. Here, there are at least two possibilities: 1) The increase of negative charges in immature autophagic membranes is derived from PI4P. However the fluorescence biosensors do not bind there for some reason; for example, they are not sensitive enough to recognize PI4P until it reaches a certain level, or simply, their binding does not occur in a quantitative manner. 2) The negative charge in immature membranes is not derived from PI4P, and PI4P is generated abundantly only after autophagosomes are closed. In either case, it is not easy to explain why STX17 is recruited to the mature autophagosome only. For the first scenario, it is not clear how the PI4P synthesis is regulated so that it reaches a sufficient level only after the membrane closure. In the second case, the mechanism that produces PI4P only after the autophagosome closure needs to be elucidated (so, in this case, the question of the temporal regulation issue remains the same).

Reviewer #2 (Public Review):

Summary:

Recent advances in single-cell profiling of gene expression (RNA) permit the analysis of specialized cell types, an approach that has great value in the nervous system which is characterized by prodigious neuronal diversity. The novel data in this study focus primarily on genetic profiling to compare autonomic neurons from ganglia associated with the cranial parasympathetic outflow (sphenopalatine (also known as pteropalatine), the thoraco-lumbar sympathetic outflow (stellate, coeliac) and the sacral parasympathetic outflow (pelvic). Using statistical methods to reduce the dimensionality of the data and map gene expression, the authors provide interesting evidence that cranial parasympathetic and sacral sympathetic ganglia differ from each other and from sympathetic ganglia (Figures 1, S1 - S4). The authors interpret the mapping analysis as evidence that the cranial and sacral outflows differ so calling them both parasympathetic is unjustified. Based on anatomical localization of markers (Figure 2 ) (mainly transcription factors) the authors show a similarity between the sympathetic and pelvic ganglion. In Figure 3 they present evidence that some pelvic ganglionic neurons are dually innervated by sympathetic preganglionic neurons and sacral preganglionic neurons. These observations are interpreted to mean that the pelvic ganglion is not parasympathetic, but rather a modified sympathetic ganglion - hence the title of the manuscript.

Strengths:<br /> The extensive use of single-cell profiling in this work is both interesting and exciting. Although still in its early stages, it holds promise for a deepened understanding of autonomic development and function. As noted in the introduction, this study extends previous work by Professor Brunet and his associates.

Weaknesses:<br /> This work further documents differences between the cranial and sacral parasympathetic outflows that have been known since the time of Langley - 100 years ago. The approach taken by Brunet et al. has focused on late neonatal and early postnatal development, a time when autonomic function is still maturing. In addition, the sphenopalatine and other cranial ganglia develop from placodes and the neural crest, while sympathetic and sacral ganglia develop from the neural crest alone. How then do genetic programs specifying brainstem and spinal development differ and how can this account for kinship that Brunet documents between spinal and sacral ganglia? One feature that seems to set the pelvic ganglion apart is the mixture of 'sympathetic' and 'parasympthetic' ganglion cells and the convergence of preganglionic sympathetic and parasympathetic synapses on individual ganglion cells (Figure 3). This unusual organization has been reported before using microelectrode recordings (see Crowcroft and Szurszewski, J Physiol (1971) and Janig and McLachlan, Physiol Rev (1987)). Anatomical evidence of convergence in the pelvic ganglion has been reported by Keast, Neuroscience (1995). It should also be noted that the anatomy of the pelvic ganglion in male rodents is unique. Unlike other species where the ganglion forms a distributed plexus of mini-ganglia, in male rodents the ganglion coalesces into one structure that is easier to find and study. Interestingly the image in Figure 3A appears to show a clustering of Chat-positive and Th-positive neurons. Does this result from the developmental fusion of mini ganglia having distinct sympathetic and parasympathetic origins? In addition, Brunet et al dismiss the cholinergic and noradrenergic phenotypes as a basis for defining parasympathetic and parasympathetic neurons. However, see the bottom of Figure S4 and further counterarguments in Horn (Clin Auton Res (2018)). What then about neuropeptides, whose expression pattern is incompatible with the revised nomenclature proposed by Brunet et al.? Figure 1B indicates that VIP is expressed by sacral and cranial ganglion cells, but not thoracolumbar ganglion cells. The authors do not mention neuropeptide Y (NPY). The immunocytochemistry literature indicates that NPY is expressed by a large subpopulation of sympathetic neurons but never by sacral or cranial parasympathetic neurons.

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 #2 (Public Review):

In this study, the authors aimed to evaluate the contribution of brain-age indices in capturing variance in cognitive decline and proposed an alternative index, brain-cognition, for consideration.

The study employs suitable methods and data to address the research questions, and the methods and results sections are generally clear and easy to follow.

Comments on revised submission:

I appreciate the authors' efforts in significantly improving the paper, including some considerable changes, from the original submission. While not all reviewer points were tackled, the majority of them were adequately addressed. These include additional analyses, more clarity in the methods and a much richer and nuanced discussion. While recognising the merits of the revised paper, I have a few additional comments.

Perhaps it would help the reader to note that it might be expected for brain-cognition to account for a significantly larger variance (11%) in fluid cognition, in contrast to brain-age. This stems from the fact that the authors specifically trained brain-cognition to predict fluid cognition, the very variable under consideration. In line with this, the authors later recommend that researchers considering the use of brain-age should evaluate its utility using a regression approach. The latter involves including a brain index (e.g. brain-cognition) previously trained to predict the regression's target variable (e.g. fluid cognition) alongside a brain-age index (e.g., corrected brain-age gap). If the target-trained brain index outperforms the brain-age metric, it suggests that relying solely on brain-age might not be the optimal choice. Although not necessarily the case, is it surprising for the target-trained brain index to demonstrate better performance than brain-age? This harks back to the broader point raised in the initial review: while brain-age may prove useful (though sometimes with modest effect sizes) across diverse outcomes as a generally applicable metric, a brain index tailored for predicting a specific outcome, such as brain-cognition in this case, might capture a considerably larger share of variance in that specific context but could lack broader applicability. The latter aspect needs to be empirically assessed.

Furthermore, the discussion pertaining to training brain-age models on healthy populations for subsequent testing on individuals with neurological or psychological disorders seems somewhat one-sided within the broader debate. This one-sidedness might potentially confuse readers. It is worth noting that the choice to employ healthy participants in the training model is likely deliberate, serving as a norm against which atypical populations are compared. To provide a more comprehensive understanding, referencing Tim Hans's counterargument to Bashyam's perspective could offer a more complete view (https://academic.oup.com/brain/article/144/3/e31/6214475?login=false).

Overall, this paper makes a significant contribution to the field of brain-age and related brain indices and their utility.

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 #3 (Public Review):

The main question of this article is as follows: "To what extent does having information on brain-age improve our ability to capture declines in fluid cognition beyond knowing a person's chronological age?" This question is worthwhile, considering that there is considerable confusion in the field about the nature of brain-age.

Comments on revised version:

Thank you to the authors for addressing so many of my concerns with this revision. There are a few points that I feel still need addressing/clarifying related to 1) calculating brain cognition, 2) the inevitability of their results, and 3) their continued recommendation to use brain-age metrics.

Reviewer #2 (Public Review):

Summary:<br /> The manuscript by Howard et al reports the development of high-affinity WDR5-interaction site inhibitors (WINi) that engage the protein to block the arginine-dependent engagement with its partners. Treatment of MLL-rearranged leukemia cells with high-affinity WINi (C16) decreases the expression of genes encoding most ribosomal proteins and other proteins required for translation. Notably, although these targets are enriched for WDR5-ChIP-seq peaks, such peaks are not universally present in the target genes. High concordance was found between the alterations in gene expression due to C16 treatment and the changes resulting from treatment with an earlier, lower affinity WINi (C6). Besides protein synthesis, genes involved in DNA replication or MYC responses are downregulated, while p53 targets and apoptosis genes are upregulated. Ribosome profiling reveals a global decrease in translational efficiency due to WINi with overall ribosome occupancies of mRNAs ~50% of control samples. The magnitude of the decrements of translation for most individual mRNAs exceeds the respective changes in mRNA levels genome-wide. From these results and other considerations, the authors hypothesize that WINi results in ribosome depletion. Quantitative mass spec documents the decrement in ribosomal proteins following WINi treatment along with increases in p53 targets and proteins involved in apoptosis occurring over 3 days. Notably, RPL22L1 is essentially completely lost upon WINi treatment. The investigators next conduct a CRISPR screen to find moderators and cooperators with WINi. They identify components of p53 and DNA repair pathways as mediators of WINi-inflicted cell death (so gRNAs against these genes permit cell survival). Next, WINi are tested in combination with a variety of other agents to explore synergistic killing to improve their expected therapeutic efficacy. The authors document the loss of the p53 antagonist MDM4 (in combination with splicing alterations of RPL22L1), an observation that supports the notion that WINi killing is p53-mediated.

Strengths:<br /> This is a scientifically very strong and well-written manuscript that applies a variety of state-of-the art molecular approaches to interrogate the role of the WDR5 interaction site and WINi. They reveal that the effects of WINi seem to be focused on the overall synthesis of protein components of the translation apparatus, especially ribosomal proteins-even those that do not bind WDR5 by ChIP (a question left unanswered is how much the WDR5-less genes are nevertheless WINi targeted). They convincingly show that disruption of the synthesis of these proteins is accompanied by DNA damage inferred by H2AX-activation, activation of the p53-pathway, and apoptosis. Pathways of possible WINi resistance and synergies with other anti-neoplastic approaches are explored. These experiments are all well-executed and strongly invite more extensive pre-clinical and translational studies of WINi in animal studies. The studies also may anticipate the use of WINi as probes of nucleolar function and ribosome synthesis though this was not really explored in the current manuscript.

Weaknesses:<br /> A mild deficiency in the current manuscript is the absence of cell biological methods to complement the molecular biological and biochemical approaches so ably employed. Some microscopic observations and confirmation of nucleolar dysfunction and DNA damage would be reassuring.

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?.

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 #2 (Public Review):

Understanding disease conditions often yields valuable insights into the physiological regulation of biological functions, as well as potential therapeutic approaches. In previous investigations, the author's research group identified abnormal expression of brain-derived neurotrophic factor (BDNF) in the hypothalamus of a mouse model exhibiting Smith-Magenis syndrome (SMS), which is caused by heterozygous mutations of the Rai1 gene. Human SMS is associated with distinct facial characteristics, sleep disturbances, behavioral issues, and intellectual disabilities, often accompanied by obesity. Conditional knockout (cKO) of the Bdnf gene from the paraventricular hypothalamus (PVH) in mice led to hyperphagic obesity, while overexpression of the Bdnf gene in the PVH of Rai1 heterozygous mice restored the SMS-like obese phenotype. Based on these preceding findings, the authors of the present study discovered that homozygous Rai1 cKO restricted to Bdnf-expressing cells, or Rai1 gene knockdown solely in Bdnf-positive neurons in the PVH, induced obesity along with intricate alterations in adipose tissue composition, energy expenditure, locomotion, feeding patterns, and glucose tolerance, some of which varied between sexes. Additionally, the authors demonstrated that a brain-penetrating drug capable of activating the AKT cascades, a downstream signaling pathway of BDNF, partially alleviated the SMS-like obesity phenotype in female mice with Rai1 heterozygous mutations. Although the specific (neural) cell type responsible for this signaling remains an open question, the present study unequivocally highlights the importance of Rai1 gene function in PVH Bdnf neurons for the obesity phenotype, providing valuable insights into potential therapeutic strategies for managing obesity associated with SMS.

In the proteomic analysis (Fig. 1), the authors elucidated that multiple phospho-protein signaling pathways, including Akt and mTOR pathways, exhibited significant attenuation in the SMS model mice. Of significance, the manifestation of haploinsufficiency of the Rai1 gene exclusively within the BDNF+ cells demonstrated negligible impact on body weight (Fig. 2-supple 3D), despite observing a reduction in BDNF levels in the heterozygous Rai1 mutant (Fig. 1A). Conversely, the homozygous Rai1 cKO in the BDNF+ cells prominently displayed an obesity phenotype, suggesting substantial dissimilarities in the gene expression profiles between Rai1 heterozygous and homozygous conditions within the BDNF+ cell population. It would be advantageous to precisely identify the responsible differentially expressed genes, possibly including Bdnf itself, in the homozygous cKO model. The observed reduction in the excitability of PVH BDNF+ cells (Fig. 3) is presumably attributed to aberrant gene expression other than Bdnf itself, which may serve as a prospective target for gene expression analysis. Notably, the Rai1 homozygous cKO mice in BDNF+ cells exhibited some sexual dimorphisms in feeding and energy expenditures, as evidenced by Fig. 2 and related figures. Exploring the potential relevance of these sexual differences to human SMS cases and investigating the underlying cellular/molecular mechanisms in the future would provide valuable insights.

The CRISPR-mediated knockdown of the Rai1 gene appears to be highly effective, and the majority of Rai1 cKO effects in Bdnf+ cells are primarily attributed to PVH-Bdnf+ cells based on the similarity of phenotypes observed. With regards to the apparent rescue of the body weight phenotype in Rai1 heterozygous mutants using an AKT pathway activator, the specific biological processes, and neurons responsible for this effect remain unclear. Elucidating these aspects in future studies would be significant when considering potential applications to human SMS cases.

Overall, the present study represents a valuable addition to the authors' series of high-quality molecular genetic investigations into the in vivo functions of the Rai1 gene. This reviewer particularly commends their diligent efforts to enhance our comprehension of SMS and contribute to the future development of more effective therapies for this syndrome.

Reviewer #3 (Public Review):

Summary:<br /> Smith-Magenis syndrome (SMS) is associated with obesity and is caused by deletion or mutations in one cope of the Rai1 gene which encodes a transcriptional regulator. Previous studies have shown that Bdnf gene expression is reduced in the hypothalamus of Rai1 heterozygous mice. This manuscript by Javed et al. further links SMS-associated obesity with reduced Bdnf gene expression in the PVH by providing three lines of evidence. First, the authors conducted proteomic analysis of hypothalamic extracts from WT and SMS (Rai1 +/-) mice and showed that several signaling cascades downstream of BDNF (e.g., PI3K-AKT and mTOR) were down regulated in SMS mice. Second, the authors found that deletion of both copies of the Rai1 gene in all BDNF-expressing cells or BDNF-expressing neurons in the PVH led to obesity, although the phenotype is more subtle than that observed in SMS mice. Third, they found that Rai1 deletion reduced excitability of PVH BDNF neurons.

Strengths:<br /> The study provides additional evidence linking BDNF deficiency to hyperphagia and obesity associated with SMS. Furthermore, the study shows that deletion of only one copy of the Rai1 gene in all BDNF-expressing cells did not cause obesity. This result indicates that BDNF deficiency only has a minor contribution to the metabolic symptoms associated with SMS patients who lose one copy of the RAI1 gene. The discovery that Rai1 is important for excitability of PVH BDNF neurons is interesting.

Weaknesses:<br /> The main mechanism underlying SMS-associated obesity remains to be identified. This limitation is discussed in this revised manuscript. The authors also address my previous concerns in this revised manuscript.

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 #2 (Public Review):

Summary:<br /> The research conducted by Yaning Cui and colleagues delves into understanding FLS2-mediated immunity. This is achieved by comparing the spatiotemporal dynamics of an FLS2-S938A mutant and FLS2-WT, especially in relation to their association with the remorin protein. To delineate the differences between the FLS2-S938A mutant and FLS2-WT, they utilized a plethora of advanced fluorescent imaging techniques. By analyzing surface dynamics and interactions involving the receptor signal co-receptor BAK1 and remorin proteins, the authors propose a model of how FLS2 and BAK1 are assembled and positioned within a remorin-specific nano-environment during FLS2 ligand-induced immune responses.

Strengths:<br /> These techniques offer direct visualizations of molecular dynamics and interactions, helping us understand their spatial relationships and interactions during innate immune responses.

Advanced cell biology imaging techniques are crucial for obtaining high-resolution insights into the intracellular dynamics of biomolecules. The demonstrated imaging systems are excellent examples to be used in studying plant immunity by integrating other functional assays.

Weaknesses:<br /> It's essential to acknowledge that every fluorescence-based method, just like biochemical assays, comes with its unique limitations. These often pertain to spatial and temporal resolutions, as well as the sensitivity of the cameras employed in each setup. Meticulous interpretation is pivotal to guarantee an accurate depiction and to steer clear of potential misunderstandings when employing specific imaging systems to analyze molecular attributes. Moreover, a discerning interpretation and accurate image analysis can offer invaluable guidance for future studies on plant signaling molecules using these nice cell imaging techniques.

For instance, although single-particle analysis couldn't conclusively link FLS2 and remorin, FLIM-FRET effectively highlighted their ligand-triggered association and the disengagement brought on by mutations. While these methodologies seemed to present differing outcomes, they were described in the manuscript as harmonious. In reality, these differences could highlight distinct protein populations active in immune responses, each accentuated differently by the respective imaging techniques due to their individual spatial and temporal limitations. Addressing these variations is imperative, especially when designing future imaging explorations of immune complexes.

Reviewer #3 (Public Review):

Summary:<br /> Receptor kinases (RKs) perceive extracellular signals to regulate many processes in plants. FLS2 is an RK that acts as a pattern-recognition receptor (PRR) to recognize bacterial flagellin and activate pattern-triggered immunity (PTI). PRRs such as FLS2 have been previously shown to reside within PM nanodomains, which can regulate downstream PTI signaling. In the current manuscript, Cui et al use single particle tracking to characterize the effect of previously-described phosposite mutants (FLS2-S938A/D) on the PM organization, endocytosis, and signaling functions of FLS2. The authors confirm that FLS2-S938D but not -S938A is functional for flg22-induced responses, while also demonstrating that phopshodead mutation at this site (S938A) prevents flg22-induced sorting into nanodomains and endocytosis. These results are consistent with S938 being an important phosphorylation site for FLS2 function, however, they fall short of demonstrating that membrane disorganization of FLS2-938A is responsible for downstream signaling defects.

Strengths:<br /> The authors' experiments (single particle tracking, co-localization, etc) do a good job of demonstrating how a non-functional version of FLS2 (S938A) does not alter its spatio-temporal dynamics, nanodomain organization, and endocytosis in response to flg22, suggesting that these require a functional receptor and are regulated by intracellular signaling components.

