Reviewer #2 (Public Review):

Significance<br /> Rubio et al. study the behavior of the transcription factor Hsf1 under ethanol stress, examining its distribution within the nucleus and the coalescence of heat shock response genes in budding yeast. In comparison to the heat shock response, the response to ethanol stress shows similar gene coalescence and Hsf1 binding. However, there is a notable delay in the transcriptional response to ethanol, and a disconnect between it and the appearance of irreversible Hsf1 condensates/puncta, highlighting important differences in how Hsf1 responds to these two related but distinct environmental stresses.

Overview and general concerns<br /> The authors studied how yeast responds to ethanol stress (8.5%) and compared it to the heat shock response (from 25{degree sign}C to 39{degree sign}C). They observed a more gradual increase in the expression of heat shock response (HSR) genes during ethanol stress compared to heat shock. Additionally, the recruitment of Hsf1 and Pol II to HSR genes, and the inter- and intrachromosomal interactions among these genes, showed slower kinetics under ethanol stress. They attribute the delay in transcriptional response to chromatin compaction induced by ethanol. Despite this delay, these interactions persisted longer. Hsf1 clusters, previously documented during the heat shock response, were also observed during ethanol stress and persisted for an extended period. The conditional degradation of Hsf1 and Rpb1 eliminated most inter- and intrachromosomal interactions for heat shock responsive genes in both ethanol stress and heat shock conditions, indicating the importance of these factors for long-distance interactions between HSR genes. Overall, this manuscript provides novel insights into the differential behavior of HSR genes under different stress conditions. This contributes to the broader understanding of how different stressors might elicit unique responses at the genomic and topographical level under the regulation of transcription factor Hsf1.

The central finding of the study highlights the different dynamics of Hsf1, Pol II, and gene organization in response to heat shock versus ethanol stress. However, one important limitation to consider is that the two chosen conditions may not be directly comparable. For a balanced assessment, the authors should ideally expose yeast to various ethanol concentrations and different heat shock temperatures, ensuring the observed differences stem from the nature of the stressor rather than suboptimal stress intensity. At the very least, an additional single ethanol concentration point on each side of 8.5% should be investigated to ensure that 8.5% is near the optimum. In fact, comparing the number of Hsp104 foci in the two conditions in Fig. 1E and F suggests that the yeast is likely experiencing different intensities of stress for the chosen heat shock condition and ethanol concentration used in this study.

A second significant concern is the use of the term "Hsf1 condensate". Chowdhary et al.'s 2022 Molecular Cell study highlighted an inhomogeneous distribution and rapid dynamics of Hsf1 clustering upon heat shock, with sensitivity to 1,6-hexandiol, which is interpreted as evidence for condensation by LLPS. However this interpretation has been criticized severely by McSwiggen et al. Genes Dev 2019 and Mussacchio EMBO J 2022. It is important to mention that 1,6-hexandiol is known to affect chromatin organization (Itoh et al. Life Science Alliance 2021). Describing such clusters as 'condensates' without further experimental evidence is premature. I encourage authors to settle on their neutral term 'puncta' which they use interchangeably with 'condensate' so as not to confuse the reader. The dynamic binding and unbinding of the low-abundance Hsf1 at coalescent chromatin target sites might explain the liquid-like properties of these clusters without the need for invoking the phase-separation hypothesis. While Hsf1 clusters exhibit features consistent with phase-separated condensates, other equally plausible alternative mechanisms, such as dynamic site-specific interactions (Musacchio, EMBO J, 2022), should also be considered. This is best left for the discussion where the underlying mechanism for puncta formation can be addressed.

Specific comments:

- Figure 1: Why does ethanol stress at 0 min display a larger number of Hsp104 foci per cell than heat shock at the same time? How are foci defined by the authors? In Fig. 1D, there are many smaller puncta. A comparative assessment of the number and size of foci for heat shock and ethanol stress would be beneficial.

- Figure 2: Selecting a housekeeping gene with consistent expression levels is crucial for meaningful qPCR analysis. Do SCR1 mRNA levels fluctuate during heat shock or ethanol stress? Additionally, certain genes, such as TMA10 and SSA4, lack visible bars at time 0. Are these levels undetectable? The varying y-axis scales are confusing; presenting data as relative fold changes could offer a clearer perspective.

- Line 239: The evidence for chromatin compaction is unconvincing. An increase in H3 occupancy by ChIP might indicate a reduction in histone exchange dynamics but may not relate to overall chromatin compaction. The authors use H2A-mCherry to suggest a decrease in chromatin volume, but this data is not persuasive. Did the authors observe any changes in nuclear size? Perhaps quantifying chromatin compaction more directly, using signal intensity per volume, would be informative.

- Line 340: The claim of a "strong spatiotemporal correlation" isn't evident from the data. Could correlation coefficients be provided? There is potential anti-correlation in Fig. 6 - Figure Supplement 1C.

- Figure 8: The WT data in Fig 8 seem inconsistent with Fig. 4 (e.g. the interaction frequency for HSP104 and SSA2). Are these fluctuations between experiments, or are they side effects of IAA treatment? The use of ethanol as an IAA solvent vehicle raises concerns. It would be beneficial if the authors could demonstrate that 1.7% ethanol in the control does not induce ethanol stress.

Reviewer #2 (Public Review):

Moutard, Laura, et al. investigated the gene expression and functional aspects of Leydig cells in a cryopreservation/long-term culture system. The authors found that critical genetic markers for Leydig cells were diminished when compared to the in-vivo testis. The testis also showed less androgen production and androgen responsiveness. Although they did not produce normal testosterone concentrations in basal media conditions, the cultured testis still remained highly responsive to gonadotrophin exposure, exhibiting a large increase in androgen production. Even after the hCG-dependent increase in testosterone, genetic markers of Leydig cells remained low, which means there is still a missing factor in the culture media that facilitates proper Leydig cell differentiation. Optimizing this testis culture protocol to help maintain proper Leydig cell differentiation could be useful for future human testis biopsy cultures, which will help preserve fertility and child cancer patients.

Overall, the authors addressed most comments and questions from the previous review. The additional data regarding the necrotic area is helpful for interpreting the quality of the cultures.

The authors did not conduct multiple comparison tests although there are multiple comparisons conducted for a single dependent variable (Fig 2J, Fig 3F, among many others), however, the addition of this multiple comparison is unlikely to change the conclusions of the paper or the figure and, thus is a minor technical detail in this case.

Reviewer #2 (Public Review):

The authors have studied in detail the embryogenesis of the ametabolan insect Thermobia domestica. They have also measured the levels of the two most important hormones in insect development: juvenile hormone (JH) and ecdysteroids. The work then focuses on JH, whose occurrence concentrates in the final part (between 70 and 100%) of embryo development. Then, the authors used a precocene compound (7-ethoxyprecocene, or 7EP) to destroy the JH producing tissues in the embryo of the firebrat T. domestica, which allowed to unveil that this hormone is critically involved in the last steps of embryogenesis. The 7EP-treated embryos failed to resorb the extraembryonic fluid and did not hatch. More detailed observations showed that processes like the maturational growth of the eye, the lengthening of the foregut and posterior displacement of the midgut, and the detachment of the E2 cuticle, were impaired after the 7EP treatment. Importantly, a treatment with a JH mimic subsequent to the 7EP treatment restored the correct maturation of both the eye and the gut. It is worth noting that the timing of JH mimic application was essential for correcting the defects triggered by the treatment with 7EP.

This is a relevant result in itself since the role of JH in insect embryogenesis is a controversial topic. It seems to have an important role in hemimetabolan embryogenesis, but not so much in holometabolans. Intriguingly, it appears important for hatching, an observation made in hemimetabolan and in holometabolan embryos. Knowing that this role was already present in ametabolans is relevant from an evolutionary point of view, and knowing exactly why embryos do not hatch in the absence of JH, is relevant from the point of view of developmental biology.

Then, the authors describe a series of experiments applying the JH mimic in early embryogenesis, before the natural peak of JH occurs, and its effects on embryo development. Observations were made under different doses of JHm, and under different temporal windows of treatment. Higher doses triggered more severe effects, as expected, and different windows of application produced different effects. The most used combination was 1 ng JHm applied 1.5 days AEL, checking the effects 3 days later. Of note, 1.5 days AEL is about 15% embryonic development, whereas the natural peak of JH occurs around 85% embryonic development. In general, the ectopic application of JHm triggered a diversity of effects, generally leading to an arrest of development. Intriguingly, however, a number of embryos treated with 1 ng of JHm at 1.5 days AEL showed a precocious formation of myofibrils in the longitudinal muscles. Also, a number of embryos treated in the same way showed enhanced chitin deposition in the E1 procuticle and showed an advancement of at least a day in the deposition of the E2 cuticle.

While the experiments and observations are done with great care and are very exhaustive, I am not sure that the results reveal genuine JH functions. The effects triggered by a significant pulse of ectopic JHm when the embryo is 15% of the development will depend on the context: the transcriptome existing at that time, especially the cocktail of transcription factors. This explains why different application times produce different effects. This also explains why the timing of JHm application was essential for correcting the effects of 7EP treatment. In this reasoning, we must consider that the context at 85% development, when the JH peaks in natural conditions and plays its genuine functions, must be very different from the context at 15% development, when the JHm was applied in most of the experiments. In summary, I believe that the observations after the application of JHm reveal effects of the ectopic JHm, but not necessarily functions of the JH. If so, then the subsequent inferences made from the premise that these ectopic treatments with JHm revealed JH functions are uncertain and should be interpreted with caution.

Those inferences affect not only the "JH and the progressive nature of embryonic molts" section, but also, the "Modifications in JH function during the evolution of hemimetabolous and holometabolous life histories" section, and the entire "Discussion". In addition to inferences built on uncertain functions, the sections mentioned, especially the Discussion, I think suffer from too many poorly justified speculations. I love speculation in science, it is necessary and fruitful. But it must be practiced within limits of reasonableness, especially when expressed in a formal journal.

Finally, In the section "Modifications in JH function during the evolution of hemimetabolous and holometabolous life", it is not clear the bridge that connects the observations on the embryo of Thermobia and the evolution of modified life cycles, hemimetabolan and holometabolan.

Reviewer #2 (Public Review):

Summary:

The authors compared the cortical folding of human brains with folding in macaque monkey brains to reveal shared and unique locations of gyral peaks. The shared gyral peaks were located in cortical regions that are functionally similar and less changed in humans from those in macaques, while the locations of unique peaks in humans are in regions that have changed or expanded functions. These findings are important in that they suggest where human brains have changed more than macaque brains in their subsequent evolution from a common ancestor. The massive analysis of comparative results provides evidence of where humans and macaques are similar or different in cortical markers, as well as noting some of the variations within each of the two primates.

Strengths:

The study includes massive detail.

Weaknesses:

The manuscript is too long and there is not enough focus on the main points. A brief listing of previous views on why fissures form and what factors are important would be helpful.

Reviewer #2 (Public Review):

Summary:<br /> In the current work, authors deploy a set of behavioral tasks to explore individual differences in the preferred perceptual and motor rhythms. They found a consistent individual preference for a given perceptual and motor frequency across tasks and, while these were correlated, the latter is slower than the former one. Additionally, they show that the accuracy of adaptation to rate changes is proportional to the amount of rate variation and, crucially, the amount of adaptation decreases with age.

Strengths:<br /> Authors carefully designed several experiments to measure individual preferred motor and perceptual tempo. Furthermore, before completing the main experiment they validated the experimental design by testing the consistency across tasks and test-retest. Additionally, to the value of the reported findings, the introduced paradigm represents a useful tool for future research.<br /> The obtained data is rigorously analyzed using a diverse set of tools, each adapted to the specificities across the different research questions and tasks.<br /> This study identifies several relevant behavioral features: (i) each individual shows a preferred and reliable motor and perceptual tempo and, while both are related, the motor is consistently slower than the pure perceptual one; (ii) the existence of hysteresis in the adaptation to rate variations; and (iii) the decrement of this adaptation with age. All these observations are valuable for the auditory-motor integration field of research, and they could potentially inform existing biophysical models to increase their descriptive power.