Weaknesses:<br /> The authors do not provide direct evidence that S938 phosphorylation specifically affects membrane organization, rather than FLS2 signaling more generally. All evidence is consistent with S938A being a non-functional version of FLS2, wherein an activated/functional receptor is required for all downstream events including membrane re-organization, downstream signalling, internalization, etc. Furthermore, the authors never demonstrate that this site is phosphorylated in planta in the basal or flg22-elicited state.

As written, the manuscript also has numerous scientific issues, including a misleading/incomplete description of plant immune signaling, lack of context from previous work, and extensive use of inappropriate references.

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 #2 (Public Review):

Summary:<br /> The mechanisms by which seizures induce neurogenesis has remained unclear. Prior work from the authors demonstrated Mossy cell expressed Shh, that altered Shh expression follows epileptic seizures, and that Shh is a neural mitogen. Here authors show that Shh from mossy cells, which are well positioned between the pyramidal and granule cell layers, are a major source of signaling after seizures, contributing to seizure-induced neurogenesis. Moreover, they find that Mossy cell-sourced Shh is required for self-renewal of NSCs even outside of the context of seizures.

SVZ Gli1 expression was detected in NSCs and Gli1 reporter activity follows kainate-induced seizures. Heterozygous Shh mice show reduced seizure induced Shh signaling and reduced neurogenesis. After localizing Shh production to Mossy cells, authors removed Shh from Mossy cells and found reduced neurogenesis. By activating mossy cells through chemogenetic DREADD, they found that the effect of mossy cells on SVZ neurogenesis is activity-dependent, that Shh signaling activity is upregulated in NSCs by mossy cell neuronal activity, and that the induction of neurogenesis by mossy cell neuronal activity is compromised in the absence of Shh from mossy cells. In a series of experiments incorporating AAV DREADD, they find that mossy cell activity can contribute to neurogenesis in contralateral DG, and that seizure induced Shh may be transported along mossy axons. To examine long-term effects, they study mice several weeks after seizure, and find that suggesting that NSCs are less likely to return to their stem cell state after seizure-induced proliferation in the absence of Shh from mossy cells, and that Shh from mossy cells contributes to persistence of the NSC state during aging.

Strengths:<br /> The results are compelling and impactful, and the study is extremely well done. The various genetic lines in the study ensure robust results. Adequate consideration of statistics, methods of quantification, and avoidance of artifact is given.

Weaknesses:<br /> None identified.

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 #2 (Public Review):

Summary:<br /> The author's main goal is to understand the mechanism by which pyroptosis (through the formation of Gasdermin D (GSDMD) pores in the plasma membrane) contributes to increased release of procoagulant Tissue Factor-containing microvesicles (MV). Their previous data demonstrate that GSDMD is critical for the release of MV that contains Tissue Factor (TF), thus making a link between pyroptosis and hypercoagulation. Given the recent identification of NINJ1 being responsible for plasma membrane rupture (Kayagaki et al. Nature 2011), the authors wanted to determine if NINJ1 is responsible for TF-containing MV release. Given the constitutive ninj1 KO mouse leads to partial embryonic lethality, the authors decided to use a heterozygous ninj1 KO mouse (ninj1+/-). While the data are well controlled, there is limited understanding of the mechanism of action. Also, given that the GSDMD pores have an ~18 nm inner diameter enough to release IL-1β, while larger molecules like LDH (140 kDa) and other DAMPs require plasma membrane rupture (likely mediated by NINJ1), it s not unexpected that large MVs require NINJ1-mediated plasma cell rupture.

Strengths:<br /> The authors convincingly demonstrate that ninj1 haploinsufficiency leads to decreased prothrombin time, plasma TAT and plasma cytokines 90 minutes post-treatment in mice, which leads to partial protection from lethality.

Weaknesses:<br /> - In the abstract, the authors say "...cytokines and protected against blood coagulation and lethality triggered by bacterial flagellin". This conclusion is not substantiated by the data, as you still see 70% mortality at 24 hours in the ninj1+/- mice.

- The previous publication by the authors (Wu et al. Immunity 2019) clearly shows that GSDMD-dependent pyroptosis is required for inflammasome-induced coagulation and mouse lethality. However, as it is not possible for the authors to use the homozygous ninj1 KO mouse due to partial embryonic lethality, it becomes challenging to compare these two studies and the contributions of GSDMD vs. NINJ1. Comparing the contributions of GSDMD and NINJ1 in human blood-derived monocytes/macrophages where you can delete both genes and assess their relevant contributions to TF-containing MV release within the same background would be crucial in comparing how much contribution NINJ1 has versus what has been published for GSDMD? This would help support the in vivo findings and further corroborate the proposed conclusions made in this manuscript.

- What are the levels of plasma TAT, PT, and inflammatory cytokines if you collect plasma after 90 minutes? Given the majority (~70%) of the ninj+/- mice are dead by 24 hours, it is imperative to determine whether the 90-minute timeframe data (in Fig 1A-G) is also representative of later time points. The question is whether ninj1+/- just delays the increases in prothrombin time, plasma TAT, and plasma cytokines.

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 #2 (Public Review):

Summary: In this manuscript, Trautman et al. set out to test the hypothesis that increased intake of dietary protein is deleterious to health when uncoupled from resistance training.

Strengths: The experimental design is well crafted and the experiments provide useful information supporting the hypothesis. The authors take into account the limitations of their study in the discussion, and guide the reader through their results and the interpretation in a fair and measured way, without overstating claims.

Weaknesses: As acknowledged by the authors in the discussion section, this study only features a small sample of male mice from a single strain. Thus the results may not hold when female mice and diverse genetic backgrounds are analyzed. The lack of repeated measures of physiological parameters is also a limitation of the study. Measurements of body weight, body composition, food (calorie) consumption, and locomotor/strength assays could have been provided throughout the study and compared to a baseline value for each animal.

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 #2 (Public Review):

Summary:<br /> The manuscript by Kandoi et al. describes a new 3D retinal organoid model of a mono-allelic copy number variant of the rhodopsin gene that was previously shown to induce autosomal dominant retinitis pigmentosa via a dominant negative mechanism in patients. With advancements in the low-cost genomics application to detect copy number variations, this is a timely article that highlights a potential disease mechanism that goes beyond the retina field. The evidence is relatively strong that the rod photoreceptor phenotype observed in an adult patient with RP in vivo is similar to that phenotype observed in human stem cell-derived retinal organoids. Increases in RHO expression detected by qPCR, RNA-seq, and IHC support this phenotype. Importantly, the amelioration of photoreceptor rhodopsin mislocalization and related defects using the small molecule drug photoregulin demonstrates an important potential clinical application.

Overall, the authors succeeded in providing solid evidence that copy number variation via a genomic RHO duplication leads to abnormalities in rod photoreceptors that can be partially blocked by photoregulin. However, there are several points that should be addressed that will enhance this paper.

Strengths:<br /> - The use of patient-derived organoids from patients that have visual defects is a major strength of this work and adds relevance to the disease phenotype.<br /> - The rod phenotype assessed by qPCR, RNA-seq, and IHC supports a phenotype that shares similarities with the patient.<br /> - The use of a small molecule drug that selectively targets rod photoreceptors, as opposed to cones, is a noteworthy strength.

Weaknesses:<br /> 1. The chromosomal segment that was duplicated had 3 copies of RHO in addition to three copies of each of the flanking genes (IFT122, HIF100, PLXND1). Discussion of the involvement of these genes would be helpful. Would duplication of any of these genes alone cause or contribute to adRP? As an example, a missense mutation in IFT122 was previously implicated in photoreceptor loss (PMID: 33606121 PMCID: PMC8519925).

2. Related to #1, have the authors considered inserting extra copies of RHO (and/or the flanking genes) of these at a genomic safe harbor site? Although not required, this would allow one to study cells with isogenic-matched genetic backgrounds and would partially address the technical challenge of repairing a 188kb duplication, which as the authors note would be difficult to do. Demonstrating that excess copy numbers in different genetic backgrounds would be a huge contribution to the field. At a minimum, a discussion of the role of the nearby genes should be included. 


3. In the patient, the central foveal region was spared suggesting that cones were normal. Was there a similar assessment that cones are unaffected in retinal organoids? 


4. Pathway analysis indicated that glycosylation was perturbed and this was proposed as an explanation as to why rhodopsin was mislocalized. Have the authors verified that there is an actual decrease in glycosylation? 


5. Line 182: by what criteria are the authors able to state that " there were no clear visible anatomical changes in apical-basal retinal cell type distribution during the early differentiation timeframe (data not shown)." Was this based on histological staining with antibodies, nuclear counter-staining, or some other evaluation?


6. Figure 2C - the appearance of the inner segments in RC and RM looks very different from one another. Have the authors ruled out the possibility that the RC organoid cell isn't a cone? In addition, the RM structure has what appears to be a well-defined OLM which would suggest well-formed Muller glia. Do these structures also exist in RC organoids? Typically the OLM does form in older organoids. In addition, was this representative in numerous EM preparations?


7. What criteria were used to assess cell loss? Has any TUNEL labeling been performed to confirm cell loss? From the existing data, it seems that rod outer segments appear to be affected in organoids. However, it's not clear if the photoreceptors themselves actually die in this model.

8. Figure 5B. The RHO staining in the vehicle-treated sample is perturbed relative to the PR3 treatments as indicated in the text. In the vehicle-treated sample, the number of DAPI-positive cells that are completely negative proximal to the inner segments suggests that there might be non-rod cells there. Have the authors confirmed whether these are cones? Labels would be helpful in the left vehicle panel as the morphology looks very different than the treated samples.
<br /> <br /> 9. It is interesting that in addition to increases in RHO, and photo-transduction, there are also increases in PTPRT which is related to synaptic adhesion. Is there evidence of ectopic neurites that result from PTPRT over-expression?

Reviewer #3 (Public Review):

This manuscript reports a novel pedigree with four intact copies of RHO on a single chromosome which appears to lead to overexpression of rhodopsin and a corresponding autosomal dominant form of RP. The authors generate retinal organoids from patient- and control-derived cells, characterize the phenotypes of the organoids, and then attempt to 'treat' aberrant rhodopsin expression/mislocalization in the patient organoids using a small molecule called photoregulin 3 (PR3). While this novel genetic mechanism for adRP is interesting, the organoid work is not compelling. There are multiple problems related to the technical approaches, the presentation of the results, and the interpretations of the data. I will present my concerns roughly in the order in which they appear in the manuscript.

Major concerns:<br /> (1) Individual human retinal organoids in culture can show a wide range of differentiation phenotypes with respect to the expression of specific markers, percentages of given cell types, etc. For this reason, it can be very difficult to make rigorous, quantitative comparisons between 'wild-type' and 'mutant' organoids. Despite this difficulty, the author of the present manuscript frequently presents results in an impressionistic manner without quantitation. Furthermore, there is no indication that the investigator who performed the phenotypic analyses was blind with respect to the genotype. In my opinion, such blinding is essential for the analysis of phenotypes in retinal organoids.

To give an example, in lines 193-194 the authors write "we observed that while the patient organoids developing connecting cilium and the inner segments similar to control organoids, they failed to extend outer segments". Outer segments almost never form normally in human retinal organoids, even when derived from 'wild-type' cells. Thus, I consider it wholly inadequate to simply state that outer segment formation 'failed' without a rigorous, quantitative, and blinded comparison of patient and control organoids.

(2) The presentation of qPCR results in Figure 3A is very confusing. First, the authors normalize expression to that of CRX, but they don't really explain why. In lines 210-211, they write "CRX, a ubiquitously expressing photoreceptor gene maintained from development to adulthood." Several parts of this sentence are misleading or incomplete. First, CRX is not 'ubiquitously expressed' (which usually means 'in all cell types') nor is it photoreceptor-specific: CRX is expressed in rods, cones, and bipolar cells. Furthermore, CRX expression levels are not constant in photoreceptors throughout development/adulthood. So, for these reasons alone, CRX is a poor choice for the normalization of photoreceptor gene expression.

Second, the authors' interpretation of the qPCR results (lines 216-218) is very confusing. The authors appear to be saying that there is a statistically significant increase in RHO levels between D120 and D300. However, the same change is observed in both control and patient organoids and is not unexpected, since the organoids are more mature at D300. The key comparison is between control and patient organoids at D300. At this time point, there appears to be no difference between control and patient. The authors don't even point this out in the main text.

Third, the variability in the number of photoreceptor cells in individual organoids makes a whole-organoid comparison by qPCR fraught with difficulty. It seems to me that what is needed here is a comparison of RHO transcript levels in isolated rod photoreceptors.

(3) I cannot understand what the authors are comparing in the bulk RNA-seq analysis presented in the paragraph starting with line 222 and in the paragraph starting with line 306. They write "we performed bulk-RNA sequencing on 300-days-old retinal organoids (n=3 independent biological replicates). Patient retinal organoids demonstrated upregulated transcriptomic levels of RHO... comparable to the qRT-PCR data." From the wording, it suggests that they are comparing bulk RNA-seq of patients and control organoids at D300. However, this is not stated anywhere in the main text, the figure legend, or the Methods. Yet, the subsequent line "comparable to the qRT-PCR data" makes no sense, because the qPCR comparison was between patient samples at two different time points, D120 and D300, not between patient and control. Thus, the reader is left with no clear idea of what is even being compared by RNA-seq analysis.

Remarkably, the exact same lack of clarity as to what is being compared is found in the second RNA-seq analysis presented in the paragraph starting with line 306. Here the authors write "We further carried out bulk RNA-sequencing analysis to comprehensively characterize three different groups of organoids, 0.25 μM PR3-treated and vehicle-treated patient organoids and control (RC) organoids from three independent differentiation experiments. Consistent with the qRT-PCR gene expression analysis, the results showed a significant downregulation in RHO and other rod phototransduction genes." Here, the authors make it clear that they have performed RNA-seq on three types of samples: PR3-treated patient organoids, vehicle-treated patient organoids, and control organoids (presumably not treated). Yet, in the next sentence, they state "the results showed a significant downregulation in RHO", but they don't state what two of the three conditions are being compared! Although I can assume that the comparison presented in Fig. 6A is between patient vehicle-treated and PR3-treated organoids, this is nowhere explicitly stated in the manuscript.

(4) There are multiple flaws in the analysis and interpretation of the PR3 treatment results. The authors wrote (lines 289-2945) "We treated long-term cultured 300-days-old, RHO-CNV patient retinal organoids with varying concentrations of PR3 (0.1, 0.25 and 0.5 μM) for one week and assessed the effects on RHO mRNA expression and protein localization. Immunofluorescence staining of PR3-treated organoids displayed a partial rescue of RHO localization with optimal trafficking observed in the 0.25 μM PR3-treated organoids (Figure 5B). None of the organoids showed any evidence of toxicity post-treatment."

There are multiple problems here. First, the results are impressionistic and not quantitative. Second, it's not clear that the investigator was blinded with respect to the treatment condition. Third, in the sections presented, the organoids look much more disorganized in the PR3-treated conditions than in the control. In particular, the ONL looks much more poorly formed. Overall, I'd say the organoids looked considerably worse in the 0.25 and 0.5 microM conditions than in the control, but I don't know whether or not the images are representative. Without rigorously quantitative and blinded analysis, it is impossible to draw solid conclusions here. Lastly, the authors state that "none of the organoids showed any evidence of toxicity post-treatment," but do not explain what criteria were used to determine that there was no toxicity.

(5) qPCR-based quantitation of rod gene expression changes in response to PR3 treatment is not well-designed. In lines 294-297 the authors wrote "PR3 drove a significant downregulation of RHO in a dose-dependent manner. Following qRT-PCR analysis, we observed a 2-to-5 log2FC decrease in RHO expression, along with smaller decreases in other rod-specific genes including NR2E3, GNAT1 and PDE6B." I assume these analyses were performed on cDNA derived from whole organoids. There are two problems with this analysis/interpretation. First, a decrease in rod gene expression can be caused by a decrease in the number of rods in the treated organoids (e.g., by cell death) or by a decrease in the expression of rod genes within individual rods. The authors do not distinguish between these two possibilities. Second, as stated above, the percentage of cells that are rods in a given organoid can vary from organoid to organoid. So, to determine whether there is downregulation of rod gene expression, one should ideally perform the qPCR analysis on purified rods.

(6) In Figure 4B 'RM' panels, the authors show RHO staining around the somata of 'rods' but the inset images suggest that several of these cells lack both NRL and OTX2 staining in their nuclei. All rods should be positive for NRL. Conversely, the same image shows a layer of cells scleral to the cells with putative RHO somal staining which do not show somal staining, and yet they do appear to be positive for NRL and OTX2. What is going on here? The authors need to provide interpretations for these findings.

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 #2 (Public Review):

Summary:<br /> In this study, Rana and colleagues present interesting findings demonstrating the potential beneficial effects of AMPA receptor modulators with ampakines in the context of the neurogenic bladder following acute spinal cord injury. Neurogenic bladder dysfunction is characterized by urinary retention and/or incontinence, with limited treatments available. Based on recent observations showing that ampakines improved respiratory function in rats with SCI, the authors explored the use of ampakine CX1739 on bladder and external urethral sphincter (EUS) function and coordination early after mid-thoracic contusion injury. Using continuous flow cystometry and EUS myography the authors showed that ampakine treatment led to decreased peak pressures, threshold pressure, intercontraction interval, and voided volume in SCI rats versus vehicle-treated controls. Although CX1739 did not alter EUS EMG burst duration, treatment did lead to EUS EMG bursting at lower bladder pressure compared to baseline. In a subset of rats that did not show regular cystometric voiding, CX1739 treatment diminished non-voiding contractions and improved coordinated EUS EMG bursting. Based on these findings the authors conclude that ampakines may have utility in recovery of bladder function following SCI.

Strengths:<br /> The experimental design is thoughtful and rigorous, providing an evaluation of both the bladder and external urethral sphincter function in the absence and presence of ampakine treatment. The data in support of a role for CX1789 treatment in the context of the neurogenic bladder are presented clearly, and the conclusions are adequately supported by the findings.