Weaknesses:<br /> The current study is presented in the framework of the ongoing debate of oscillator vs. timekeeper mechanisms underlying perceptual and motor timing, and authors claim that the observed results support the former mechanism. In this line, every obtained result is related by the authors to a specific ambiguous (i.e., not clearly related to a biophysical parameter) feature of an internal oscillator. As pointed out by an essay on the topic (1), claiming that a pattern of results is compatible with an "oscillator" could be misleading, since some features typically used to validate or refute such mechanisms are not well grounded on real biophysical models. Relatedly, a recent study (2) shows that two quantitatively different computational algorithms (i.e., absolute vs relative timing) can be explained by the same biophysical model. This demonstrates that what could be interpreted as a timekeeper, or an oscillator can represent the same biophysical model working under different conditions. For this reason, if authors would like to argue for a given mechanism underlying their observations, they should include a specific biophysical model, and test its predictions against the observed behavior. For example, it's not clear why authors interpret the observation of the trial's response being modulated by the rate of the previous one, as an oscillator-like mechanism underlying behavior. As shown in (1) a simple oscillator returns to its natural frequency as soon as the stimulus disappears, which will not predict the long-lasting effect of the previous trial. Furthermore, a timekeeper-like mechanism with a long enough integration window is compatible with this observation.<br /> Still, authors can choose to disregard this suggestion, and not testing a specific model, but if so, they should restrict this paper to a descriptive study of the timing phenomena.

1. Doelling, K. B., & Assaneo, M. F. (2021). Neural oscillations are a start toward understanding brain activity rather than the end. PLoS biology, 19(5), e3001234.<br /> 2. Doelling, K. B., Arnal, L. H., & Assaneo, M. F. (2022). Adaptive oscillators provide a hard-coded Bayesian mechanism for rhythmic inference. bioRxiv, 2022-06.

Reviewer #2 (Public Review):

When people help others is an important psychological and neuroscientific question. It has received much attention from the psychological side, but comparatively less from neuroscience. The paper translates some ideas from a social Psychology domain to neuroscience using a neuroeconomically oriented computational approach. In particular, the paper is concerned with the idea that people help others based on perceptions of merit/deservingness, but also because they require/need help. To this end, the authors conduct two experiments with an overlapping participant pool:

1) A social perception task in which people see images of people that have previously been rated on merit and need scales by other participants. In a blockwise fashion, people decide whether the depicted person a) deserves help, b) needs help, and c) whether the person uses both hands (== control condition).

2) In an altruism task, people make costly helping decisions by deciding between giving a certain amount of money to themselves or another person. How much the other person needs and deserves the money is manipulated.

The authors use a sound and robust computational modelling approach for both tasks using evidence accumulation models. They analyse behavioural data for both tasks, showing that the behaviour is indeed influenced, as expected, by the deservingness and the need of the shown people. Neurally, the authors use a block-wise analysis approach to find differences in activity levels across conditions of the social perception task (there is no fMRI data for the other task). The authors do find large activation clusters in areas related to the theory of mind. Interestingly, they also find that activity in TPJ that relates to the deservingness condition correlates with people's deservingness ratings while they do the task, but also with computational parameters related to helping others in the second task, the one that was conducted many months later. Also, some behavioural parameters correlate across the two tasks, suggesting that how deserving of help others are perceived reflects a relatively stable feature that translates into concrete helping decisions later-on.

The conclusions of the paper are overall well supported by the data.

1) I found that the modelling was done very thoroughly for both tasks. Overall, I had the impression that the methods are very solid with many supplementary analyses. The computational modelling is done very well.

2) A slight caveat, however, regarding this aspect, is that, in my view, the tasks are relatively simplistic, so even the complex computational models do not do as much as they can in the case of more complex paradigms. For example, the bias term in the model seems to correspond to the mean response rate in a very direct way (please correct me if I am wrong).

3) Related to the simple tasks: The fMRI data is analysed in a simple block-fashion. This is in my view not appropriate to discern the more subtle neural substrates of merit/need-based decision-making or person perception. Correspondingly, the neural activation patterns (merit > control, need > control) are relatively broad and unspecific. They do not seem to differ in the classic theory of mind regions, which are the focus of the analyses.

4) However, the relationship between neural signal and behavioural merit sensitivity in TPJ is noteworthy.

5) The latter is even more the case, as the neural signal and aspects of the behaviour are correlated across subjects with the second task that is conducted much later. Such a correlation is very impressive and suggests that the tasks are sensitive for important individual differences in helping perception/behaviour.

6) That being said, the number of participants in the latter analyses are at the lower end of the number of participants that are these days used for across-participant correlations.

Reviewer #2 (Public Review):

Summary:

In this manuscript, Shen and collaborators described the generation of cDKO mice lacking LRRK1 and LRRK2 selectively in DAT-positive DAergic neurons. The Authors asked whether selective deletion of both LRRK isoforms could lead to a Parkinsonian phenotype, as previously reported by the same group in germline double LRRK1 and LRRK2 knockout mice (PMID: 29056298). Indeed, cDKO mice developed a late reduction of TH+ neurons in SNpc that partially correlated with the reduction of NeuN+ cells. This was associated with increased apoptotic cell and microglial cell numbers in SNpc. Unlike the constitutive DKO mice described earlier, however, cDKO mice did not replicate the dramatic increase in the number of autophagic vacuoles. The study supports the authors' hypothesis that loss of function rather than gain of function of LRRK2 leads to PD.

Strengths:

The study described for the first time a model where both the PD-associated gene LRRK2 and its homolog LRRK1 are deleted selectively in DAergic neurons, offering a new tool to understand the physiopathological role of LRRK2 and the compensating role of LRRK1 in modulating DAergic cell function.

Weaknesses:

The model has no construct validity since loss of function mutations of LRRK2 are well-tolerated in humans and do not lead to PD. The evidence of a Parkinsonian phenotype in these cDKO mice is limited and should be considered preliminary.

Reviewer #2 (Public Review):

Summary:<br /> The authors tried to identify the genetic factors for asthenoteratozoospermia. Using whole-exome sequencing, they analyzed a family with an infertile male and identified CFAP52 variants. They further knockout mouse Cfap52 gene and the homozygous mice phenocopied the patient. CFAP52 interacts with several other sperm proteins to maintain normal sperm morphology. Finally, CFAP52-associated male infertility in humans and mice could be overcome by using intracytoplasmic sperm injections (ICSI).

Strengths:<br /> The major strength of this study is to identify genetic factors contributing to asthenoteratozoospermia, and to generate a mouse knockout model to validate the factor.

Weaknesses:<br /> The authors did not use the OMICS to dissect the potential mechanisms. Instead, they took the advantage of direct co-IP experiment to fish the binding partners. They also did not discuss in detail why other motile cilia have different behavior.