Weaknesses:<br /> Since CX1789 was administered in the context of cystometry and urethral sphincter EMG, a brief discussion of how ampakines could be used in a therapeutic context in humans would help to understand the translational significance of the work. The study lacks information on the half-life of CX1789 and how might this impact the implementation of CX1789 for clinical use. In addition, the study was limited to female rats. Lastly, given the male bias of traumatic SCI in humans, a brief discussion of this limitation is warranted.

Reviewer #3 (Public Review):

Summary:<br /> In this manuscript, Rana and colleagues examined the effect of a "low impact" ampakine, an AMPA receptor allosteric modulator, on the voiding function of rats subjected to midline T9 spinal cord contusion injury. Previous studies have shown that the micturition reflex fully depends on AMPA glutaminergic signaling, and, that the glutaminergic circuits are reorganized after spinal cord injury. In chronic paraplegic rats, other circuits (no glutaminergic) become engaged in the spinal reflex mechanism controlling micturition. The authors employed continuous flow cystometry and external urethral sphincter electromyography to assess bladder function and bladder-urethral sphincter coordination in naïve rats (control) and rats subjected to spinal cord injury (SCI). In the acute phase after SCI, rats exhibit larger voids with lower frequency than naïve rats. This study shows that CX1739 improves, in a dose-dependent manner, bladder function in rats with SCI. The interval between voids and the voided volume was reduced in rats with SCI when compared to controls. In summary, this is an interesting study that describes a potential treatment for patients with SCI.

Strengths:<br /> The findings described in this manuscript are significant because neurogenic bladder predisposes patients with SCI to urinary tract infections, hydronephrosis, and kidney failure. The manuscript is clearly written. The study is technically outstanding, and the conclusions are well justified by the data.

Weaknesses:<br /> The study was conducted 5 days after spinal cord contusion when the bladder is underactive. In rats with chronic SCI, the bladder is overactive. Therefore, the therapeutic approach described here is expected to be effective only in the underactive bladder phase of SCI. The mechanism and site of action of CX1739 is not defined.

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 #2 (Public Review):

The current manuscript by Ban et al describes that cells undergoing EMT have increased rRNA synthesis, as analyzed by RNA seq-based gene expression analysis, and that the increased rRNA synthesis provides a therapeutic opportunity to target chemoresistance. The cells utilized in this manuscript were isolated from the authors' Tri-PyMT EMT lineage tracing model published a few years ago which demonstrated that cells undergoing EMT are not the cells that are contributing to metastasis but rather to tumor chemoresistance (Fischer, Nature 2015). This in vivo model has since then been criticized for not capturing all relevant EMT events which the authors also acknowledge in the introduction. The authors therefore reason that they use this lineage tracing model to better understand the role of EMT in chemoresistance.

A major problem with the current manuscript is that the authors present many of their findings as a novel without the proper acknowledgment of previously published literature in particular, Prakash et al., Nature Communications, 2019 and Dermitt, Dev Cell, 2020. In the studies by Prakash, the authors demonstrate that maintaining ongoing rRNA biogenesis is essential for the execution of the EMT program, and thus the ability of cancer cells to become migratory and invasive. Further, Prakash et al showed that blocking rRNA biogenesis with a small molecule inhibitor, CX-5461 (which is also used in the study by Ban et al) specifically inhibits breast cancer growth, invasion, EMT, and metastasis in animal models without significant toxicity to normal tissues. As such a significant revision that is necessary at this time is a rewrite of the manuscript especially the introduction and the discussion to more accurately describe and cite previously published findings and then highlight the current work by Ban et al which nicely builds on the previously published literature as it highlights the contribution of EMT to chemoresistance rather than metastasis. The suggestion for the authors is that they therefore should focus on highlighting the chemotherapy resistance angle as their Tri-PyMT EMT lineage tracing was chosen to test this angle and as such focus on both primary tumor growth and metastasis.

Additional major revisions:<br /> The authors use the FSP1-Cre Model which in the field has been questioned as to not capture all the relevant EMT events and therefore their findings should be corroborated by another EMT model system.

In the current version of the manuscript, there are no measurements of rRNA synthesis, but the gene expression profiles are used as a proxy for rRNA synthesis. The authors therefore need to include measurements of rRNA synthesis corroborating the RNA sequencing data to support their scientific findings and claims. This can be accomplished by qPCR, Northern blot, or EU staining of the respective sorted cell population. Quantification of rRNA synthesis is also needed for the CX-5461/BMH-21 and silencing studies.

Currently, there is no mechanistic insight as to how rRNA synthesis is increased during EMT, which would also strengthen the manuscript. This could be done through targeted ChIP analysis.

rRNA synthesis has canonically been linked to the cell cycle therefore it will be necessary for the authors to determine the cell cycle state of their respective cell populations throughout the manuscript.

Statistics and quantifications are currently missing in several figures and need to be better explained throughout the manuscript to strengthen the scientific rigor of the studies.

Only metastasis studies are shown in the current version of the manuscript. These studies should be complemented with primary tumor studies as the main focus of the paper is the contribution of EMT to chemoresistance.

Reviewer #3 (Public Review):

Summary:<br /> Ban et al. investigated the role of ribosome biogenesis (RiBi) in epithelial-to-mesenchymal transition (EMT) and its contribution to chemoresistance in breast cancer. They used a Tri-PyMT EMT lineage-tracing model and scRNA-seq to analyze EMT status and found that RiBi was elevated during both EMT and mesenchymal-to-epithelial transition (MET) of cancer cells. They further revealed that nascent protein synthesis mediated by ERK and mTOR signaling pathways was essential for the completion of RiBi. Inhibiting excessive RiBi impaired EMT and MET capability. More importantly, combinatorial treatment with RiBi inhibitors and chemotherapy drugs reduced metastatic outgrowth of both epithelial and mesenchymal tumor cells. These results suggest that targeting the RiBi pathway may be an effective strategy for treating advanced breast cancer with EMT-related chemoresistance.

Strengths:<br /> The conclusions of this study are generally supported by the data. However, some weaknesses still exist as mentioned below.

Weaknesses:<br /> 1) The study predominantly focused on RiBi as a target for overcoming EMT-related chemoresistance. Thus, it will be necessary to provide some canonical outcomes after upregulating ribosome biogenesis, such as translation activity. I would suggest ribosome profiling or puromycin-incorporation assay, or other more suitable experiments.

2) The results were basically obtained from mice and in vitro experiments. While these results provide valuable insights, it will be valuable to validate part of the findings using some tissue samples from patients (e.g. RiBi activity) to determine the clinical relevance and potential therapeutic applications.

3) The results revealed that mTORC1 and ERK mediated RiBi activation. How about mTORC2? It will be informative to evaluate mTORC2 signaling.

4) The results also demonstrated promising synergic effects of Pol I inhibitor (BMH21) and chemotherapy drug (CTX) on chemo-resistant metastasis. How about using the inhibitors of mTORC1 together with CTX?

5) While the results demonstrate the potential efficacy of RiBi inhibitors in reducing metastatic outgrowth, other factors and mechanisms contributing to chemoresistance may exist and need further investigation. I would suggest some discussion about this aspect.

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.

Reviewer #2 (Public Review):

Overview:

As a report of the first structure of VMAT2, indeed the first structure of any vesicular monoamine transporter, this manuscript represents an important milestone in the field of neurotransmitter transport. VMAT2 belongs to a large family (the major facilitator superfamily, MFS) containing transporters from all living species. There is a wealth of information relating to the way that MFS transporters bind substrates, undergo conformational changes to transport them across the membrane, and couple these events to the transmembrane movement of ions. VMAT2 couples the movement of protons out of synaptic vesicles to the vesicular uptake of biogenic amines (serotonin, dopamine, and norepinephrine) from the cytoplasm. The new structure presented in this manuscript can be expected to contribute to an understanding of this proton/amine antiport process.

The structure contains a molecule of the inhibitor TBZ bound in a central cavity, with no access to either luminal or cytoplasmic compartments. The authors carefully analyze which residues interact with bound TBZ and measure TBZ binding to VMAT2 mutated at some of those residues. These measurements allow well-reasoned conclusions about the differences in inhibitor selectivity between VMAT1 and VMAT2 and differences in affinity between TBZ derivatives.

The structure also reveals polar networks within the protein and hydrophobic residues in positions that may allow them to open and close pathways between the central binding site and the cytoplasm or the vesicle lumen. The authors propose the involvement of these networks and hydrophobic residues in the coupling of transport to proton translocation and conformational changes. However, these proposals are quite speculative in the absence of supporting structures and experimentation that would test specific mechanistic details.

Critique:

Although the structure presented in this MS is clearly important, I feel that the authors have overstated several of the conclusions that can be drawn from it. I don't agree that the structure clearly indicates why TBZ is a non-competitive inhibitor; the proposal that specific hydrophobic residues function as gates will depend on lumen- and cytoplasm-facing structures for verification; the polar networks could have any number of functions - indeed it would be surprising if they were all involved in proton transport. Several of these issues could be resolved by a clearer illustration of the data, but I believe that a more rigorous description of the conclusions and where they fall between firm findings and speculation would help the reader put the results in perspective.

Non-competitive inhibition occurs when the action of an inhibitor can't be overcome by increasing substrate concentration. The structure shows TBZ sequestered in the central cavity with no access to either cytoplasm or lumen. The explanation of competitive vs non-competitive inhibition depends entirely on how TBZ got there. If it is bound from the cytoplasm, cytoplasmic substrate should have been able to compete with TBZ and overcome the inhibition. If it is bound from the lumen, or from within the bilayer, cytoplasmic substrate would not be able to compete, and inhibition would be non-competitive. The structure does not tell us how TBZ got there, only that it was eventually occluded from both aqueous compartments and the bilayer.

The issue of how VMAT2 opens access to the central binding site from luminal and cytoplasmic sides is an important and interesting one, and comparison with other MFS structures in cytoplasmic-open or extracellular/luminal-open is a very reasonable approach. However, any conclusions for VMAT2 should be clearly indicated as speculative in the absence of comparable open structures of VMAT2. As a matter of presentation, I found the illustrations in ED Fig. 6 to be less helpful than they could have been. Specifically, illustrations that focus on the proposed gates, comparing that region of the new structure with the corresponding region of either VGLUT or GLUT4 would better help the reader to compare the position of the proposed gate residues with the corresponding region of the open structure. I realize that is the intended purpose of ED Fig. 6b and 6c, but currently, those show the entire protein, and a focus on the gate regions might make the proposed gate movements clearer. I also appreciate the difference between the Alphafold prediction and the new structure, but I'm not convinced that ED Fig. 6a adds anything helpful.

The polar networks described in the manuscript provide interesting possibilities for interactions with substrates and protons whose binding to VMAT2 must control conformational change. Aside from the description of these networks, there is little evidence presented to assess the role of these networks in transport. Are the networks conserved in other closely related transporters? How could the interaction of the networks with substrate or protons affect conformational change? Of course, any potential role proposed for the networks would be highly speculative at this point, and any discussion of their role should point out their speculative nature and the need for experimental verification. Some speculation, however, can be useful for focusing the field's attention on future directions. However, statements in the abstract (three distinct polar networks... play a role in proton transduction.) and the discussion (...are likely also involved in mediating proton transduction.) should be clearly presented as speculation until they are validated experimentally.

The strongest aspect of this work (aside from the structure itself) is the analysis of TBZ binding. There is a problematic aspect to this analysis. The discussion on how TBZ stabilizes the occluded conformation of VMAT2 is premature without structures of apo-VMAT2 and possibly structures with other ligands bound. We don't really know at this point whether VMAT2 might be in the same occluded conformation in the absence of TBZ. Any statements regarding the effect of interactions between VMAT2 and TBZ depend on demonstrating that TBZ has a conformational effect. The same applies to the discussion of the role of W318 on conformation and to the loops proposed to "occlude the luminal side of the transporter" (line 131).

The description of VMAT2 mechanism makes many assumptions that are based on studies with other MFS transporters. Rather than stating these assumptions as fact (VMAT2 functions by alternating access...), it would be preferable to explain why a reader should believe these assumptions. In general, this discussion presents conclusions as established facts rather than proposals that need to be tested experimentally.

The MD simulations are not described well enough for a general reader. What is the significance of the different runs? ED Fig. 4d is not high enough resolution to see the details.

Reviewer #3 (Public Review):

Summary:

The vesicular monoamine transporter is a key component in neuronal signaling and is implicated in diseases such as Parkinson's. Understanding of monoamine processing and our ability to target that process therapeutically has been to date provided by structural modeling and extensive biochemical studies. However, structural data is required to establish these findings more firmly.

Strengths:

Dalton et al resolved a structure of VMAT2 in the presence of an important inhibitor, tetrabenazine, with the protein in detergent micelles, using cryo-EM and with the aid of domains fused to its N- and C-terminal ends. The resolution of the maps allows clear assignment of the amino acids in the core of the protein. The structure is in good agreement with a wealth of experimental and structural prediction data and provides important insights into the binding site for tetrabenazine and selectivity relative to analogous compounds.

Weaknesses:

The authors follow up their structures with molecular dynamics simulations. The simulations resulted in repositioning of the ligand, which does not seem to be well founded, and raises questions about the methodological choices made for the simulations.

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 #2 (Public Review):

Summary:<br /> The authors aimed to identify the neural sources of behavioral variation in a decision between odor and air, or between two odors.

Strengths:<br /> -The question is of fundamental importance.<br /> -The behavioral studies are automated, and high-throughput.<br /> -The data analyses are sophisticated and appropriate.<br /> -The paper is clear and well-written aside from some strong wording.<br /> -The figures beautifully illustrate their results.<br /> -The modeling efforts mechanistically ground observed data correlations.

Weaknesses:<br /> -The correlations between behavioral variations and neural activity/synapse morphology are (i) relatively weak, (ii) framed using the inappropriate words "predict", "link", and "explain", and (iii) sometimes non-intuitive (e.g., PC 1 of neural activity).<br /> -No attempts were made to perturb the relevant circuits to establish a causal relationship between behavioral variations and functional/morphological variations.

Reviewer #3 (Public Review):

Churgin et. al. seeks to understand the neural substrates of individual odor preference in the Drosophila antennal lobe, using paired behavioral testing and calcium imaging from ORNs and PNs in the same flies, and testing whether ORN and PN odor responses can predict behavioral preference. The manuscript's main claims are that ORN activity in response to a panel of odors is predictive of the individual's preference for 3-octanol (3-OCT) relative to clean air, and that activity in the projection neurons is predictive of both 3-OCT vs. air preference and 3-OCT vs. 4-methylcyclohexanol (MCH). They find that the difference in density of fluorescently-tagged brp (a presynaptic marker) in two glomeruli (DC2 and DM2) trends towards predicting behavioral preference between 3-oct vs. MCH. Implementing a model of the antennal lobe based on the available connectome data, they find that glomerulus-level variation in response reminiscent of the variation that they observe can be generated by resampling variables associated with the glomeruli, such as ORN identity and glomerular synapse density.

Strengths:<br /> The authors investigate a highly significant and impactful problem of interest to all experimental biologists, nearly all of whom must often conduct their measurements in many different individuals and so have a vested interest in understanding this problem. The manuscript represents a lot of work, with challenging paired behavioral and neural measurements.

Weaknesses:<br /> The overall impression is that the authors are attempting to explain complex, highly variable behavioral output with a comparatively limited set of neural measurements. Given the degree of behavioral variability they observe within an individual (Figure 1- supp 1) which implies temporal/state/measurement variation in behavior, it's unclear that their degree of sampling can resolve true individual variability (what they call "idiosyncrasy") in neural responses, given the additional temporal/state/measurement variation in neural responses. The statistical analyses in the manuscript are underdeveloped, and it's unclear the degree to which the correlations reported have explanatory (causative) power in accounting for organismal behavior.

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 #2 (Public Review):

Erbacher et al. have used new techniques to explore the neuro-cutaneous structures of human epidermis, which is a valuable goal given the lack of in-depth studies in human skin. Human skin is less studied than rodent skin because it presents challenges in obtaining samples and finding excellent immunohistological labels. They have employed expansion microscopy and super resolution array tomography for histological studies and have developed a human keratinocyte and human iPSC-derived sensory neuron co-culture. The authors have used these techniques to investigate the relation of intraepidermal nerve fibers (IENF) and keratinocytes, as well as to probe the localization of connexin 43. The data offer some anatomical insights, but as is does not add to our understanding of keratinocyte-neuron coupling.

Strengths:<br /> This paper is applying newer techniques to probe structure in human skin and establishes some useful immunohistochemical labels to do this, which sets up a foundation that will be valuable for future studies. The observation that IENF sometimes tunnel through keratinocytes is interesting, and the manuscript does show that Cx43 hemichannels are localized near IENF. Their data definitely represents a technical achievement, as these studies are challenging.

Weaknesses:<br /> Throughout the paper, the authors imply that they make discoveries that shed light on neuro-cutaneous interactions, but the data in this manuscript do not offer any functional insight into connections between IENF and keratinocytes. For example, the final figure legend indicates they have found evidence of "electrical and chemical synapse-like contacts to nerve fibers" (Figure 9), but no such evidence was shown. Only a single neuron vesicular marker (synaptophysin) was shown to localize to neurons in culture, as expected. They also "...propose a crucial role of nerve fiber ensheathment and Cx43-based keratinocyte-fiber contacts in neuropathic pain and small fiber pathology." but do not show any data regarding the contribution of their anatomical findings to sensory function.

Their data do show that IENF are anatomically closely apposed to keratinocytes, but this is inevitable given their location in the epidermis. The expression of Cx43 in human epidermis is also known (PMID: 7518858) and localizing Cx43 plaques near IENF does not add to current knowledge, as wide expression in keratinocytes naturally positions them near the embedded IENF. There is no indication whether IENF also expresses Cx43 to form gap junctions. Moreover, due to the lack of quantification, it is not clear whether Cx43 labeling is enriched at IENF sites as compared to other areas on the keratinocytes.

The authors' implication that their anatomical data offers insight into neuro-cutaneous functional coupling is a leap that is evident throughout the manuscript.

Reviewer #3 (Public Review):

This paper offers a fundamental advance in our understanding of communication between human sensory neurons and keratinocytes in the skin of humans. The work, which used EM and expansion microscopy, shows that axons tunnel through keratinocytes and form gap junctions along the axon as it passes by or potentially where it is ensheathed by the cell. This is a fairly remarkable arrangement and is seen both in vivo and in vitro.