Reviewer #2 (Public Review):

Summary and Strengths:<br /> In this manuscript, Chotiner and colleagues demonstrated the localization of TRIP13 and clarified the phenotypes of Trip13-null mice in mouse meiosis. The meiotic phenotypes of Trip13 have been well characterized using the hypomorph alleles in the literature. However, the null phenotypes have not been examined, and the localization of TRIP13 was not clearly demonstrated. The study fills these important knowledge gaps in the field. The demonstration of TRIP13 localization to SC in mice provides an explanation of how HOMRA domain proteins are evicted from SC in diverse organisms. This conclusion was confirmed in both IF and TRIP13-tagged Tg mice. Further, the phenotypes of Trip13-null mice are very clear. The manuscript is well crafted, and the discussion section is well organized and comprehends the topic in the field. All in all, the manuscript will provide important knowledge in the field of meiosis.

Weaknesses:<br /> The heterozygous phenotypes demonstrate that TRIP13 is a dosage-sensitive regulator of meiosis. In relation to this conclusion, as summarized in the discussion section, other mutants defective in meiotic recombination showed dosage-sensitive phenotypes. However, the authors did not examine meiotic recombination in the Trip13-null mice.

Reviewer #2 (Public Review):

The objective of this study from Lazar-Contes et al. is to examine chromatin accessibility changes in "spermatogonial cells" (SCs) across testis development. Exactly what SCs are, however, remains a mystery. The authors mention in the abstract that SCs are undifferentiated male germ cells and have self-renewal and differentiation activity, which would be true for Spermatogonial STEM Cells (SSCs), a very small subset of total spermatogonia, but then the methods they use to retrieve such cells using antibodies that enrich for undifferentiated spermatogonia encompass both undifferentiated and differentiating spermatogonia. Data in Fig. 1B prove that most (85-95%) are PLZF+, but PLZF is known to be expressed both by undifferentiated and differentiating (KIT+) spermatogonia (Niedenberger et al., 2015; PMID: 25737569). Thus, the bulk RNA-seq and ATAC-seq data arising from these cells constitute the aggregate results comprising the phenotype of a highly heterogeneous mixture of spermatogonia (plus contaminating somatic cells), NOT SSCs. Indeed, Fig. 1C demonstrates this by showing the detection of Kit mRNA (a well-known marker of differentiating spermatogonia - which the authors claim on line 89 is a marker of SCs!), along with the detection of markers of various somatic cell populations (albeit at lower levels). This admixture problem influences the results - the authors show ATAC-seq accessibility traces for several genes in Fig. 2E (exhibiting differences between P15 and Adult), including Ihh, which is not expressed by spermatogenic cells, and Col6a1, which is expressed by peritubular myoid cells. Thus, the methods in this paper are fundamentally flawed, which precludes drawing any firm conclusions from the data about changes in chromatin accessibility among spermatogonia (SCs?) across postnatal testis development. In addition, there already are numerous scRNA-seq datasets from mouse spermatogenic cells at the same developmental stages in question. Moreover, several groups have used bulk ATAC-seq to profile enriched populations of spermatogonia, including from synchronized spermatogenesis which reflects a high degree of purity (see Maezawa et al., 2018 PMID: 29126117 and Schlief et al., 2023 PMID: 36983846 and in cultured spermatogonia - Suen et al., 2022 PMID: 36509798) - so this topic has already begun to be examined. None of these papers was cited, so it appears the authors were unaware of this work. The authors' methodological choice is even more surprising given the wealth of single-cell evidence in the literature since 2018 demonstrating the exceptional heterogeneity among spermatogonia at these developmental stages (the authors DID cite some of these papers, so they are aware). Indeed, it is currently possible to perform concurrent scATAC-seq and scRNA-seq (10x Genomics Multiome), which would have made these data quite useful and robust. As it stands, given the lack of novelty and critical methodological flaws, readers should be cautioned that there is little new information to be learned about spermatogenesis from this study, and in fact, the data in Figures 2-5 may lead readers astray because they do not reflect the biology of any one type of male germ cell. Indeed, not only do these data not add to our understanding of spermatogonial development, but they are damaging to the field if their source and identity are properly understood. Here are some specific examples of the problems with these data:

1. Fig. 2D - Gata4 and Lhcgr are not expressed by germ cells in the testis.

2. Fig. 3A - WT1 is expressed by Sertoli cells, so the change in accessibility of regions containing a WT1 motif suggests differential contamination with Sertoli cells. Since Wt1 mRNA was differentially high in P15 (Fig. 3B) - this seems to be the most likely explanation for the results. How was this excluded?

3. Fig. 3D - Since Dmrt1 is expressed by Sertoli cells, the "downregulation" likely represents a reduction in Sertoli cell contamination in the adult, like the point above. Did the authors consider this?

Reviewer #2 (Public Review):

Summary:

Liao and colleagues generated tagged SMAD1 and SMAD5 mouse models and identified genome occupancy of these two factors in the uterus of these mice using the CUT&RUN assay. The authors used integrative bioinformatic approaches to identify putative SMAD1/5 direct downstream target genes and to catalog the SMAD1/5 and PGR genome co-localization pattern. The role of SMAD1/5 on stromal decidualization was assayed in vitro on primary human endometrial stromal cells. The new mouse models offer opportunities to further dissect SMAD1 and SMAD5 functions without the limitation from SMAD antibodies, which is significant. The CUT&RUN data further support the usefulness of these mouse models for this purpose.

Strengths:<br /> The strength of this study is the novelty of new mouse models and the valuable cistromic data derived from these mice.

Weaknesses:<br /> The weakness of the present version of the manuscript includes the self-limited data analysis approaches such as the proximal promoter based bioinformatic filter and a missed opportunity to investigate the role of SMAD1/5 on determining the genome occupancy of major uterine transcription regulators.

Reviewer #2 (Public Review):

Summary:<br /> The authors investigated the molecular evolution of members of the gasdermin (GSDM) family. By adding the evolutionary time axis of animals, they created a new molecular phylogenetic tree different from previous ones. The analyzed result verified that non-mammalian GSDMAs and mammalian GSDMAs have diverged into completely different and separate clades. Furthermore, by biochemical analyses, the authors demonstrated non-mammalian GSDMA proteins are cleaved by the host-encoded caspase-1. They also showed mammalian GSDMAs have lost the cleavage site recognized by caspase-1. Instead, the authors proposed that the newly appeared GSDMD is now cleaved by caspase-1.

Through this study, we have been able to understand the changes in the molecular evolution of GSDMs, and by presenting the cleavage of GSDMAs through biochemical experiments, we have become able to grasp the comprehensive picture of this family of molecules. However, there are some parts where explanations are insufficient, so supplementary explanations and experiments seem to be necessary.

Strengths:<br /> It has a strong impact in advancing ideas into the study of pyroptotic cell death and even inflammatory responses involving caspase-1.

Weaknesses:<br /> Based on the position of mammalian GSDMA shown in the molecular phylogenetic tree (Figure 1), it may be difficult to completely agree with the authors' explanation of the evolution of GSDMA.

1) Focusing on mammalian GSDMA, this group, and mammalian GSDMD diverged into two clades, and before that, GSDMA/D groups and mammalian GSDMC separated into two, more before that, GSDMB, and further before that, non-mammalian GSDMA, when we checked Figure 1. In the molecular phylogenetic tree, it is impossible that GSDMA appears during evolution again. Mammalian GSDMAs are clearly paralogous molecules to non-mammalian GSDMAs in the figure. If they are bona fide orthologous, the mammalian GSDMA group should show a sub-clade in the non-mammalian GSDMA clade. It is better to describe the plausibility of the divergence in the molecular evolution of mammalian GSDMA in the Discussion section.

2) Regarding (1), it is recommended that the authors reconsider the validity of estimates of divergence dates by focusing on mammalian species divergence. Because the validity of this estimation requires a recheck of the molecular phylogenetic tree, including alignment.

3) If GSDMB and/or GSDMC between non-mammalian GSDMA and mammalian GSDMD as shown in the molecular phylogenetic tree would be cleaved by caspase-1, the story of this study becomes clearer. The authors should try that possibility.

Reviewer #2 (Public Review):

In this work, Chang-Gonzalez and co-workers investigate the role of force in peptide recognition by T-cells using a model T-cell/peptide recognition complex. By applying forces through a harmonic restraint on distances, the authors probe the role of mechanical pulling on peptide binding specificity. They point to a role for force in distinguishing the different roles played by agonist and antagonist peptides for which the bound configuration is not clearly distinguishable. Overall, I would consider this work to be extensive and carefully done, and noteworthy for the number of mutant peptides and conditions probed. From the text, I'm not sure how specific these conclusions are to this particular complex, but I do not think this diminishes the specific studies.

I have a couple of specific comments on the methodology and analysis that the authors could consider:<br /> 1) It is not explained what is the origin of force on the peptide-MHC complex. Although I do know a bit about this, it's not clear to me how the force ends up applied across the complex (e.g. is it directional in any way, on what subdomains/residues do we expect it to be applied), and is it constant or stochastic. I think it would be important to add some discussion of this and how it translates into the way the force is applied here (on terminal residues of the complex).

2) In terms of application of the force, I find the use of a harmonic restraint and then determining a distance at which the force has a certain value to be indirect and a bit unphysical. As just mentioned, since the origin of the force is not a harmonic trap, it would be more straightforward to apply a pulling force which has the form -F*d, which would correspond to a constant force (see for example comment articles 10.1021/acs.jpcb.1c10715, 10.1021/acs.jpcb.1c06330). While application of a constant force will result in a new average distance, for small forces it does so in a way that does not change the variance of the distance whereas a harmonic force pollutes the variance (see e.g. 10.1021/ct300112v in a different context). A constant force could also shift the system into a different state not commensurate with the original distance, so by applying a harmonic trap, one could be keeping ones' self from exploring this, which could be important, as in the case of certain catch bond mechanisms. While I certainly wouldn't expect the authors to redo these extensive simulations, I think they could at least acknowledge this caveat, and they may be interested in considering a comparison of the two ways of applying a force in the future.

3) For the PCA analysis, I believe the authors learn separate PC vectors from different simulations and then take the dot product of those two vectors. Although this might be justified based on the simplified coordinate upon which the PCA is applied, in general, I am not a big fan of running PCA on separate data sets and then comparing the outputs, as the meaning seems opaque to me. To compare the biggest differences between many simulations, it would make more sense to me to perform PCA on all of the data combined, and see if there are certain combinations of quantities that distinguish the different simulations. Alternatively and probably better, one could perform linear discriminant analysis, which is appropriate in this case because one already knows that different simulations are in different states, and hence the LDA will directly give the linear coordinate that best distinguishes classes.

Reviewer #2 (Public Review):

In HD patients, immune pathways alteration leads to higher susceptibility to infection and lower response to the COVID-19 mRNA vaccine. Therefore, it is important to understand the immune response to vaccines in ESRD patients against the COVID-19 pandemic. In this MS, the authors recruited 20 HD patients and cohort-matched controls to perform multiple experimental studies (including transcriptomic analysis, RNAseq, and Anti-Spike (trimer) IgG Titer Quantification) to investigate how immune pathways alteration in HD patients after COVID-19 mRNA vaccine injection. They demonstrate differing expression of BTMs and differing time courses of immune responses to the BTN162b2 mRNA COVID-19 vaccination in maintenance hemodialysis subjects (HD) compared to controls, which warrants further characterization of the immune dysregulation of ESRD and immune biomarkers. Overall, the study is well designed, and the result has potential clinical value and will interest nephrologists. The major concern of this study is the cohort set up. The sample sizes of recruited candidates are relatively small, and no validation cohort was designed. More importantly, between the two groups, the race distribution is uneven. For example, 10 black and 2 white HD patients were included, but accordingly, 3 black and 8 white people were recruited as controls. In such a small size of the clinical study, this kind of unevenness might cause potential issues in concluding. In addition, the control cohort also included 1 diabetes and 4 hypertension, patients. Will these existing primary diseases in controls cause noise in the data analysis because these metabolic diseases also can directly cause immune system dysfunction? In addition, there were 8 HD patients and 5 HC with a positive test of SARS-CoV-2 from 8 months to four weeks preceding vaccination. How long does the immune response last after being infected with COVID-19? Several studies have found that people infected with COVID-19 continue to produce antibodies to the virus for seven or eight months after recovery. Therefore, people with a COVID-19 history might not be suitable for this trial.

Reviewer #2 (Public Review):

This study proposes to evaluate and compare different replay methods in the absence of "ground truth" using data from hippocampal recordings of rodents that were exposed to two different tracks on the same day. The study proposes to leverage the potential of Bayesian methods to decode replay and reactivation in the same events. They find that events that pass a higher threshold for replay typically yield a higher measure of reactivation. On the other hand, events from the shuffled data that pass thresholds for replay typically don't show any reactivation. While well-intentioned, I think the result is highly problematic and poorly conceived.