The major strengths are the quality of the imaging, the use of expansion microscopy to reveal new anatomical information and the new insight the detailed work offers to our understanding of sensory neuroscience. Another major strength is that the work was done in humans, and using human cells in vitro. I think the authors have achieved their goal of thoroughly characterizing this interesting interaction between sensory neurons and keratinocytes. The obvious next step is to understand if these interactions become pathological in neuropathies.

I do think there are some weaknesses that should be addressed, and some questions that are outstanding that the authors might want to discuss. Chief amongst these is the question of what types of sensory neurons form these contacts with keratinocytes and do these change in clinical neuropathies. A more thorough discussion of these issues for future investigation would help to place the findings in the broader context of the field, in my opinion.

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 #2 (Public Review):

Results from these experiments confirm the role of TRP channels but raise serious doubts that HCN channels contribute to the light response, refuting the findings of an influential paper that appeared in Cell (Jiang et al., 2018). Instead, a major role for T-type voltage-gated Ca2+channels is suggested. Together, these results further clarify our understanding of intrinsic photosensitivity in ganglion cells. However, there are several technical issues that need to be clarified before the major claims of this paper are justified.

Reviewer #3 (Public Review):

This important body of work aims at identifying the divergent phototransduction pathways in different subtypes of melanopsin-expressing retinal ganglion cells. The authors use a combination of patch-clamp recordings of three subtypes of ipRGCs M1, M2, and M4, and their post hoc rigorous identification. The authors demonstrate that within their conditions of recordings and the choice of light stimulus recorded ipRGCs subtypes do not signal via HCN channels as previously proposed; and that M1 signal via TRPC channel, M2 signal via TRPC, or a newly identified T-Type Ca2+ channel. While the data seem to support the authors' claims that HCN channels are not involved in phototransduction pathways of ipRGCs here, the light stimulus used is different than in the previous study (Jing et al, 2018) which contradicts this claim. This opens up questions on whether this inconsistency originates in differences in light stimulus used in these studies or something else.

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 #2 (Public Review):

The manuscript by Chi, et al., mainly investigated the mutational characteristics of ctDNA, ctDNA-related markers in metastasis triple-negative breast cancer (mTNBC). They evaluated the translational value of ctDNA in predicting the prognosis and monitoring the treatment response of patients with mTNBC. Overall, this study is interesting and decent with great clinical significance.

Reviewer #3 (Public Review):

The manuscript by Chi et al investigated the value of ctDNA for predicting the prognosis and monitoring the treatment response in mTNBC patients. They found that patients with ctDNA+, had a shorter progression-free survival (PFS) than ctDNA− patients (5.16 months vs. 9.05 months, P = 0.001) and ctDNA+ was independently associated with a shorter PFS (HR, 95%CI: 2.67, 1.2-5.96; P = 0.016) by multivariable analyses. This study provides novel insight into the mutational landscape of mTNBC and may reliably predict the prognosis and treatment response of mTNBC patients. Overall, this study is interesting and important.

Strengths<br /> This study is well designed and novel.

Weaknesses<br /> This is a single-center study. Future studies may further validate the findings in other centers.

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 #2 (Public Review):

In this study authors study how OFP operates in control healthy humans and people that suffered of lesions of the OFP. Authors used a variation of the local vs. global oddball paradigm to study different levels of regularity violations. Overall the data is very interesting and having the study based on healthy and lesion humans make the results much more valuable than, other studies on healthy subject or even in animal studies.

However, the current version of the manuscript is overall very long and verbose, for example, the introduction is 5 pages long and includes up to 102 references. In my view this is way too much. I suppose authors wish to be very detailed, but somehow they get an opposite effect, the main message of the introduction and aims get diluted.

I wonder if the presentation rate used, SOA; 150 is too fast and the stimuli too short 50 ms. Please prove a rationale for this. Also, one of the conditions is 'omissions', but results are not reported, so either authors do not mention this at all, or they report these data, which would be probably interesting.<br /> The results are complex themselves and difficult to follow for a non-specialist in the field and there is not much to simplify here, but again, the Discussion is very long and in some aspect even too speculative. For example, in the conclusions authors claim that the OFC contributes to a top-down predictive process that modulates the deviance detection system in the primary auditory cortices and may be involved in connecting PEs at lower hierarchical areas with predictions at higher areas. I am not sure the current data support this. This would-be probably more appropriate if they could compare results from OFP and AC etc. so it is a more dynamic study.

At the beginning of Discussion, the authors mention that overall, these findings provide novel information about the role of the OFC in detecting violation of auditory prediction at two levels of stimuli abstraction/time scale. I think this needs to be detailed more specifically rather than mention they provide novel results

I am not sure I like to have a section as a general discussion within the discussion itself, probably this heading should be reformatted to be more specific to what is discussed.

In sum, while I find that this paper is potentially very interesting, it needs to be recast and shortened to make it more direct and appealing.

Reviewer #3 (Public Review):

This study reports how human OFC lesions impact neural responses to sounds that are surprising with respect to local (sequences of sounds) and global expectations (sequences of sequences). The authors have used a clever global-local paradigm that dissociates hierarchical levels of expectations. The results are interpreted under the framework of predictive coding. A comparison with healthy controls and a group of lateral prefrontal cortex patients highlights the specific role of OFC in the reported effects.

Strengths

This study is methodologically sound, employing the well-established global-local paradigm and a set of classical event related analyses to disentangle different types of auditory expectations and answer the research question. The use of EEG in OFC patients provides causal evidence linking this area with altered evoked responses. Furthermore, the comparison with another lesion group (lateral PFC) provides evidence for a specific role of the OFC in the reported effects. The study contributes an interesting piece of evidence and does a good job placing the findings in the landscape of the relevant literature.

Weaknesses

The central claim of the study is that hierarchical predictive processing is altered in OFC patients. However, OFC patients were able to identify global deviants as well as controls. Thus, hierarchical predictive processing itself seems to be unaltered, even though its neural correlates were different. This begs the question of what exactly the functional meaning of the EEG findings is. From the evidence presented this is difficult to determine for three reasons.

First, it is possible that the shifts in scalp potentials are due to volume conduction differences linked to post-lesion changes in neural tissue and anatomy rather than differences in information processing per se. Second, it is unclear from the analyses whether the P3a amplitude differences are true amplitude differences or a byproduct of latency differences. The reason is that the statistical method used (cluster based permutations) might yield significant effects when the latency of a component is shifted, even if peak amplitudes are the same. Complementary analyses on mean or peak amplitudes could resolve this issue.

The third reason is that the MMN, P3a and P3b components are difficult to map to the hierarchical PC theory. Traditionally, the MMN is ascribed to lower level processing while P3a and P3b are ascribed to higher level processing. However, the picture is more complicated. For example, the current results show that the MMN is enhanced in local + global surprise while the P3a is elicited by local surprise. Furthermore, the P3a is classically interpreted as reflecting attention reorientation and the P3b as reflecting the conscious detection of task-relevant targets. How attention and conscious awareness fit in hierarchical PC is not entirely clear. Moreover, the fact that lateral PFC patients show unaltered neural responses contradicts prominent views from PC identifying this region as a generator of the MMN and a source of predictions sent to temporal auditory areas.

For these reasons, a more critical view on the extent to which the findings support hierarchical predictive coding is needed.

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 #2 (Public Review):

In this manuscript, Lu et al. aimed to identify and characterize how cyclin D1 is ubiquitinated and degraded through Cullin-E3 ligases in addition to the well-documented CUL1/7-F-box proteins (Fbxw8, Fbx4, and Fbx031). The authors first confirmed that in addition to CUL1/7, all seven Cullin proteins (CUL1, 2,3, 4A, 4B, 5, and 7) are required for cyclin D1 degradation via overexpression or siRNA-mediated knockdown approach. Next, these seven Cullin proteins are validated as critical factors for cyclin D1 ubiquitination and proteosome-mediated degradation via a phosphorylation-dependent mechanism. A siRNA library of 154 e3 ligases was screened to identify 24 E3 ligases for cyclin D1 degradation, five of which (Fbxw8, Keap1, DDB2, WSB2, and Rbx1) were selected for further analysis. Functional validation and characterization analyses have shown that Keap1, DDB2, WSB2, and Rbx1 interact with cyclin D1, and that Wild Type but not mutant version of Keap1, DDB2, WSB2, and Rbx1 induces cyclin D1 ubiquitination and degradation. Finally, these cullin-E3 ligases-mediated cyclin D1 degradation is important for cell cycle progression, DNA replication, and cell viability.

Although the experimental design is overall sound and the presentation of the data is great, some major weaknesses (see details below) dampen the rigor of the study and overall claim.

Major weaknesses:<br /> 1) The biggest weakness of the manuscript is the lack of appropriate explanation and interpretation of these observed cyclin D1 ubiquitination and degradation by at least five different combinations of Cullin-E3 ligases. Are all the five cullin-E3 combinations exclusive and/or redundant to each other for cyclin D1 ubiquitination? What are the speculations in terms of the underlying mechanism? At least a working model should be included to better interpret the data.

2) Although a phosphorylation-mutant cyclin D1 (i.e., T286) was included in the manuscript, there is no Lysine residue mutant within cyclin D1 identified and characterized for the critical function of cyclin D1 ubiquitination.

3) The significance of these different Cullin 1-7 and associated E3 ligases (Keap1-CUL3, DDB2-CUL4A/4B, WSB2-CUL2/5, and RBX1-CUL1-7) in cyclin D1 ubiquitination is mainly determined by siRNA-mediated knockdown or overexpression of target cullin/E3 proteins. However, it is not clear whether the observed phenotypes of cyclin D1 are due to these cullin-E3 ligases directly or indirectly. In vitro ubiquitination assay with E1, E2, and E3 should be performed to demonstrate whether recombinant cyclin D1 is ubiquitinated.

Reviewer #3 (Public Review):

Lu, Zhang et al. utilize siRNA-mediated depletion and ectopic expression to show that CUL1-7, the scaffold proteins of CRLs, control levels of ectopically expressed cyclin D1, but not a phosphorylation deficient cyclin D1 variant (T286A) in HEK293 cells. This process occurs in a proteasome-dependent manner. Through an siRNA screen for CRL substrate adaptors in NIH3T3 cells, using a previously established Cyclin D1 activity reporter, the authors then identify the CRL adaptors KEAP1 (CRL3), DDB2 (CRL4A/B), and WSB2 (CRL2/5) as new candidate regulators of cyclin D1. They provide evidence that these CRL substrate adaptors, when ectopically expressed, co-immunoprecipitate with endogenous cyclin D1 and induce ubiquitylation and proteasomal degradation of ectopically expressed cyclin D1 in HEK293 cells. In addition, through siRNA depletion and CHX chase assays, the authors provide evidence that KEAP1, DDB2, and WSB2 are regulating the half-life of endogenous cyclin D1 in HEK293 cells. Finally, experiments in HCT-116 cells that ectopic expression of KEAP1, DDB2, and WSB2, inhibit cell growth in cells stably expressing exogenous cyclin D1, but not a phosphorylation deficient cyclin D1 variant (T286A). From these results, the authors conclude that cyclin D1 degradation in cells is mediated by multiple CRLs.

Strength:<br /> This study identifies new candidate regulators of cyclin D1 protein levels KEAP1, DDB2, and WSB2.

Weaknesses:<br /> While this study provides evidence that KEAP1, DDB2, and WSB2 are candidate regulators of cyclin D1 protein levels, the co-IP experiments and CHX chases lack important controls or are not convincing. More importantly, there are no experiments demonstrating that cyclin D1 is directly ubiquitylated by these substrate adaptors in the context of their respective CRL complexes, the main conclusion of this short report. Another major weakness is the omission of recent studies that demonstrate that the major E3 ligase degrading cyclin D(1-3) is CRL4-AMBRA1 (Simoneschi et al., Nature 2021; Maiani et al., Nature 2021; Chaikovsky et al., Nature 2021). In these studies, three independent groups taking complementary approaches show that in several cell lines and contexts CRL4-AMBRA1 is the only ligase degrading cyclin D and other cullins and substrate adaptors have little to no effect. While these data do not rule out the existence of other CRLs regulating cyclin D, they raise the question of under which conditions and in which cell lines other CRLs would be important for cyclin D degradation, a question that is not addressed or discussed.

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 #2 (Public Review):

The preliminary cohort study has provided the efficacy and safety profile of immunotherapy combined with SBRT and cytotoxic chemotherapy, and the data are solid to support the findings, which could serve as evidence for future basic research and larger scale randomized control trials. While the major innovation of this study concentrates on immunotherapy, the description of specific issues regarding immunotherapy should be strengthened and more detailed.

Reviewer #3 (Public Review):

The exploratory cohort study examined the efficacy and safety of immunotherapy in combination with SBRT and cytotoxic chemotherapy. The results are well supported by the data, which may be used as justification for further fundamental investigation and larger-scale randomized control trials. Although immunotherapy is the focus of this study's main innovation, a stronger and more thorough discussion of specific immunotherapy-related difficulties is necessary.

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 #2 (Public Review):

The analysis of bundle morphology using both confocal and SEM imaging is a strength of the paper and the authors have some nice images, especially with SEM. Still, the main weakness is that it is unclear how significant their findings are in terms of understanding bundle development; the mouse phenotypes are not distinct enough to make it clear that they serve different functions so the reader is left wondering what the main takeaway is.

In Figure 1 and 3, changes in bundle morphology clearly don't occur until after P5. Widening still occurs to some extent but lengthening does not and instead the stereocilia appear to shrink in length. EPS8 levels appear to be the most reduced of all the tip proteins (Srf mutants) so I wonder if these mutants are just similar to an EPS8 KO if the loss of EPS8 occurred postnatally (P0-P5).

A major shortcoming is that there are few details on how the image analyses were done. Were SEM images corrected for shrinkage? How was each of the immunocytochemistry quantitation (e.g., cuticular plates for phalloidin and tip staining for antibodies) done? There are multiple ways of doing this but there are few indications in the manuscript.

The tip protein analysis in Figs 2 and 4 is nice but it would be nice for the authors to show the protein staining separately from the phalloidin so you could see how restricted to the tips it is (each in grayscale). This is especially true for the CNN2 labeling in Fig 7 as it does not look particularly tip specific in the x-y panels. It would be especially important to see the antibody staining in the reslices separate from phalloidin.

In Fig 6, why was the transcriptome analysis at P2 given that the phenotype in these mice occurs much later? While redoing the transcriptome analysis is probably not an option, an alternative would be to show more examples of EPS8/GNAI/CNN2 staining in the KO, but at younger ages closer to the time of PCR analysis, such as at P5. Pinpointing when the tip protein intensities start to decrease in the KOs would be useful rather than just showing one age (P10).

While it is certainly interesting if it turns out CNN2 is indeed at tips in this phase, the experiments do not tell us that much about what role CNN2 may be playing. It is notable that in Fig 7E in the control+GFP panel, CNN2 does not appear to be at the tips. Those images are at P11 whereas the images in panel A are at P6 so perhaps CNN2 decreases after the widening phase. An important missing control is the Anc80L65-Cnn2 AAV in a wild-type cochlea.

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 #2 (Public Review):

In this article Zhang et al. report that the Histone Deacetylase-3 (HDAC3) is highly expressed in mouse pDC and that pDC development is severely affected both in vivo and in vitro when using mice harbouring conditional deletion of HDAC3. However, pDC numbers are not affected in Hdac3fl/fl Itgax-Cre mice, indicating that HDCA3 is dispensable in CD11c+ late stages of pDC differentiation. Indeed, the authors provide wide experimental evidence for a role of HDAC3 in early precursors of pDC development, by combining adoptive transfer, gene expression profiling and in vitro differentiation experiments. Mechanistically, the authors have demonstrated that HDAC3 activity represses the expression of several transcription factors promoting cDC1 development, thus allowing the expression of genes involved in pDC development. In conclusion, these findings reveals HDAC3 as a key epigenetic regulator of the expression of the transcription factors required for pDC vs cDC1 developmental fate.

These results are novel and very promising. However, supplementary information and eventual further investigations are required to improve the clarity and the robustness of this article.

Major points<br /> 1) The gating strategy adopted to identify pDC in the BM and in the spleen should be entirely described and shown, at least as a Supplementary Figure. For the BM the authors indicate in the M & M section that they negatively selected cells for CD8a and B220, but both markers are actually expressed by differentiated pDC. However, in the Figures 1 and 2 pDC has been shown to be gated on CD19- CD11b- CD11c+. What is the precise protocol followed for pDC gating in the different organs and experiments?

2) pDC identified in the BM as SiglecH+ B220+ can actually contain DC precursors, that can express these markers, too. This could explain why the impact of HDAC3 deletion appears stronger in the spleen than in the BM (Figures 1A and 2A). Along the same line, I think that it would important to show the phenotype of pDC in control vs HDAC3-deleted mice for the different pDC markers used (SiglecH, B220, Bst2) and I would suggest to include also Ly6D, taking also in account the results obtained in Figures 4 and 7. Finally, as HDCA3 deletion induces downregulation of CD8a in cDC1 and pDC express CD8a, it would important to analyse the expression of this marker on control vs HDAC3-deleted pDC.

3) How do the authors explain that in the absence of HDAC3 cDC2 development increased in vivo in chimeric mice, but reduced in vitro (Figures 2B and 2E)? More generally, as reported also by authors (line 207), the reconstitution with HDAC3-deleted cells is poorly efficient. Although cDC seem not to be impacted, are other lymphoid or myeloid cells affected? This should be expected as HDAC3 regulates T and B development, as well as macrophage function. This should be important to know, although this does not call into question the results shown, as obtained in a competitive context.

4) What are the precise gating strategies used to identify the different hematopoietic precursors in the Figure 4 ? In particular, is there any lineage exclusion performed? Moreover, what is the SiglecH+ CD11c- population appearing in the spleen of mice reconstituted with HDAC3-deleted CDP? Data shown in Figure 4F should be expressed as log2 and not10. Finally, how do the authors explain that Hdac3fl/fl express Il7r, while they are supposed to be sorted CD127- cells?

5) What is known about the expression of HDAC3 in the different hematopoietic precursors analysed in this study? This information is available only for a few of them in Supplementary Figure 1. If not yet studied, they should be addressed.

6) It would be highly informative to extend CUT and Tag studies to Irf8 and Tcf4, if this is technically feasible.

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.

Reviewer #2 (Public Review):

In this manuscript, Yu and colleagues profile the lysosome content in C. elegans. They implement lysosome immunoprecipitation (Lyso-IP) for C. elegans and they convincingly show that this method successfully isolates lysosomes from whole worms. The authors find that the lysosomes of worms overexpressing the lysosomal lipase lipl-4 are enriched for AMPK subunits and nucleoporins and that these proteins are required for the longevity of lipl-4 overexpressing worms. The authors also show that this is specific to this longevity pathway given that another long-lived worm strain (daf-2) does not exhibit enrichment for nucleoporins nor does it require them for longevity. The authors go on to express the Lyso-IP tag in different tissues of C. elegans (muscle, hypodermis, intestine, neurons) and identify the tissue-specific lysosome proteomes. Finally, the authors use this method to identify lysosome proteins in mature lysosomes and they find new proteins that regulate lysosomal acidification.

The authors present a powerful tool to unbiasedly identify lysosome-associated proteins in C. elegans, and they provide an in-depth assessment of how this method can be used to understand longevity pathways and identify novel proteins. Understanding lysosomal differences in specific tissues or in response to different longevity conditions are exciting as it provides new insight into how organelles could control specific homeostasis responses. This tool and proteomics datasets also represent a great resource for the C. elegans community and should pry open new studies on the regulation and role of the lysosome at the organismal level.

Addressing the following suggestions would help strengthen this already strong manuscript. First, it would be helpful to validate selected candidates from the tissue-specific Lyso-IP to verify that the protocol is still specific with lower sample amounts. Second, it would be helpful to provide more details on the methods, notably for sample preparation and analysis, so that it can serve as a guideline for the community. Third, the manuscript contains a lot of data and conditions, which is great, but they may also feel disconnected in some cases and it could be helpful to focus the study on the main key findings.

Reviewer #3 (Public Review):

The manuscript by Ji et al dissects the important role of lysosomes in cellular metabolism and signaling and their regulation by various associated proteins. The authors utilized deep proteomic profiling in C.Elegans to identify lysosome-associated proteins involved in regulating longevity and discovered the recruitment of AMPK and nucleoporin proteins in response to increased lysosomal lipolysis. Additionally, the authors found lysosomal heterogeneity across different tissues and specific enrichment of the Ragulator complex on Cystinosin-positive lysosomes.

Strengths of this work include the utilization of deep proteomic profiling to identify novel lysosome-associated proteins involved in longevity regulation, as well as the discovery of lysosomal heterogeneity and specific protein enrichments across different worm tissues. These findings point to a complex interplay between lysosomal protein dynamics, signal transduction, organelle crosstalk, and organism longevity.

One weakness of this work may be the limited scope of the study, as it focuses primarily on the identification and characterization of lysosome-associated proteins involved in longevity regulation, with limited mechanistic follow-up and some unsubstantiated claims.

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 #2 (Public Review):

This work investigates the possible association between language experience and morphology of the superior temporal cortex, a part of the brain responsible for the processing of auditory stimuli. Previous studies have found associations between language and music proficiency as well as language learning aptitude and cortical morphometric measures in regions in the primary and associated auditory cortex. These studies have most often, however, focused on finding neuroanatomical effects of difference between features in a few (often two) languages or from learning single phonetic/phonological features and have often been limited in terms of N. On this background, the authors use more sophisticated measures of language experience that take into account the age of onset and the differences in phonology between languages the subjects have been exposed to as well as a larger number of subjects (N = 146 + 69) to relate language experience to the shape and structure of the superior temporal cortex, measured from T1-weighted MRI data. It shows solid evidence for there being a negative relationship between language experience and the right 2nd transverse temporal gyrus as well as some evidence for the relationship representing phoneme-level cross-linguistic information.

Strengths<br /> The use of entropy measures to quantify language experience and include typological distance measures allows for a more general interpretation of the results and is an important step toward respecting and making use of linguistic diversity in neurolinguistic experiments.

A relatively large group of subjects with a range of linguistic backgrounds.

The full analysis of the structure of the superior temporal cortex including cortical volume, area, as well as the shape of the transverse gyrus/gyri. There is a growing literature on the meaning of the shape and number of the transverse gyri in relation to language proficiency and the authors explore all measures given the available data.

The authors chose to use a replication data set to verify their data, which is applaudable. However, see the relevant point under "Weaknesses".

Weaknesses<br /> The authors fail to explain how a thinner cortex could reflect the specialization of the auditory cortex in the processing of diverse speech input. The Dynamic Restructuring Model (Pliatsikas, 2020) which is referred to does not offer clear guidance to interpretation. A more detailed discussion of how a phonologically diverse environment could lead to a thinner cortex would be very helpful.

It is difficult to understand what measure of language experience is used when. Clearer and more explicit nomenclature would assist in the interpretation of the results.

There is a lack of description of the language backgrounds of the included subjects. How many came from each of the possible linguistic backgrounds? How did they differ in language exposure? This would be informative to evaluate the generalizability of the conclusions.

Only the result from the multiple transverse temporal gyri (2nd TTG) is analyzed in the replicated dataset. Only the association in the right hemisphere 2nd TTG is replicated but this is not reflected in the discussion or the conclusions. The positive correlation in the right TTG is thus not attempted to be replicated.

The replication dataset differed in more ways than the more frequent combination of English and German experience, as mentioned in the discussion. Specifically, the fraction of monolinguals was higher in the replication dataset and the samples came from different scanners. It would be better if the primary and replication datasets were more equally matched.

Even if the language experience and typological distance measures are a step in the right direction for correctly associating language exposure with cortical plasticity, it still is a measure that is insensitive to the intensity of the exposure. The consequences of this are not discussed.

Reviewer #3 (Public Review):

Summary:<br /> The study uses structural MRI to identify how the number, degree of experience, and phonemic diversity of language(s) that a speaker knows can influence the thickness of different sub-segments of the auditory cortex. In both a primary and replication sample of adult speakers, the authors find key differences in cortical thickness within specific subregions of the cortex due to either the age at which languages are acquired (degree of experience), or the diversity of the phoneme inventories carried by that/those language(s) (breadth of experience).

Strengths:<br /> The results are first and foremost quite fascinating and I do think they make a compelling case for the different ways in which linguistic experience shapes the auditory cortex.

The study uses a number of different measures to quantify linguistic experience, related to how many languages a person knows (taking into account the age at which each was learned) as well as the diversity of the phoneme inventories contained within those languages. The primary sample is moderately large for a study that focuses on brain-behaviour relationships; a somewhat smaller replication sample is also deployed in order to test the generality of the effects.

Analytic approaches benefit from the careful use of brain segmentation techniques that nicely capture key landmarks and account for vagaries in the structure of STG that can vary across individuals (e.g., the number of transverse temporal gyri varies from 1-4 across individuals).

Weaknesses:<br /> The specificity of these effects is interesting; some effects really do appear to be localized to the left hemisphere and specific subregions of the auditory cortex e.g., TTG. However because analyses only focus on auditory regions along the STG and MTG, one could be led to the conclusion that these are the only brain regions for which such effects will occur. The hypothesis is that these are specifically auditory effects, but that does make a clear prediction that non-auditory regions should not show the same sort of variability. I recognize that expanding the search space will inflate type-1 errors to a point where maybe it's impossible to know what effects are genuine. And the fine-grained nature of the effects suggests a coarse analysis of other cortical regions is likely to fail. So I don't know the right answer here. Only that I tend to wonder if some control region(s) might have been useful for understanding whether such effects truly are limited to the auditory cortex. Otherwise one might argue these are epiphenomenal or some hidden factor unrelated to auditory experience predicting that we'd also see them in the non-auditory cortex as well, either within or outside the brain's speech network(s).

The reason(s) why we might find a link between cortical thickness and experience is not fully discussed. The introduction doesn't really mention why we'd expect cortical thickness to be correlated (positively or negatively) with speech experience. There is some discussion of it in the Discussion section as it relates to the Pliatsikas' Dynamic Restructuring Model, though I think that model only directly predicts thinning as a function of experience (here, negative correlations). It might have less to say about observed positive correlations e.g., HG in the right hemisphere. In any case, I do think that it's interesting to find some relationship between brain morphology and experience but clearer explanations for why these occur could help, and especially some mention of it in the intro so readers are clearer on why cortical thickness is a useful measure.

One pitfall of quantifying phoneme overlap across languages is that what we might call a single 'phoneme', shared across languages, will, in reality, be realized differently across them. For instance, English and French may be argued to both use the vowel /u/ although it's realized differently in English vs. French (it's often fronted and diphthongized in many English speaker groups). Maybe the phonetic dictionaries used in this study capture this using a close phonetic transcription, but it's hard to tell; I suspect they don't, and in that case, the diversity measures would be an underestimate of the actual number of unique phonemes that a listener needs to maintain.

Discussion of potential genetic differences underlying the findings is interesting. One additional data point here is a study finding a relationship between the number of repeats of the READ1 (a factor of the DCDC2 gene) in populations of speakers, and the phoneme inventory of language(s) predominant in that population (DeMille, M. M., Tang, K., Mehta, C. M., Geissler, C., Malins, J. G., Powers, N. R., ... & Gruen, J. R. (2018). Worldwide distribution of the DCDC2 READ1 regulatory element and its relationship with phoneme variation across languages. Proceedings of the National Academy of Sciences, 115(19), 4951-4956.) Admittedly, that paper makes no claim about the cortical expression of that regulatory factor under study, and so more work needs to be done on whether this has any bearing at all on the auditory cortex. But it does represent one alternative account that does not have to do with plasticity/experience.

The replication sample is useful and a great idea. It does however feature roughly half the number of participants meaning statistical power is weaker. Using information from the first sample, the authors might wish to do a post-hoc power analysis that shows the minimum sample size needed to replicate their effect; given small effects in some cases, we might not be surprised that the replication was only partial. I don't think this is a deal breaker as much as it's a way to better understand whether the failure to replicate is an issue of power versus fragile effects.

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 #2 (Public Review):

The manuscript examined the behavioural and neural profile of weak and strong fear memories. The data provide strong evidence that weak but not strong fear memories are subject to extinction and reconsolidation disruption. Strong memories also show greater generalization. These differences were echoed in differential neural connectivity with weak fear memories showing greater connectivity between brains areas than strong fear memories.

The findings are of a great importance and offer insight into why resistance to extinction and reconsolidation may underlie fear-related psychopathology.<br /> The study uses key behavioural tests to study the durability of weak vs strong memories (extinction and reconsolidation) as well as studies the generalisation of those memories. These behavioural effects nicely dovetail with the neural connectivity analyses that were performed.<br /> The data presented in this paper will be the basis for future hypothesis driven examinations on the causal influence of specific pathways involved in contextual fear.<br /> Excellent use of the open field to control for motor effects.

This is a strong paper and the results support the conclusions. The findings are of broad interest and are important for future research.

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 #2 (Public Review):

In Bolumar, Moncayo-Arlandi et al. the authors explore whether endometrium-derived extracellular vesicles contribute DNA to embryos and therefore influence embryo metabolism and respiration. The manuscript combines techniques for isolating different populations of extracellular vesicles, DNA sequencing, embryo culture, and respiration assays performed on human endometrial samples and mouse embryos.

Vesicle isolation is technically difficult and therefore collection from human samples is commendable. Also, the influence of maternally derived DNA on the bioenergetics of embryos is unknown and therefore novel. However, several experiments presented in the manuscript fail to reach statistical significance, likely due to the small sample sizes. This manuscript is a good but incomplete start as to the potential function of maternal DNA transfer via vesicles.

In my opinion the manuscript supports the following of the authors' claims:

1. Different amounts of nDNA and mtDNA are shed in human endometrial extracellular vesicles during different phases of the menstrual cycle.<br /> 2. Endometrial microvesicles are more enriched for mitochondrial DNA sequences compared to other types of vesicles present in the human samples.<br /> 3. Fluorescently labelled DNA from extracellular vesicles derived from an endometrial adenocarcinoma cell line can be incorporated into hatched mouse embryos.<br /> 4. Culture of mouse embryos with endometrial extracellular vesicles can influence embryo respiration and the effect is greater when cultured with isolated exosomes compared to other isolated microvesicles.

My main concerns with the manuscript:

1. Several experiments presented fail to reach statistical significance or are qualitative.<br /> 2. The definitive experiments presented in the manuscript are limited to the transfer of DNA in general not mtDNA. Therefore a strong connection with metabolism is missing, diminishing the significance of the findings.

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 #2 (Public Review):

Pinpoint by Birman et al. serves not only as a probe trajectory planning tool but also offers a far richer suite of functionalities. It provides a simple and intuitive environment that users can learn within minutes and start planning trajectories for multiple probes based on the Allen mouse brain atlas. Pinpoint further includes two MRI-based transformations to better map the Allen atlas to live brains. It features a coefficient to adjust for different Bregma-Lambda distances and includes a mouse skull model to provide a better approximation of the craniotomy coordinates, rather than the coordinate of the point of insertion on the brain. It also offers tools to link the application to manipulator controllers to visualise the position of probes in the brain in real-time. Remarkably, most of these features are available right from the web browser, without the need to install anything or any coding knowledge.

The authors developed an open-source and well-documented software. Although I did not test it myself, it can communicate with the most common recording softwares (Open Ephys, SpikeGLX) and manipulators (New Scale, Sensapex) in the field. The current level of support by the developers on GitHub is reassuring, and I hope this continues as Pinpoint matures into a more stable and robust version.

Reviewer #3 (Public Review):

Summary:<br /> Birman and colleagues have introduced an invaluable tool designed specifically for electrophysiologists, simplifying the precise planning of trajectories for placing high-density probes within designated locations. Pinpoint offers users an interactive 3D environment within which they can explore electrophysiological trajectories within the anatomical context of the mouse brain. Within this environment, users can visualize the probe, target regions, and the constraints imposed by their experimental setup. Advanced users also have the flexibility to customize the entire Pinpoint scene to align with alternative coordinate systems and rig geometries. In cases involving multiple-probe recordings, Pinpoint shows 3D paths while issuing warnings about potential collisions. Additionally, Pinpoint can account for the individual variability in brain size among mice.

Strengths:<br /> Pinpoint provides real-time visualization of current brain region targets alongside neural data. Anatomical targeting information is accessible live during recordings. This is made possible through two sets of features: hardware that allows Pinpoint to communicate with micro-manipulators and software that broadcasts the current location of each recording channel to data acquisition software. Researchers can monitor the precise positioning of their probe during insertion and observe the anatomical locations of live electrophysiology data throughout an experiment, enabling them to make corrections if necessary.

Weaknesses:<br /> 1. Pinpoint's novelty lies in its ability to be linked to data acquisition programs and electronic micro-manipulators. However, a similar program, Neuropixels Trajectory Explorer, was released before Pinpoint with comparable features. Please refer to https://github.com/petersaj/neuropixels_trajectory_explorer. It would be beneficial to clarify the distinctions between these two applications and discuss on the necessity and advantages of creating Pinpoint.

2. Currently, in Pinpoint, users can only select one area of the mouse brain for probe placement and then use the controller to adjust the probe´s position if they wish to target multiple brain areas. This can complicate planning when inserting multiple probes. It would be advantageous to have the option to choose the specific areas the probes are to traverse, with Pinpoint automatically suggesting the most optimal trajectories while avoiding potential collisions. While this may require additional development, a comment on this possibility would be appreciated.

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 #2 (Public Review):

Summary:<br /> This is an interesting and well-written study assessing the role of dopaminergic inputs from the VTA on orexin cell responses in an opto-pavlovian conditioning task. These data are consistent with a possible role of this system in reward expectation and are surprisingly one of the first demonstrations of a role for dopamine in this phenomenon.

Strengths:

The study has used an interesting opto-Pavlovian approach combined with fibre photometry.

Weaknesses:

It is unclear what n size was used or analysed, particularly for AUC measures e.g. Figures 1 D/E and 3 G. The number of trials reflected and the animal numbers need clarification.

The study focussed on opto-stim omissions - this work would be significantly strengthened by a comparison to a real-world examination where animals are trained for a radiation reward (food pellet). Have the authors considered the role of orexin in the opposing situation i.e. a surprise addition of reward? Similarly, there remains some conjecture regarding the role of these systems in reward and aversion - have the authors considered aversive learning paradigms - fear, or fear extinction - to further explore the roles of this system? There are some (important) discussions about the possible role of orexin in negative reinforcement. Further studies to address this could be warranted.

I think some further discussion of the work by Lineman concerning the interesting bidirectional actions of d1/d2 r signalling on glutamatergic transmission onto orexin neurons is worthwhile. While this work is currently cited, the nuance and perhaps relevance to d1 and d2 signalling could be contextualised a little more (https://doi.org/10.1152/ajpregu.00150.2018).

Reviewer #3 (Public Review):

Summary:<br /> Harada and colleagues describe an interesting set of experiments characterizing the relationship between dopamine cell activity in the ventral tegmental area (VTA) and orexin neuron activity in the lateral hypothalamus (LH). All experiments are conducted in the context of an opto-Pavlovian learning task, in which a cue predicts optogenetic stimulation of VTA dopamine neurons. With training, cues that predict DA stimulation come to elicit dopamine release in LH (a similar effect is seen in accumbens). After training, omission trials (cue followed by no laser) result in a dip (inhibition) of dopamine release in LH, characteristic of reward prediction error observed in the striatum. Across cue training, the activity pattern of orexin neurons in LH mirrors that of LH DA levels. However, unlike the DA signal, orexin neurons do not exhibit a decrease in activity in omission trials. Systemic blockade of D2 but not D1 receptors blocked DA release in LH following VTA DA cell stimulation.

Strengths:<br /> Although much work has been dedicated to examining projections from orexin cells to VTA, less has been done to characterize reciprocal projections and their function. In this way, this paper is a very important addition to the literature. The experiments are technically sound (with some limitations, below) and utilize sophisticated approaches, the manuscript is nicely written, and the conclusions are mostly reasonable based on the data collected.