The work presents a lot of confusion about the nature of null hypothesis testing and the meaning of p-values. The prescription arrived at, to correct p-values by putting animals on two separate tracks and calculating a "sequence-less" measure of reactivation are impractical from an experimental point of view, and unsupportable from a statistical point of view. Much of the observations are presented as solutions for the field, but are in fact highly dependent on distinct features of the dataset at hand. The most interesting observation is that despite the existence of apparent sequences in the PRE-RUN data, no reactivation is detectable in those events, suggesting that in fact they represent spurious events. I would recommend the authors focus on this important observation and abandon the rest of the work, as it has the potential to further befuddle and promote poor statistical practices in the field.

The major issue is that the manuscript conveys much confusion about the nature of hypothesis testing and the meaning of p-values. It's worth stating here the definition of a p-value: the conditional probability of rejecting the null hypothesis given that the null hypothesis is true. Unfortunately, in places, this study appears to confound the meaning of the p-value with the probability of rejecting the null hypothesis given that the null hypothesis is NOT true-i.e. in their recordings from awake replay on different mazes. Most of their analysis is based on the observation that events that have higher reactivation scores, as reflected in the mean log odds differences, have lower p-values resulting from their replay analyses. Shuffled data, in contrast, does not show any reactivation but can still show spurious replays depending on the shuffle procedure used to create the surrogate dataset. The authors suggest using this to test different practices in replay detection. However, another important point that seems lost in this study is that the surrogate dataset that is contrasted with the actual data depends very specifically on the null hypothesis that is being tested. That is to say, each different shuffle procedure is in fact testing a different null hypothesis. Unfortunately, most studies, including this one, are not very explicit about which null hypothesis is being tested with a given resampling method, but the p-value obtained is only meaningful insofar as the null that is being tested and related assumptions are clearly understood. From a statistical point of view, it makes no sense to adjust the p-value obtained by one shuffle procedure according to the p-value obtained by a different shuffle procedure, which is what this study inappropriately proposes. Other prescriptions offered by the study are highly dataset and method dependent and discuss minutiae of event detection, such as whether or not to require power in the ripple frequency band.

Reviewer #2 (Public Review):

This study proposes to evaluate and compare different replay methods in the absence of "ground truth" using data from hippocampal recordings of rodents that were exposed to two different tracks on the same day. The study proposes to leverage the potential of Bayesian methods to decode replay and reactivation in the same events. They find that events that pass a higher threshold for replay typically yield a higher measure of reactivation. On the other hand, events from the shuffled data that pass thresholds for replay typically don't show any reactivation. While well-intentioned, I think the result is highly problematic and poorly conceived.

The work presents a lot of confusion about the nature of null hypothesis testing and the meaning of p-values. The prescription arrived at, to correct p-values by putting animals on two separate tracks and calculating a "sequence-less" measure of reactivation are impractical from an experimental point of view, and unsupportable from a statistical point of view. Much of the observations are presented as solutions for the field, but are in fact highly dependent on distinct features of the dataset at hand. The most interesting observation is that despite the existence of apparent sequences in the PRE-RUN data, no reactivation is detectable in those events, suggesting that in fact they represent spurious events. I would recommend the authors focus on this important observation and abandon the rest of the work, as it has the potential to further befuddle and promote poor statistical practices in the field.

The major issue is that the manuscript conveys much confusion about the nature of hypothesis testing and the meaning of p-values. It's worth stating here the definition of a p-value: the conditional probability of rejecting the null hypothesis given that the null hypothesis is true. Unfortunately, in places, this study appears to confound the meaning of the p-value with the probability of rejecting the null hypothesis given that the null hypothesis is NOT true-i.e. in their recordings from awake replay on different mazes. Most of their analysis is based on the observation that events that have higher reactivation scores, as reflected in the mean log odds differences, have lower p-values resulting from their replay analyses. Shuffled data, in contrast, does not show any reactivation but can still show spurious replays depending on the shuffle procedure used to create the surrogate dataset. The authors suggest using this to test different practices in replay detection. However, another important point that seems lost in this study is that the surrogate dataset that is contrasted with the actual data depends very specifically on the null hypothesis that is being tested. That is to say, each different shuffle procedure is in fact testing a different null hypothesis. Unfortunately, most studies, including this one, are not very explicit about which null hypothesis is being tested with a given resampling method, but the p-value obtained is only meaningful insofar as the null that is being tested and related assumptions are clearly understood. From a statistical point of view, it makes no sense to adjust the p-value obtained by one shuffle procedure according to the p-value obtained by a different shuffle procedure, which is what this study inappropriately proposes. Other prescriptions offered by the study are highly dataset and method dependent and discuss minutiae of event detection, such as whether or not to require power in the ripple frequency band.

Reviewer #2 (Public Review):

Summary:

The work demonstrates that high-intensity ultrasound produces a release of extracellular vesicles from murine myotubes that is dependent on ultrasound intensity. It shows that this increase in extracellular vesicles is abolished in a nominally zero Ca2+ solution. It then shows that these vesicles reduce the mRNA levels of IL-1b and IL-6 in murine bone marrow-derived macrophages and uses a dilution technique to demonstrate that the number, but not the type of vesicles is responsible for this change in mRNA expression. It also compares the miRNA levels in constitutively-released vesicles with those released by high-intensity ultrasound.

Strengths:

The experiments are logically sequenced. It is very helpful to see assessment of the viability of the preparations.<br /> The results are presented fairly clearly and the statistical approach is described. The findings are reasonably clear and the writing is succinct.

Weaknesses:

The work is quite limited in scope and of limited novelty, largely recapitulating work from the first-named author's own recent publications.<br /> Thus, perhaps the most significant weakness of this study is that it makes claims of mechanisms, or of clinical or therapeutic relevance, that are not supported or even addressed by the study.

The aspects of the current work which are novel are hard to identify because the statement of aims is too broad and therefore encapsulates previous work. In addition, the introduction and discussion are vague and fail, for example, to mention the cell types used in the previous studies that are quoted. This means that it is not obvious from the Introduction whether the present study is at all novel.

The size of the study is quite small, with most experiments employing n = 4. This inevitably means that, for example, there is no significant effect of the lower power levels of ultrasound despite shifts in the mean values that might be of interest. Thus, the study appears underpowered. This problem is compounded by a failure to use appropriate analysis methods in the studies looking at dose-responses, where a regression analysis might be more appropriate than multiple individual t-tests / ANOVA.