Weaknesses:<br /> I believe the impact of the paper could be enhanced by considering and/or addressing the following:

Major:<br /> • I encourage the authors to discuss in the Introduction previous work on DA regulation of orexin neurons. In particular, the authors cite, but do not describe in any detail, the very relevant Linehan paper (2019; Am J Physiol Regul) which shows that DA differentially alters excitatory/inhibitory input onto orexin neurons and that these actions are reversed by D1 vs D2 receptor antagonists. Another paper (Bubser, 2005, EJN) showed that dopamine agonists increase the activity of orexin neurons and that these effects are blocked by D1/D2 antagonists. The current findings should be discussed in the context of these (and any other relevant) papers in the Discussion, too.<br /> • In the Discussion, the authors provide two (plausible) explanations for why they did not observe a dip in the calcium signal of orexin neurons during omission trials. Is it not possible that these cells do not encode for this type of RPE?<br /> • Related to the above - I am curious about the authors' thoughts on why there is such redundancy in the system. i.e. why is dopamine doing the same thing in NAC and LH in the context of cue-reward learning?<br /> • The data, as they stand, are largely correlative and do not indicate that DA recruitment of orexin neurons is necessary for learning to occur. It would be compelling if blocking the orexin cell recruitment affected some behavioral outcomes of learning. Similarly - does raclopride treatment across training prevent learning?<br /> • Only single doses of SCH23390 and raclopride were used. How were these selected? It would be nice to use more of a dose range to show that 1) and effect of D1R blockade was not missed, and 2) that the reduction in orexin signal with raclopride was dose-dependent.<br /> • Fig 1C, could the effect the authors observed be due to movement? Relatedly, what was the behavior like when the cue was on? Did mice orient/approach the cue? Also, when does the learning about the cue occur? Does it take all 10 days of learning or does this learning/cue-induced increase in dopamine signaling occur in less than 10 days?<br /> • Also related to the above, could the observed dopamine signal be a result of just the laser turning on? It would seem important to include mice with a control sensor.<br /> • Fig 1E, the effect seems to be driven by one mouse which looks like it could be a statistical outlier. The inclusion of additional animals would make these data more compelling.<br /> • For Fig 1C, 3D, 3F, and 4D, could the authors please show the traces for the entire length of laser onset? It would be helpful to see both the rise and the fall of dopamine signals.<br /> • Fig 2C, could the authors comment on how they compared the AUC to baseline? Was this comparison against zero? Because of natural hills and troughs during signals prior to cue (which may not equate to a zero), comparing the omission-induced dip to a zero may not be appropriate. A better baseline might be using the signals prior to the cue.<br /> • Could the authors comment on how they came up with the 4-5.3s window to observe the AUC in Fig 3H?

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 #2 (Public Review):

The question of whether the neural mechanisms for reward and punishment learning are similar has been a constant debate over the last two decades. Numerous studies have shown that the midbrain dopamine neurons respond to both negative and salient stimuli, some of which can't be well accounted for by the classic RL theory (Delgado et al., 2007). Other research even proposed that aversive learning can be viewed as reward learning, by treating the omission of aversive stimuli as a negative PE (Seymour et al., 2004).

Although the current study took an axiomatic approach to search for the PE encoding brain regions, which I like, I have major concerns regarding their experimental design and hence the results they obtained. My biggest concern comes from the false description of their task to the participants. To increase the number of "valid" trials for data analysis, the instructed and actual probabilities were different. Under such a circumstance, testing axiom 2 seems completely artificial. How does the experimenter know that the participants truly believe that the 75% is more probable than, say, the 25% stimulation? The potential confusion of the subjects may explain why the SCR and relief report were rather flat across the instructed probability range, and some of the canonical PE encoding regions showed a rather mixed activity pattern across different probabilities. Also for the post-hoc selection criteria, why pick the larger SCR in the 75% compared to the 25% instructions? How would the results change if other criteria were used?

To test axiom 3, which was to compare the 100% stimulation to the 0% stimulation conditions, how did the actual shock delivery affect the fMRI contrast result? It would be more reasonable if this analysis could control for the shock delivery, which itself could contaminate the fMRI signal, with extra confound that subjects may engage certain behavioral strategies to "prepare for" the aversive outcome in the 100% stimulation condition. Therefore, I agree with the authors that this contrast may not be a good way to test axiom 3, not only because of the arguments made in the discussion but also the technical complexities involved in the contrast.

Reviewer #3 (Public Review):

Summary:<br /> The authors conducted a human fMRI study investigating the omission of expected electrical shocks with varying probabilities. Participants were informed of the probability of shock and shock intensity trial-by-trial. The time point corresponding to the absence of the expected shock (with varying probability) was framed as a prediction error producing the cognitive state of relief/pleasure for the participant. fMRI activity in the VTA/SN and ventral putamen corresponded to the surprising omission of a high probability shock. Participants' subjective relief at having not been shocked correlated with activity in brain regions typically associated with reward-prediction errors. The overall conclusion of the manuscript was that the absence of an expected aversive outcome in human fMRI looks like a reward-prediction error seen in other studies that use positive outcomes.

Strengths:<br /> Overall, I found this to be a well-written human neuroimaging study investigating an often overlooked question on the role of aversive prediction errors, and how they may differ from reward-related prediction errors. The paper is well-written and the fMRI methods seem mostly rigorous and solid.

Weaknesses:<br /> I did have some confusion over the use of the term "prediction-error" however as it is being used in this task. There is certainly an expectancy violation when participants are told there is a high probability of shock, and it doesn't occur. Yet, there is no relevant learning or updating, and participants are explicitly told that each trial is independent and the outcome (or lack thereof) does not affect the chances of getting the shock on another trial with the same instructed outcome probability. Prediction errors are primarily used in the context of a learning model (reinforcement learning, etc.), but without a need to learn, the utility of that signal is unclear.

An overarching question posed by the researchers is whether relief from not receiving a shock is a reward. They take as neural evidence activity in regions usually associated with reward prediction errors, like the VTA/SN. This seems to be a strong case of reverse inference. The evidence may have been stronger had the authors compared activity to a reward prediction error, for example using a similar task but with reward outcomes. As it stands, the neural evidence that the absence of shock is actually "pleasurable" is limited-albeit there is a subjective report asking subjects if they felt relief.

I have some other comments, and I elaborate on those above comments, below:

1. A major assumption in the paper is that the unexpected absence of danger constitutes a pleasurable event, as stated in the opening sentence of the abstract. This may sometimes be the case, but it is not universal across contexts or people. For instance, for pathological fears, any relief derived from exposure may be short-lived (the dog didn't bite me this time, but that doesn't mean it won't next time or that all dogs are safe). And even if the subjective feeling one gets is temporary relief at that moment when the expected aversive event is not delivered, I believe there is an overall conflation between the concepts of relief and pleasure throughout the manuscript. Overall, the manuscript seems to be framed on the assumption that "aversive expectations can transform neutral outcomes into pleasurable events," but this is situationally dependent and is not a common psychological construct as far as I am aware.

2. The authors allude to this limitation, but I think it is critical. Specifically, the study takes a rather simplistic approach to prediction errors. It treats the instructed probability as the subjects' expectancy level and treats the prediction error as omission related activity to this instructed probability. There is no modeling, and any dynamic parameters affected by learning are unaccounted for in this design. That is subjects are informed that each trial is independently determined and so there is no learning "the presence/absence of stimulations on previous trials could not predict the presence/absence of stimulation on future trials." Prediction errors are central to learning. It is unclear if the "relief" subjects feel on not getting a shock on a high-probability trial is in any way analogous to a prediction error, because there is no reason to update your representation on future trials if they are all truly independent. The construct validity of the design is in question.

3. Related to the above point, even if subjects veered away from learning by the instruction that each trial is independent, the fact remains that they do not get shocks outside of the 100% probability shock. So learning is occurring, at least for subjects who realize the probability cue is actually a ruse.

4. Bouton has described very well how the absence of expected threat during extinction can create a feeling of ambiguity and uncertainty regarding the signal value of the CS. This in large part explains the contextual dependence of extinction and the "return of fear" that is so prominent even in psychologically healthy participants. The relief people feel when not receiving an expected shock would seem to have little bearing on changing the long-term value of the CS. In any event, the authors do talk about conditioning (CS-US) in the paper, but this is not a typical conditioning study, as there is no learning.

5. In Figure 2 A-D, the omission responses are plotted on trials with varying levels of probability. However, it seems to be missing omission responses in 0% trials in these brain regions. As depicted, it is an incomplete view of activity across the different trial types of increasing threat probability.

6. If I understand Figure 2 panels E-H, these are plotting responses to the shock versus no-shock (when no-shock was expected). It is unclear why this would be especially informative, as it would just be showing activity associated with shocks versus no-shocks. If the goal was to use this as a way to compare positive and negative prediction errors, the shock would induce widespread activity that is not necessarily reflective of a prediction error. It is simply a response to a shock. Comparing activity to shocks delivered after varying levels of probability (e.g., a shock delivered at 25% expectancy, versus 75%, versus 100%) would seem to be a much better test of a prediction error signal than shock versus no-shock.

7. I was unclear what the results in Figure 3 E-H were showing that was unique from panels A-D, or where it was described. The images looked redundant from the images in A-D. I see that they come from different contrasts (non0% > 0%; 100% > 0%), but I was unclear why that was included.

8. As mentioned earlier, there is a tendency to imply that subjects felt relief because there was activity in "the reward pathway."

9. From the methods, it wasn't entirely clear where there is jitter in the course of a trial. This centers on the question of possible collinearity in the task design between the cue and the outcome. The authors note there is "no multicollinearity between anticipation and omission regressors in the first-level GLMs," but how was this quantified? The issue is of course that the activity coded as omission may be from the anticipation of the expected outcome.

10. I did not fully understand what the LASSO-PCR model using relief ratings added. This result was not discussed in much depth, and seems to show a host of clusters throughout the brain contributing positively or negatively to the model. Altogether, I would recommend highlighting what this analysis is uniquely contributing to the interpretation of the findings.

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 #2 (Public Review):

Summary<br /> The paper introduces a valuable method, tCFS, for measuring suppression depth in continuous flash suppression (CFS) experiments. tCFS uses a continuous-trial design instead of the discrete trials standard in the literature, resulting in faster, better controlled, and lower-variance estimates. The authors measured suppression depth during CFS for the first time and found similar suppression depths for different image categories. This finding provides an interesting contrast to previous results that breakthrough thresholds differ for different image categories and refine inferences of subconscious processing based solely on breakthrough thresholds. However, the paper overreaches by claiming breakthrough thresholds are insufficient for drawing certain conclusions about subconscious processing.

Strengths<br /> 1. The tCFS method, by using a continuous-trial design, quickly estimates breakthrough and re-suppression thresholds. Continuous trials better control for slowly varying factors such as adaptation and attention. Indeed, tCFS produces estimates with lower across-subject variance than the standard discrete-trial method (Fig. 2). The tCFS method is straightforward to adopt in future research on CFS and binocular rivalry.<br /> 2. The CFS literature has lacked re-suppression threshold measurements. By measuring both breakthrough and re-suppression thresholds, this work calculated suppression depth (i.e., the difference between the two thresholds), which warrants different interpretations from the breakthrough threshold alone.<br /> 3. The work found that different image categories show similar suppression depths, suggesting some aspects of CFS are not category-specific. This result enriches previous findings that breakthrough thresholds vary with image categories. Re-suppression thresholds vary symmetrically, such that their differences are constant.

Weaknesses<br /> 1. The results and arguments in the paper do not support the claim that 'variations in breakthrough thresholds alone are insufficient for inferring unconscious or preferential processing of given image categories,' to take one example phrasing from the abstract. The same leap in reasoning recurs on lines 28, 39, 125, 566, 666, 686, 759, etc.<br /> Take, for example, the arguments on lines 81-83. Grant that images are inequivalent, and this explains different breakthrough times. This is still no argument against differential subconscious processing. Why are images non-equivalent? Whatever the answer, does it qualify as 'residual processing outside of awareness'? Even detecting salience requires some processing. The authors appear to argue otherwise on lines 694-696, for example, by invoking the concept of effective contrasts, but why is effective contrast incompatible with partial processing? Again, does detecting (effective) contrast not involve some processing? The phrases 'residual processing outside of awareness' and 'unconscious processing' are broad enough to encompass bottom-up salience and effective contrast. Salience and (effective) contrast are arguably uninteresting, but that is a different discussion. The authors contrast 'image categories' or semantics with 'low-level factors.' In my opinion, this is a clearer contrast worth emphasizing more. However, semantic processing is not equal to subconscious processing writ large. The preceding does not detract from the interest in finding uniform suppression depth. Suppression depth and absolute bCFS can conceivably be due to orthogonal mechanisms warranting their own interpretations. In fact, the authors briefly take this position in the Discussion (lines 696-704, 'A hybrid model ...'). The involvement of different mechanisms would defeat the argument on lines 668-670.

2. These two hypotheses are confusing and should be more clearly distinguished: a) varying breakthrough times may be due to low-level factors (lines 76-79); b) uniform suppression depth may also arise from early visual mechanisms (e.g., lines 25-27).

Neutral remarks<br /> The depth between bCFS and reCFS depended on measurement details such as contrast change speed and continuous vs. discrete trials. With discrete trials, the two thresholds showed inverse relations (i.e., reCFS > bCFS) in some participants. The authors discuss possible reasons at some length (adaptation, attention, etc. ). Still, a variable measure does not clearly indicate a uniform mechanism.

Reviewer #3 (Public Review):

Summary:<br /> In the 'bCFS' paradigm, a monocular target gradually increases in contrast until it breaks interocular suppression by a rich monocular suppressor in the other eye. The present authors extend the bCFS paradigm by allowing the target to reduce back down in contrast until it becomes suppressed again. The main variable of interest is the contrast difference between breaking suppression and (re) entering suppression. The authors find this difference to be constant across a range of target types, even ones that differ substantially in the contrast at which they break interocular suppression (the variable conventionally measured in bCFS). They also measure how the difference changes as a function of other manipulations. Interpretation in terms of the processing of unconscious visual content, as well as in terms of the mechanism of interocular suppression.

Strengths:<br /> Interpretation of bCFS findings is mired in controversy, and this is an ingenuous effort to move beyond the paradigm's exclusive focus on breaking suppression. The notion of using the contrast difference between breaking and entering suppression as an index of suppression depth is interesting, but I also feel like it can be misleading at times, as detailed below.

Weaknesses:<br /> Here's one doubt about the 'contrast difference' measure used by the authors. The authors seem confident that a simple subtraction is meaningful after the logarithmic transformation of contrast values, but doesn't this depend on exactly what shape the contrast-response function of the relevant neural process has? Does a logarithmic transformation linearize this function irrespective of, say, the level of processing or the aspect of processing that we're talking about? Given that stimuli differ in terms of the absolute levels at which they break (and re-enter) suppression, the linearity assumption needs to be well supported for the contrast difference measure to be comparable across stimuli.

Here's a more conceptual doubt. The authors introduce their work by discussing ambiguities in the interpretation of bCFS findings with regard to preferential processing, unconscious processing, etc. A large part of the manuscript doesn't really interpret the present 'suppression depth' findings in those terms, but at the start of the discussion section (lines 560-567) the authors do draw fairly strong conclusions along those lines: they seem to argue that the constant 'suppression depth' value observed across different stimuli argues against preferential processing of any of the stimuli, let alone under suppression. I'm not sure I understand this reasoning. Consider the scenario that the visual system does preferentially process, say, emotional face images, and that it does so under suppression as well as outside of suppression. In that scenario, one might expect the contrast at which such a face breaks suppression to be low (because the face is preferentially processed under suppression) and one might also expect the contrast at which the face enters suppression to be low (because the face is preferentially processed outside of suppression). So the difference between the two contrasts might not stand out: it might be the same as for a stimulus that is not preferentially processed at all. In sum, even though the author's label of 'suppression depth' on the contrast difference measure is reasonable from some perspectives, it also seems to be misleading when it comes to what the difference measure can actually tell us that bCFS cannot.

The authors acknowledge that non-zero reaction time inflates their 'suppression depth' measure, and acknowledge that this inflation is worse when contrast ramps more quickly. But they argue that these effects are too small to explain either the difference between breaking contrast and re-entering contrast to begin with, or the increase in this difference with the contrast ramping rate. I agree with the former: I have no doubt that stimuli break suppression (ramping up) at a higher contrast than the one at which they enter suppression (ramping down). But about the latter, I worry that the RT estimate of 200 ms may be on the low side. 200 ms may be reasonable for a prepared observer to give a speeded response to a clearly supra-threshold target, but that is not the type of task observers are performing here. One estimate of RT in a somewhat traditional perceptual bistability task is closer to 500 ms (Van Dam & Van Ee, Vis Res 45 2005), but I am uncertain what a good guess is here. Bottom line: can the effect of contrast ramping rate on 'suppression depth' be explained by RT if we use a longer but still reasonable estimated RT than 200 ms?

A second remark about the 'ramping rate' experiment: if we assume that perceptual switches occur with a certain non-zero probability per unit time (stochastically) at various contrasts along the ramp, then giving the percept more time to switch during the ramping process will lead to more switches happening at an earlier stage along the ramp. So: ramping contrast upward more slowly would lead to more switches at relatively low contrast, and ramping contrast downward more slowly would lead to more switches at relatively high contrasts. This assumption (that the probability of switching is non-zero at various contrasts along the ramp) seems entirely warranted. To what extent can that type of consideration explain the result of the 'ramping rate' experiment?

When tying the 'dampened harmonic oscillator' finding to dynamic systems, one potential concern is that the authors are seeing the dampened oscillating pattern when plotting a very specific thing: the amount of contrast change that happened between two consecutive perceptual switches, in a procedure where contrast change direction reversed after each switch. The pattern is not observed, for instance, in a plot of neural activity over time, threshold settings over time, etcetera. I find it hard to assess what the observation of this pattern when representing a rather unique aspect of the data in such a specific way, has to do with prior observations of such patterns in plots with completely different axes.

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 #2 (Public Review):

Summary:<br /> The authors analyze how individual amacrine cells in the salamander retina can affect the sensitivity of retinal ganglion cells to different visual features. They use simultaneous recordings of amacrine and ganglion cells and apply current injection into the amacrine cells to assess the evoked response modulation of ganglion cells. The resulting transmission filter is combined with the amacrine cell's temporal receptive field to determine a visual feature that stands for the visual signal processing from stimulus to a ganglion cell via the recorded amacrine cell. This sets the stage for analyzing how activation of this "amacrine pathway" affects the encoding of other (orthogonal) visual features by the ganglion cell.

Strengths:<br /> The direct measurements of amacrine cell signals and their signal transmission to ganglion cells in challenging dual recordings is certainly a strength of this paper. In addition, the authors use an original and intriguing computational framework to analyze interactions of different visual features encoded by a ganglion cell and ask important questions about how inhibitory interneurons modulate stimulus encoding. The concept of distinct types of amacrine cell function with feature-specific modulation of input sensitivity and global modulation of output strength is thought-provoking and an interesting concept for follow-up investigations.

Weaknesses:<br /> However, despite the emphasis on a causal approach and direct measurements of amacrine cell effects, the paper does not use actual amacrine cell signals for the main analyses, but rather a proxy given by visual signals that are consistent with the amacrine-to-ganglion signal transmission. In doing so, it is largely disregarded that visual filters of other pathways (including, e.g., fatigue or desensitization in the excitatory signals) may overlap with the deduced amacrine pathways. It thus remains unclear how much such alternative pathways may contribute to the signals assigned to the amacrine pathway and how this might influence the findings and their interpretations. In addition, the analysis and interpretation of the amacrine pathway are hard to follow and easy to misunderstand, because the paper often applies ambiguous language by referring to the visual stimulus dimension of the amacrine pathway as "amacrine output" and "amacrine effects" and by equating activation or deactivation of the amacrine pathway with hyperpolarization or depolarization of the amacrine cell.

Some other interpretations are also unclear, by taking the results a bit too far. For example, the emphasis on divisive normalization remains unclear, as divisive normalization seems more specific than the general suppressive effects described here. Similarly, the connection to the previously observed reversal of preferred contrast by ganglion cells is somewhat tenuous. Here, the potential reversal in the analyzed response nonlinearities only concerns specific features that nonlinearly interact with other features and therefore do not easily translate to the contrast sensitivity of the ganglion cell as a whole, as is suggested in the text. In addition, the two examples of reversals shown in the figures are not fully convincing.

Regarding the clustering analysis of the pairs of amacrine cells and ganglion cell features (Fig. 4), a specific concern is that it is unclear how well the analyzed parameters can actually be extracted from the firing rate response nonlinearities. From the examples in Fig. 4A, it looks like many nonlinearities do not show a clear saturation (but might still yield a good fit by the piece-wise linear model and thus be included in the analysis). It seems plausible that this could result in a bias towards lower gain (defined via the saturation level) when nonlinearities are shifted rightward (higher threshold). It is thus not entirely clear how strong the evidence is for the correlation between gain and threshold changes.

Further, minor caveats are that only 11 amacrine cells go into the analysis, and it remains uncertain to what degree they cover the diversity of amacrine cells in the retina or rather represent a specific subset of types. Also, the restriction to visual signals with no spatial structure, though understandable, limits the generality of the findings. The extracted temporal features remain rather abstract with unspecified significance, in particular since quite a large number of features are extracted per ganglion cell (a total of 321 features, which presumably come from 39 ganglion cells that had a significant amacrine transmission filter).

Reviewer #3 (Public Review):

This study aims to provide a generalizable definition of retinal amacrine cell function in visual processing. The authors used larval tiger salamander retinas and white noise stimulus to measure the retinal ganglion cell responses with multielectrode array recording, while either measuring individual amacrine cell membrane potential or stimulating the amacrine cell by injecting white noise currents using a sharp electrode. Modulatory effects of an amacrine cell on ganglion cells are analyzed by a computational framework that parses the signaling processing underlying ganglion cell responses into multiple conceptual pathways that are differentially subject to the amacrine cell signaling. The authors conclude that an individual amacrine cell can have diverse modulatory effects on ganglion cell responses. One class of effects modulates the sensitivity of the ganglion cell to specific visual features, while the other class of effects modulates the gain of responses to all features.

Amacrine cells are known for their remarkable cell type diversity and serve as key players underlying the complexity of computations performed by the vertebrate retina. However, their functions largely remain a mystery except for a few better-studied cell types. Therefore, the topic of this study is important. Furthermore, the study aims to extract general computational functions from these neurons, which will have broader applications to sensory processing beyond the retina. My main questions are centered around the interpretation of the computational analysis. First of all, the definition of a "visual feature" in this study using the white noise stimulus is different from that used in many other retinal studies using more structured stimuli than white noise. In this study, a major finding is that amacrine cells can control the sensitivity of specific visual features of the ganglion cell. However, it is difficult to gain intuition about how such feature specificity is related to the processing of other artificial and natural stimuli. More discussion along this line will help to clarify the significance of this result.

Another concern is the assumption that the somatic membrane potential of the amacrine cell represents its transmission property to ganglion cells. There are compelling examples that amacrine cells often exhibit local response properties that dramatically differ across the dendritic arbor and the soma (e.g. AIIs, Vlgut3+ ACs, starburst amacrine cells, A17s). This potential (and likely) complication should be addressed.

The dataset in this study is from 8 sustained and 3 transient amacrine cells. Immediate questions are: do all sustained or all transient cells belong to the same cell type in terms of functional properties or morphology? Is there any difference in the modulatory effects between the sustained and transient groups?

There is a rich body of literature on the functions of various amacrine cell types in the mammalian retina in shaping the receptive field properties, gain, and sensitivity of retinal ganglion cells. It would help the reader if the novelty of the current study is adequately discussed in the context of previous work.

Technical:<br /> One concern of sharp electrode recordings is the dialysis of intracellular solution into the cytoplasm, causing changes in membrane properties over time (e.g. Hooper et al., 2015). Have the authors examined the data obtained at the earlier and later phases of the recording to assess the potential effect of dialysis?

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 #2 (Public Review):

Summary:<br /> The manuscript by Salazar-Lázaro et al. systematically dissects the different functional properties of the SNARE-domains of syntaxin-1 and syntaxin-2. By systematically substituting the SNARE-domain (or its C- or N-terminal half) into the non-cognate counterpart, the authors find that the C-terminal half of the SNARE-complex is especially important for maintaining RRP size and clamping spontaneous release. They also mutate single residues, to further nail down the effect. Overall, this is an interesting manuscript, which sheds light on the functionality of different co-expressed SNARES.

Strengths:<br /> The strength of the manuscript is the systematic dissection, using substitution of either SNARE-domain into the other syntaxin, together with the state-of-the art methods. The authors follow up with a substitution of single and paired residues. This is a large undertaking, which has been very well carried out.

Weaknesses:<br /> No major weaknesses. The large number of experiments paint a somewhat complicated picture. The writing could be improved in places to increase clarity.

Reviewer #3 (Public Review):

Summary:<br /> In this manuscript, Salazar-Lázaro et al. presented interesting data that C-terminal half of the Syx1 SNARE domain is responsible for clamping of spontaneous release, stabilizing RRP, and also Ca2+-evoked release. The authors routinely utilized the chimeric approach to replace the SNARE domain of Syx1 with its paralogue Syx2 and analyzed the neuronal activity through electrophysiology. The data are straightforward and fruitful. The conclusions are partly reasonable.

Strengths:<br /> The electrophysiology data that illustrate the important functions of Syx1 in clamping of spontaneous release, stabilizing RRP, and Ca2+-evoked release were clear and convincing.

Weaknesses:<br /> One obvious weakness is that the authors did not explore the underlying mechanism. I think it is easy for the authors to carry out some simple assays to verify their hypothesis for the mechanism, instead of just talking about it in the discussion section.

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 #2 (Public Review):

Summary:<br /> This study examined the possible effect of spike-wave discharges (SWDs) on the response to visual or somatosensory stimulation using fMRI and EEG. This is a significant topic because SWDs often are called seizures and because there is non-responsiveness at this time, it would be logical that responses to sensory stimulation are reduced. On the other hand, in rodents with SWDs, sensory stimulation (a noise, for example) often terminates the SWD/seizure.

In humans, these periods of SWDs are due to thalamocortical oscillations. A certain percentage of the normal population can have SWDs in response to photic stimulation at specific frequencies. Other individuals develop SWDs without stimulation. They disrupt consciousness. Individuals have an absent look, or "absence", which is called absence epilepsy.

The authors use a rat model to study the responses to stimulation of the visual or somatosensory systems during and in between SWDs. They report that the response to stimulation is reduced during the SWDs. While some data show this nicely, the authors also report on lines 396-8 "When comparing statistical responses between both states, significant changes (p<0.05, cluster-) were noticed in somatosensory auditory frontal..., with these regions being less activated in interictal state (see also Figure 4). That statement is at odds with their conclusion.

They also conclude that stimulation slows the pathways activated by the stimulus. I do not see any data proving this. It would require repeated assessments of the pathways in time.

The authors also study the hemodynamic response function (HRF) and it is not clear what conclusions can be made from the data.

Finally, the authors use a model to analyze the data. This model is novel and while that is a strength, its validation is unclear. The conclusion is that the modeling supports the conclusions of the study, which is useful.

Strengths:<br /> Use of fMRI and EEG to study SWDs in rats.

Weaknesses:<br /> Several aspects of the Methods and Results are unclear.

Reviewer #3 (Public Review):

Summary:<br /> This is an interesting paper investigating fMRI changes during sensory (visual, tactile) stimulation and absence seizures in the GAERS model. The results are potentially important for the field and do suggest that sensory stimulation may not activate brain regions normally during absence seizures. However the findings are limited by substantial methodological issues that do not enable fMRI signals related to absence seizures to be fully disentangled from fMRI signals related to the sensory stimuli.

Strengths:<br /> Investigating fMRI brain responses to sensory stimuli during absence seizures in an animal model is a novel approach with the potential to yield important insights.

The use of an awake, habituated model is a valid and potentially powerful approach.

Weaknesses:<br /> The major difficulty with interpreting the results of this study is that the duration of the visual and auditory stimuli was 6 seconds, which is very close to the mean seizure duration per Table 1. Therefore the HRF model looking at fMRI responses to visual or auditory stimuli occurring during seizures was simultaneously weighting both seizure activity and the sensory (visual or auditory) stimuli over the same time intervals on average. The resulting maps and time courses claiming to show fMRI changes from visual or auditory stimulation during seizures will therefore in reality contain some mix of both sensory stimulation-related signals and seizure-related signals. The main claim that the sensory stimuli do not elicit the same activations during seizures as they do in the interictal period may still be true. However the attempts to localize these differences in space or time will be contaminated by the seizure-related signals.

The claims that differences were observed for example between visual cortex and superior colliculus signals with visual stim during seizures vs. interictal are unconvincing due to the above.

The maps shown in Figure 3 do not show clear changes in the areas claimed to be involved.

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 #2 (Public Review):

The strengths of this paper begin with the topic. Specifically, this approaches the question of how GPCR signals are directed to different outcomes under different conditions. There is rich complexity within this question; there are potentially billions of molecules that could interact with >800 human GPCRs and thousands of molecular effectors that may be activated. However, these outcomes are filtered through a small number of GPCR-interacting proteins that direct the signal.

Experimentally, strengths include the initial experimental controls employed in characterizing their ever-important antisera, on which their conclusions hinge. In showing strong agonist-dependent and phosphosite-dependent recognition, as well as the addition of GRK inhibitors and eventually an antagonist and phosphatase treatment, the authors substantiate the role of the antiserum in recognizing their intended motifs. When employed, those antisera overall give clear indications of differences across variables in immunoblots, and while the immunocytochemical studies are qualitative and at times not visually significantly different across all variables, they are in large part congruent with the results of the immunoblots and provide secondary supporting evidence for the author's major claims. One confounding aspect of the immunocytochemical images is the presence of background pThr306/pThr310, like in Figures 4C and 6A and B. In 4A and C, while the immunoblot shows a complete absence of pThr306/pThr310, Figure 4C's immuno image does not. In 6A and B, a similar presence of pThr306/pThr310 is seen in the vehicle image, which is not strikingly over-shown by the MOMBA-treated image. In addition, only Ser/Thr residues of the C-terminus were investigated, while residues of ICL3 have long been known to direct signaling in many GPCRs. Because of the presentations of sequences, it was not clear whether there were residues of ICL3 that have the possibility of being involved.

It may be possible and further testable to show whether the residues that maintain basal phosphorylation could also be tissue-specific, especially considering the presence of pThr306/pThr310 detection in both the Figure 6A immunoblot's vehicle lane (but not MOMBA lane). The aforementioned detection in the immunocytochemical vehicle image could support differential basal phosphorylation in the enteroendocrine cells. Should this be the case, it could have confounded the initial mass-spec screen wherein the Ser residues were basally active in that cell type, while in a distinct cell type that may not be the case. Lastly, should normalized quantification of these images be possible, it may help in clearing up these hard-to-compare visual images.

It is noted that aspects of the writing and presentation may lead to confusion for some readers, but this does not affect the overall significance of the work.

Nevertheless, in terms of the global goal of the authors, the indication of differences in phosphorylation states between tissues is still evident across the experiments. Accordingly, the paper is overall strongly well-researched, well-controlled, and the conclusions made by the authors are data-grounded and not overly extrapolated. Providing direct evidence for the tissue-based branch of the barcode hypothesis is both novel and significant for the field, and the paper leaves room for much more exciting research to be done in the area, opening the door for new questions and hypotheses.

Reviewer #3 (Public Review):

Summary:<br /> The authors generate and characterize two phosphospecific antisera for FFA2 receptor and claim a "bar code" difference between white fat and Peyers patches.

Strengths:<br /> The question is interesting and the antibody characterization is convincing.

Weaknesses:<br /> The mass spectrometry analysis is not convincing because the method is not quantitative (no SILAC, TMT, internal standards etc). Figure 1 shows single tryptic peptides with one and two phosphorylation fragmentations as claimed, but there is no data testing the abundance of these so the differences claimed between cell treatment conditions are not established.

The blot analysis cannot distinguish 296/7 but it does convincingly show an agonist increase. Can the authors clarify why the amount of constitutive phosphorylation is much higher in the example blot in Figure 2 than in Figure 3? It would be helpful to quantify this across more than one example, like in Figures 4 and 5 for tissue.

Compound 101 is shown in Figure 2 to block barrestin recruitment. I agree this suggests phosphorylation mediated by GRK2/3 but this is not tested. The new antibodies should be good for this so I don't understand why the indirect approach.

The conditions used to inhibit dephosphorylation are not specified, the method only says "phosphatase inhibitors". How do the authors know that low P at 306/7 in white fat is not a result of dephosphorylation during sample preparation? If these sites are GRK2/3 dependent (see above) then does adipose tissue lack this GRK?

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 #2 (Public Review):

Summary:

This manuscript describes the study protocol, structure and logic of the PAVE strategy. The PAVE study is a multicentric study to evaluate a novel cervical screen-triage-treat strategy for resource-limited settings as part of a global strategy to reduce cervical cancer burden. The PAVE strategy involves: 1) screening with self-sampled HPV testing; 2) triage of HPV-positive participants with a combination of extended genotyping and visual evaluation of the cervix assisted by deep-learning-based automated visual evaluation (AVE); and 3) treatment with thermal ablation or excision (Large Loop Excision of the Transformation Zone). The PAVE study has two phases: efficacy (2023-2024) and effectiveness (planned to begin in 2024-2025). The efficacy phase aims to refine and validate the screen-triage portion of the protocol. The effectiveness phase will examine implementation of the PAVE strategy into clinical practice.

Strengths and weaknesses:

The Pave Study develops and evaluates a novel strategy that combines HPV self-collection, that has been proven effective to increase screening coverage in different settings, with genotyping and Automated Visual Evaluation as triage. The proposed strategy combined three key innovations to improve an important step in the cervical cancer care continuum. If the strategy is effective it will contribute to enhancing cervical cancer prevention in low resource settings.

As the authors mentioned, despite the existence of effective preventive technologies (e.g., HPV vaccine and HPV test) translation of the HPV prevention methods has not yet occurred in many Low-Middle-Income Countries. So, in this context, new screen-triage-treat strategies are needed and if PAVE strategy were effective, it could be a landmark for cervical cancer prevention.

The PAVE Study is a solid and important study that is aimed to be carried out in nine countries and recruit tens of thousands of women. It is a study with a large and diverse sample that can provide useful information for the development of this new screen-triage-treat strategy. Another strength is the fact that the PAVE project is integrated into the screening activities placed in the selected countries that will allow to evaluate efficacy and effectiveness in real-word context.

The manuscript does not present results because its aim is to describe the study protocol, structure and logic of the PAVE strategy.

Phase 1 aims to evaluate the efficacy of the strategy. Methods are well described and are consistent with the study aims.

Phase 2 aims to evaluate the implementation of the PAVE strategy in clinical practice. The inclusion of implementation evaluation in this type of studies is an important milestone in the field of cervical cancer prevention. It has been shown that many strategies that have proven to be effective in controlled studies face barriers when they are implemented in real life. In that sense, the results of phase 2 are key to ensure the future implementation of the strategy.

However, some aspects of Phase 2 need to be clarified and extended. Although authors mentioned that implementation outcomes, such as acceptability and feasibility will be evaluated, more information is needed about method (i.e. qualitative/quantitative), data collection tools (i.e., survey, semi-structure interviews, focus groups, etc.) and frameworks that will be used to evaluate these implementation outcomes.

Reviewer #3 (Public Review):

Summary:

Despite being preventable and treatable, cervical cancer remains the second most common cause of cancer death globally. This cancer, and associated deaths, occur overwhelmingly in low- and middle-income countries (LMIC), reflecting a lack of access to vaccination, screening and treatment services. Cervical screening is the second pillar in the WHO strategy to eliminate cervical cancer as a public health problem and will be critical in delivering early gains in cervical cancer prevention as the impact of vaccination will not be realized for several decades. However, screening strategies implemented in high income countries are not feasible or affordable in LMICs. This ambitious multi-center study aims to address these issues by developing and systematically evaluating a novel approach to cervical screening. The approach, based on primary screening with self-collected specimens for HPV testing, is focused on optimizing triage of people in whom HPV is detected, so that sensitivity for the detection of pre-cancer and cancer is maximized while treatment of people without pre-cancer or cancer is minimized.