The assessment of the role of Ca2+ is important but incomplete. Measurement of whole-cell Ca2+ levels is not really a substitute for measuring cytosolic Ca2+ as cell volume changes and sarcoplasmic reticulum Ca2+ changes would greatly influence the possible meaning of the findings. Furthermore, a statement that Ca2+ increase causes the vesicle release could only be supported by experiments that increase intracellular Ca2+, such as the use of a Ca2+ ionophore.

mRNA expression levels of IL-1b and IL-6 are reported. There should also be a report of a non-inflammatory mRNA to act as a control.

Reviewer #2 (Public Review):

The flowering plant Capsella bursa-pastoris is an allotetraploid formed from the genomes of Capsella orientalis and Capsella grandiflora. An outstanding question in the evolution of allotetraploids is the relative contribution of immediate consequences of allopolyploidization vs. long-term evolution after the event. The authors address this question by re-synthesizing the allotetraploid in the lab using the two progenitor species, and comparing its phenotypic and gene expression variation to naturally occurring C. bursa-pastoris. They find evidence primarily for long-term phenotypic evolution towards a selfing syndrome in C. bursa-pastoris, and a combination of short and long-term changes to gene expression.

The manuscript is thorough and provides lots of new insights into the mechanisms driving evolution in allopolyploids. I especially appreciated the detailed examination of different mechanisms driving gene expression variation. There are some important limitations of the experimental design related to independent evolution of the progenitor species and effects of the colchicine treatment used to induce polyploidy, but these are well-addressed in the Discussion.

Reviewer #2 (Public Review):

Summary:<br /> The authors sampled multiple populations of maize and teosinte across Mexico, aiming to characterise the geographic scale of local adaptation, patterns of selective sweeps, and modes of convergent evolution between populations and subspecies.

Strengths & Weaknesses:<br /> The population genomic methods are standard and appropriate, including Fst, Tajima's D, α, and selective sweep scans. The whole genome sequencing data seems high quality. However, limitations exist regarding limited sampling, potential high false-positive sweep detection rates, and weak evidence for some conclusions, like the role of migration in teosinte adaptation.

Aims & Conclusions:<br /> The results are interesting in supporting local adaptation at intermediate geographic scales, widespread convergence between populations, and standing variation/gene flow facilitating adaptation. However, more rigorous assessments of method performance would strengthen confidence. Connecting genetic patterns to phenotypic differences would also help validate associations with local adaptation.

Impact & Utility:<br /> This work provides some of the first genomic insights into local adaptation and convergence in maize and teosinte. However, the limited sampling and need for better method validation currently temper the utility and impact. Broader sampling and connecting results to phenotypes would make this a more impactful study and valuable resource. The population genomic data itself provides a helpful resource for the community.

Additional Context:<br /> Previous work has found population structure and phenotypic differences consistent with local adaptation in maize and teosinte. However, genomic insights have been lacking. This paper takes initial steps to characterise genomic patterns but is limited by sampling and validation. Additional work building on this foundation could contribute to understanding local adaptation in these agriculturally vital species.

Reviewer #2 (Public Review):

Summary:

The study demonstrates how inconclusive replications of studies initially with p > 0.05 can be and employs equivalence tests and Bayesian factor approaches to illustrate this concept. Interestingly, the study reveals that achieving a success rate of 11 out of 15, or 73%, as was accomplished with the non-significance criterion from the RPCB (Reproducibility Project: Cancer Biology), requires unrealistic margins of Δ > 2 for equivalence testing.

Strengths:

The study uses reliable and sharable/open data to demonstrate its findings, sharing as well the code for statistical analysis. The study provides sensitivity analysis for different scenarios of equivalence margin and alfa level, as well as for different scenarios of standard deviations for the prior of Bayes factors and different thresholds to consider. All analysis and code of the work is open and can be replicated. As well, the study demonstrates on a case-by-case basis how the different criteria can diverge, regarding one sample of a field of science: preclinical cancer biology. It also explains clearly what Bayes factors and equivalence tests are.

Weaknesses:

It would be interesting to investigate whether using Bayes factors and equivalence tests in addition to p-values results in a clearer scenario when applied to replication data from other fields. As mentioned by the authors, the Reproducibility Project: Experimental Philosophy (RPEP) and the Reproducibility Project: Psychology (RPP) have data attempting to replicate some original studies with null results. While the RPCB analysis yielded a similar picture when using both criteria, it is worth exploring whether this holds true for RPP and RPEP. Considerations for further research in this direction are suggested. Even if the original null results were excluded in the calculation of an overall replicability rate based on significance, sensitivity analyses considering them could have been conducted. The present authors can demonstrate replication success using the significance criteria in these two projects with initially p < 0.05 studies, both positive and non-positive.

Other comments:

- Introduction: The study demonstrates how inconclusive replications of studies initially with p > 0.05 can be and employs equivalence tests and Bayesian factor approaches to illustrate this concept. Interestingly, the study reveals that achieving a success rate of 11 out of 15, or 73%, as was accomplished with the non-significance criterion from the RPCB (Reproducibility Project: Cancer Biology), requires unrealistic margins of Δ > 2 for equivalence testing.

- Overall picture vs. case-by-case scenario: An interesting finding is that the authors observe that in most cases, there is no substantial evidence for either the absence or the presence of an effect, as evidenced by the equivalence tests. Thus, using both suggested criteria results in a picture similar to the one initially raised by the paper itself. The work done by the authors highlights additional criteria that can be used to further analyze replication success on a case-by-case basis, and I believe that this is where the paper's main contributions lie. Despite not changing the overall picture much, I agree that the p-value criterion by itself does not distinguish between (1) a situation where the original study had low statistical power, resulting in a highly inconclusive non-significant result that does not provide evidence for the absence of an effect and (2) a scenario where the original study was adequately powered, and a non-significant result may indeed provide some evidence for the absence of an effect when analyzed with appropriate methods. Equivalence testing and Bayesian factor approaches are valuable tools in both cases.

Regarding the 0.05 threshold, the choice of the prior distribution for the SMD under the alternative 𝐻1 is debatable, and this also applies to the equivalence margin. Sensitivity analyses, as highlighted by the authors, are helpful in these scenarios.

Reviewer #2 (Public Review):

Summary:<br /> McGinnis and colleagues conducted a study to elucidate the precise mechanism through which SEACIT detects amino acids and regulates TORC1 signaling in yeast. In their research, the authors made a noteworthy discovery by identifying the conserved 5'-3' RNA exonuclease Xrn1 as a novel regulator of TORC1 activity, particularly in response to stress-induced autophagy. The study revealed that the impact of Xrn1 on TORC1 is contingent on its catalytic activity rather than the degradation of any specific category of mRNAs. Instead, Xrn1 plays a pivotal role in modulating the nucleotide-binding state of the Gtr1/2 complex. This modulation is crucial for the complex's interaction with and subsequent activation of TORC1.