Strengths:

The triage proposed for this study builds on the authors' previously published work in designing the ScreenFire test to appropriately group the 13 detected genotypes into four channels and to develop automated visual evaluation (AVE) of images of the cervix, taken by health workers.

The move from mobile telephone devices to a dedicated device to acquire and evaluate images overcomes challenges previously encountered whereby updates of mobile phone models required retraining of the AVE algorithm.

The separation of the study into two phases, an efficacy phase in which screen positive people will be triaged and treated according to local standard of care and the performance of AVE will be evaluated against biopsy outcomes will be followed by the second phase in which the effectiveness, cost-effectiveness, feasibility and acceptability will be evaluated.

The setting in a range of low resource settings which are geographically well spread and reflective of where the global cancer burden is highest.

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.

Reviewer #2 (Public Review):

This study aims to characterize transcriptional and epigenetic activity-dependent striatal neuronal adaptations using rat primary cultures, a model still poorly characterized up to date. In addition, the authors aim to interrogate regulatory mechanisms that could modulate the expression of a highly-striatal enriched gene responding to neuronal activation in striatal neuronal cells, the Pdyn gene.

Among the major strengths of the article there is the generation of high quality neuronal RNA-seq and ATAC-seq data in rat striatal neuronal cells in basal level and upon neuronal activity, a experimental setup that has not been so characterized as other more common ones such as mouse hippocampal neuronal cells. In this model, the authors clearly demonstrate the need of protein translation to induce the transcriptional waves of late response genes. In addition, the functional characterization of an enhancer of the Pdyn gene might be of great interest for translational applications in which alterations of this gene might be occurring in neurological disorders.

On the other hand, the manuscript presents some limitations to be considered. One of the major points in this regard is that, at least in part, some of the conclusions reached by the study related to the induction of particular transcriptional programs upon neuronal activation, the changes in chromatin state, and the need of protein translation for proper induction of LRGs have been already previously described in the literature, affecting the novelty of the study. However, it is needed to be mentioned, that these previous studies were not conducted using the same model (rat striatal neurons), which can make some differences in the final outputs. The other major cautionary point in the study is the selection of the time point for distinguishing early versus late response genes, as the short difference in time and the overlap of part of the transcriptional signature between them suggest that the transcriptional waves are somehow partially overlapping (also probably in part because of the recurrent stimulation of the primary cultures with KCl), which could result in missing part of the late-response genes.

Despite this, the conclusions raised in the study are well supported by the data generated in it.

In summary, the study presents a useful set of transcriptomic and epigenomic data of activity-dependent striatal neuronal programs in rats, which will be of great use for the scientific community working in this not so well characterized model. In addition, the characterization of a Pdyn distal regulatory genomic region involved in its transcriptional regulation, both at basal levels and upon neuronal activation in this particular system, can present translational relevance for striatal disorders such as Huntington's disease or other neuropsychiatric disorders.

Reviewer #3 (Public Review):

This work contributes to the literature characterizing early and late waves of transcription and associated chromatin remodeling following neuronal depolarization, here in cultured embryonic striatum. While they find IEG transcription 1 h after depolarization, they find chromatin remodeling is slower (opening at the 4 h time point). While this is not the first paper to describe chromatin changes in response to neuronal activity, this paper ties previous findings all together in one place using novel sequencing analyses and visualizations. Previous work has found remodeling occurring at the 1 h time point, so the lack of differences at that early time point in the current study needs to be better understood and the "temporal decoupling" described by authors should be further explored. Differences may be due to chromatin at IEG regulatory regions already being open in embryonic tissue (here) vs generally more closed in adult tissue (previous), or due to previous studies using protocols to specifically silence neurons prior to activation. The authors next show that the chromatin remodeling that occurs at the late (4 h) stage is largely in putative regulatory regions of the genome (rather than gene bodies), and is dependent on translation, which validates and extends the prior literature. The authors then transition from genome-wide basic neuroscience to focus on a specific gene of interest, prodynorphin (Pdyn), and a putative enhancer they identify from their chromatin analysis. They target CRISPR-activating and -inhibiting complexes to the putative enhancer and demonstrate that accessibility of this locus is necessary and sufficient for Pdyn transcription. They then show that at least one PDYN enhancer is conserved from rodents to humans, and is only activity-regulated in human GABAergic but not glutamatergic neurons. Finally, the authors generate snATAC-seq and show Pdyn gene and enhancer activity is also cell-type-specific in rat striatum. The Pdyn work, in particular, is thorough and novel, and demonstrates a translational aspect of this work.

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.

Reviewer #2 (Public Review):

The revised paper addresses most of my major comments and concerns. The authors have added more detail explaining their model, they have added more background information, citations, and discussion for termite humidity sensing capabilities. With these modifications, this paper now provides a convincing presentation of valuable results of the drivers of nest construction for one termite species, and they briefly discuss possible relevance to other termite species. However, the authors have not yet addressed how their results may be important outside the field of termite nest construction. I could imagine the significance of the paper being elevated to important if there is a broader discussion about the impact of this work, e.g., the relevance of the results, the approach, and/or next steps to related fields outside of termite nest construction. Similarly, on a related note, as someone not directly in the field of termite nest construction but wanting to understand the system (and the results) presented here in a broader context, I found the additional information about species and natural habitat very helpful and interesting, though I was rather disappointed to find it relegated to supplementary material where most readers will not see it.

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 #2 (Public Review):

The work by Bærentsen et al., entitled "Structural basis for regulation of a tripartite toxin-antitoxin system by dual phosphorylation" deals with the structural aspects of the control of the hipBST TA operon, the role of auto-phosphorylation in the activation and neutralisation of the enzyme and the direct effects of HipS and HipB in neutralisation. This is a follow-up to the Vang Nielsen et al., and Gerdes et al., papers from the same authors on this very unique TA module, that brings forth a thorough and well written dissection of an unusually complex regulatory system.

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 #2 (Public Review):

Summary:<br /> Dolcemascolo and colleagues describe the use of the mammalian RNA-binding protein Musashi-1 (MSI-1) to implement translational regulation systems in E. coli. They perform detailed in vitro studies of MSI-1 and its binding to different RNA sequences. They provide compelling evidence of the effectiveness of the regulatory system in multiple circuits using different mRNA sequence motifs. They harness allosteric inhibition of MSI-1 by omega-9 monounsaturated fatty acids to demonstrate a fatty-acid-responsive circuit in E. coli.

Strengths:<br /> The experimental results are compelling and the characterization of the binding between MSI-1 and different RNA sequences is thorough and performed via multiple complementary techniques. Several new useful circuit components are demonstrated.

Weaknesses:<br /> MSI-1 provides 8.6-fold downregulation of sfGFP with an optimized mRNA sequence. In some applications, a larger degree of repression may be required.

Reviewer #3 (Public Review):

Summary:<br /> In this work, the authors co-opt the RRM-binding protein Musashi-1 to act as a translational repressor. The novelty of the work is in the adoption of the allosteric RRM protein Musashi-1 into a translational reporter and the demonstration that RRM proteins, which are ubiquitous in eukaryotic systems, but rare in prokaryotic ones, may act effectively as post-translational regulators in E. coli. The extent of repression achieved by the best design presented in this work is not substantially improved compared to other synthetic regulatory schemes developed for E. coli, even those that similarly regulate translation (eg. native PP7 repression is approximately 10-fold, Lim et al. J. Biol. Chem. 2001 276:22507-22513). Furthermore, the mechanism of regulation is not established due to missing key experiments. The work would be of broader interest if the allosteric properties of Musashi-1 were more effective in the context of regulation. Unfortunately, the authors do not demonstrate that fatty acids can completely de-repress expression in the experimental system used for most of their assays, nor do they use this ability in their provided application (NIMPLY gate).

Strengths:<br /> The first major achievement of this work is the demonstration that a eukaryotic RRM protein may be used to post-transcriptionally regulate expression in bacteria. In my limited literature search, this appears to be the first engineering attempt to design an RBP to directly regulate translation in E. coli, although engineered control of translation via other approaches including alterations to RNA structure or via trans-acting sRNAs have been previously described (for review see Vigar and Wieden Biochim Biophys. Acta Gen. Subj. 2017, 1861:3060-3069). Additionally, several viral systems (e.g. MS2 and PP7) have been directly co-opted to work in a similar fashion in the past (utilized recently in Nguyen et al. ACS Synthetic Biol 2022, 11:1710-1718).

The second achievement of this work is the demonstration that the allosteric regulation of Musashi-1 binding can be utilized to modulate the regulatory activity. However, the liquid culture demonstration (Suppl. Fig 8) shows that this is not a very effective switch, with de-repressed reporter activity showing substantial change but not approaching un-repressed activity. This effect is stronger when colonies are grown on a solid medium (Fig. 5).

Weaknesses:<br /> In this work, the authors codon optimize the mouse Musashi-1 coding sequence for expression in E. coli and demonstrate using an sfGFP reporter that an engineered Musashi-1 binding site near the translational start site is sufficient to enable a modest reduction in reporter gene expression. The authors postulate that the reduction in expression due to inhibition of ribosome translocation along the transcript (lines 134/135), as an expression of a control transcript (mScarlet) driven by the same promoter (Plac) but without the Musashi-1 recognition site does not demonstrate the same repression. However, the situation could be more complex. Other possibilities include inhibition of translation initiation rather than elongation, as well as accelerated mRNA decay of transcripts that are not actively translated. The authors do not present any measurements of sfGFP mRNA levels.

In subsequent sections of the work, the authors create a series of point mutations to assess RNA-protein binding and assess these via both a sfGFP reporter and in vitro binding assays (switchSENSE). Ultimately, it is difficult to fully rationalize and interpret the behavior of these mutants in the context provided. The authors do identify a relationship between equilibrium constant (1/KD) and fold-repression. However, it is not clear from the narrative why this relationship should exist. Fold-repression is one measure of regulator efficacy, but it is an indirect measure determined from unrepressed and repressed expression. It is not clear why unrepressed expression (in the absence of the protein) is expected to be a function of the equilibrium constant.

Subsequent rational redesign of the Musashi-1 binding sequence to produce three alternative designs shows that fold-repression may be improved to approximately 8.6-fold. However, the rationalization of why the best design (red3) achieves this increase based on either the extensive modelling or in vitro measured binding constants is not well articulated. Furthermore, this extent of regulation is approximately that which can be achieved from the PP7 system with its native components (Lim et al. J. Biol. Chem. 2001 276:22507-22513).

The application provided for this regulator (NIMPLY gate), is not an inherently novel regulatory paradigm, and it does not capitalize on the allosteric properties of Musashi-1, but rather treats Musashi-1 as a non-allosteric component of a regulatory circuit.

This whole document feels like it could have been written more compactly.

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 #2 (Public Review):

This model of skeletal muscle includes springs and dampers which aim to capture the effect of crossbridge and titin stiffness during the stretch of active muscle. While both crossbridge and titin stiffness have previously been incorporated, in some form, into models, this model is the first to simultaneously include both. The authors suggest that this will allow for the prediction of muscle force in response to short-, mid- and long-range stretches. All these types of stretch are likely to be experienced by muscle during in vivo perturbations, and are known to elicit different muscle responses. Hence, it is valuable to have a single model which can predict muscle force under all these physiologically relevant conditions. In addition, this model dramatically simplifies sarcomere structure to enable this muscle model to be used in multi-muscle simulations of whole-body movement.

In order to test this model, its force predictions are compared to 3 sets of experimental data which focus on short-, mid- and long-range perturbations, and to the predictions of a Hill-type muscle model. The choice of data sets is excellent and provide a robust test of the model's ability to predict forces over a range of length perturbations. However, I find the comparison to a Hill-type muscle model to be somewhat limiting. It is well established that Hill-type models do not have any mechanism by which they can predict the effect of active muscle stretch. Hence, that the model proposed here represents an improvement over such a model is not a surprise. Many other models, some of which are also simple enough to be incorporated into whole-body simulations, have incorporated mechanistic elements which allow for the prediction of force responses to muscle stretch. It is not clear from the results presented here that this model would outperform such models.

The paper begins by outlining the phenomenological vs mechanistic approaches taken to muscle modelling, historically. It appears, although is not directly specified, that this model combines these approaches. A somewhat mechanistic model of the response of the crossbridges and titin to active stretch is combined with a phenomenological implementation of force-length and force-velocity relationships. This combination of approaches may be useful in improving the accuracy of predictions of muscle models and whole-body simulations, which is certainly a worthy goal. However, it also may limit the insight that can be gained. For example, it does not seem that this model could reflect any effect of active titin properties on muscle shortening. In addition, it is not clear to me, either physiologically or in the model, what drives the shift from the high stiffness in short-range perturbations to the somewhat lower stiffness in mid-range perturbations.

Reviewer #2 (Public Review):

Summary:

This study represents an ambitious endeavor to comprehensively analyze the role of miR-199a/b-5p and its networks in cartilage formation. By conducting experiments that go beyond in vitro MSC differentiation models, more robust conclusions can be achieved.

Strengths:

This research investigates the role of miR-199a/b-5p during chondrogenesis using bioinformatics and in vitro experimental systems. The significance of miRNAs in chondrogenesis and OA is crucial, warranting further research, and this study contributes novel insights.

Weaknesses:

While miR-140 and miR-455 are used as controls, these miRNAs have been demonstrated to be more relevant to Cartilage Homeostasis than chondrogenesis itself. Their deficiency has been genetically proven to induce Osteoarthritis in mice. Therefore, the results of this study should be considered in comparison with these existing findings.

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):

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 #2 (Public Review):

Summary:

In this study, Winstel and colleagues test if the deoxycytidine kinase inhibitor, (R)-DI-87 provides therapeutic benefit during infection with Staphylococcus aureus. The premise behind the current work is a series of prior studies that found that S. aureus can disable functional immune clearance by generating NET-derived deoxyribonucleosides to induce macrophage apoptosis via purine salvage. Here, the authors use in vitro and in vivo experiments with (R)-DI-87 to demonstrate that inhibition of deoxycytidine kinase prevents S. aureus-induced deoxyribonucleoside-mediated macrophage cell death, to bolster immune cell function and promote more effective clearance during infection. The authors conclude that (R)-DI-87 represents and potentially important Host-Directed Therapy (HDT) with good potential to promote natural clearance of infection without targeting the bacterium. Overall, the study represents an important next step in the exploration of purine salvage and deoxyribonucleoside toxicity as a targetable pathway to bolster infection clearance and provides early-stage evidence of the therapeutic potential of (R)-DI-87 during S. aureus infection.

Strengths:

The study has several strengths that support its conclusions:<br /> 1. Well-controlled in vitro studies that firmly establish (R)-DI-87 is capable of blocking deoxyribonucleoside-mediated apoptosis of immune cell lines and primary cells.<br /> 2. Solid evidence to support that administration of (R)-DI-87 can have therapeutic benefits during infection (reduced number of abscesses and reduced CFU).<br /> 3. Controls included to ascertain the degree to which (R)-DI-87 might have secondary effects on immune cell distribution.<br /> 4. Controls included to ascertain whether or not (R)-DI-87 has intrinsic antibacterial properties.

Weaknesses:

However, there are several important weaknesses related to the rigor of the research and the conclusions drawn. The most relevant weaknesses noted by this reviewer are:

1. Drawing firm conclusions about the therapeutic potential of (R)-DI-87 using only S. aureus strain Newman, a methicillin-susceptible S. aureus, that while a clinical isolate is not clearly representative of the strains of S. aureus causing infection in hospitals and communities. Newman also harbors an unusual mutation in a regulator that dramatically changes virulence factor gene expression. While the data with Newman remains valuable, the absence of consideration of other strains, including MRSA, makes it more difficult to support the relatively broad conclusions about therapeutic potential made by the authors.

2. In vitro (R)-DI-87 efficacy studies with dAdo and dGuo are strong, however, the authors do not test the in vitro efficacy of (R)-DI-87 using S. aureus. They have done this type of work in prior studies (See doi: 10.1073/pnas.1805622115 - Figure 5). If included it would greatly strengthen their argument that (R)-DI-87 is directly affecting the S. aureus --> Nuclease --> AdsA macrophage-killing pathway. Without it, the evidence provided remains indirect, and several conclusions may be overstated.

3. Caspase-3 immunoblot experiments seem to suggest an alternative conclusion to what was made by the authors. They point out that Caspase-3 cleavage does not occur upon treatment with (R)-DI-87. However, the data seem to argue that there is almost no caspase-3 present in (R)-DI-87 treated cells (cleaved or uncleaved). Might this suggest that caspase-3 is not even produced when cells are not experiencing deoxyribonucleoside toxicity? Perhaps the authors could reconsider the interpretation of this data.

4. There are some concerns over experimental rigor and clarity of the experimental design in the methods. The most important points noted by this reviewer are included here. (a.) There is no description of the number of replicates or representation of the Western blots and no uncropped blots are provided. (b.) the methods describing the treatment conditions for in vivo studies are not sufficiently clear. For example, it is hard to tell when (R)-DI-87 is first administered to mice. Is it immediately before the infection, immediately after, or at the same time? This has important implications for interpreting the results in terms of therapeutic potential. (c.) There are several statements made that (R)-DI-87 does not have a negative impact on the mice however, it is not sufficiently clear that the studies conducted are sufficient to make this broader claim that (R)-DI-87 has no impact on the animal, except as it relates to the distribution of immune cells, which is directly tested. (d.) there are no quantitative measures of apoptosis or macrophage infiltration, which impacts the rigor of these imaging experiments. (d.) only female mice are used in the in vivo studies. There is no justification provided for this choice; however, the rigor of the study design and the ability to draw conclusions about therapeutic potential is impacted in the absence of consideration of both sexes.

5. Animal studies show significant disease burden (CFU) even after administration of (R)-DI-87. Given the absence of robust clearance of infection, the author's claims read as an overstatement of the data. The authors may wish to reframe their conclusions to better highlight the potential benefit of this therapy at reducing severe disease but also to point out relevant limitations, especially considering that it does not lead to clearance in this model. In general, the consideration of the limitations of the proposed therapeutic approach, as uncovered by the data, is not present. A more nuanced consideration of the data and its interpretations, including both strengths and limitations, would greatly help to frame the study.