Strengths:<br /> This study holds considerable potential as it illuminates an intriguing function of Xrn1 in nutrient sensing and growth control, expanding beyond its conventional role in RNA degradation. Furthermore, the research suggests a novel pathway through which RNA metabolism can influence methionine signaling to activate TORC1.

Weaknesses/General comments:<br /> 1) Previous work has shown that SAMTOR, upstream of mTORC1 in mammalian cells, senses methionine abundance through SAM levels (PMID: 29123071). However, this study suggests that Xrn1 senses and signals methionine to regulate mTORC1 signaling independently of SAM abundance. This finding appears to contradict the mentioned previous work. The authors should address this discrepancy. Moreover, the title of this manuscript does not seem to fit with actual findings. In the title, the authors mention that Xrn1 regulates TORC1 in response to SAM availability, but SAM levels do not seem to matter for Xrn1-dependent regulation of autophagy and TORC1.<br /> 2) This group has previously shown that the addition of methionine stimulates the synthesis of S-adenosylmethionine (SAM), which inhibits autophagy and promotes growth through the action of the methyltransferase Ppm1p, which modifies the catalytic subunit of PP2A in tune with SAM levels (PMID: 23870128). Since Xrn1 controls autophagy in a methionine-dependent manner, the authors should assess the effects of Xrn1 on SAM-dependent methylation of PP2A?<br /> 3) The authors should measure the effects of Xrn1 and TORC1 regulation on the methionine-SAM cycle activity through an isotope tracing approach, possibly by using U-13C-methionine.<br /> 4) The authors use mainly the GFP cleavage assay from Idh1-GFP to assess mitochondria degradation (or mitophagy) and generalize that autophagy is induced. Other assays should be employed more notably to assess globally non-mitochondrial specific degradation. For example, the authors could employ the Pho8∆60 assay.<br /> 5) In several blots (Panel 3D, 4D, 4B, 4F), the authors assess autophagy through GFP cleavage from Idh1-GFP but do not assess TORC1 activity in the same conditions. Showing autophagy induction and TORC1 activity on the same panels would be preferable.

Specific comments:<br /> 1) Panel 5E: As a control, the authors should use DNA instead of NMPs.<br /> 2) Panel S3B: Contrary to what is indicated in the text, this panel does not display ATG mRNA levels.<br /> 3) Panel S5K is not cited in the text. The rationale behind measuring the steady-state levels of GTP and GDP is not explained.<br /> Several panels are not subjected to statistical analysis. It is important for the authors to ensure that appropriate statistical methods are applied.

Reviewer #2 (Public Review):

Summary:<br /> This manuscript clearly shows that Trypanosoma PKA is controlled by nucleoside analogues rather than cyclic nucleotides, which are the primary allosteric effectors of human PKA and PKG. The authors demonstrate that the inosine, guanosine, and adenosine nucleosides bind with high affinity and activate PKA in the tropical pathogens T. brucei, T. cruzi and Leishmania. The underlying determinants of nucleoside binding and selectivity are dissected by solving the crystal structure of T. cruzi PKAR(200-503) and T. brucei PKAR(199-499) bound to inosine at 1.4 Å and 2.1 Å resolution and through comparative mutational analyses. Of particular interest is the identification of a minimal subset of 2-3 residues that controls nucleoside vs. cyclic nucleotide specificity.

Strengths:<br /> The significance of this study lies not only in the structure-activity relationships revealed for important targets in several parasite pathogens but also in the understanding of CNB's evolutionary role.

Weaknesses:<br /> The main missing piece is the model for activation of the kinetoplastid PKA which remains speculative in the absence of a structure for the trypanosomatid PKA holoenzyme complex. However, this appears to be beyond the scope of this manuscript, which is already quite dense.

Reviewer #2 (Public Review):

Thawornwattana et al. reconstruct a species tree of the genus Heliconius using the full-likelihood multispecies coalescent, an exciting approach for genera with a history of extensive gene flow and introgression. With this, they obtain a species tree with H. aoede as the earliest diverging lineage, in sync with ecological and morphological characters. They also add resolution to the species relationships of the melpomene-silvaniform clade and quantify introgression events. Finally, they trace the origins of an inversion on chromosome 15 that exists as a polymorphism in H. numata, but is fixed in other species. Overall, obtaining better species tree resolutions and estimates of gene flow in groups with extensive histories of hybridization and introgression is an exciting avenue. Being able to control for ILS and get estimates between sister species are excellent perks. One overall quibble is that the paper seems to be best suited to a Heliconius audience, where past trees are easily recalled, or members of the different clades are well known.

Overall, applying approaches such as these to gain greater insight into species relationships with extensive gene flow could be of interest to many researchers.

Reviewer #2 (Public Review):

Summary

The findings reported by Diaz-Vegas et al. extend those described in a previous paper from the same group establishing a role for mitochondrial CoQ depletion in the development of insulin resistance in muscle and adipose tissue (Fazakerley, 2018). In this new report, investigators sought to determine whether CoQ depletion contributes to insulin resistance caused by palmitate exposure and/or intracellular ceramide accumulation. To this end, researchers employed a widely used in vitro model of insulin resistance wherein L6 myocytes develop impaired Glut4 translocation upon exposure to palmitate (in this case, 150 uM for 16 hours). This model was combined with a variety of pharmacologic and genetic manipulations aimed at augmenting or inhibiting CoQ biosynthesis and/or ceramide biosynthesis, specifically in mitochondria. This series of experiments produced a valuable and provocative body of evidence positioning CoQ depletion downstream of mitochondrial ceramide accumulation and necessary for both palmitate- and ceramide-induced insulin resistance in L6 myocytes. Investigators concluded that mitochondrial ceramides, CoQ depletion and respiratory dysfunction are part of a core pathway leading to insulin resistance.

Strengths

The study provides exciting, first-time evidence linking palmitate-induced insulin resistance to ceramide accumulation within the mitochondria and subsequent depletion of CoQ. Ceramide accumulation specifically in mitochondria was found to be necessary and sufficient to cause insulin resistance in cultured L6 myocytes.

The in vitro experiments featured a set of mitochondrial-targeted genetic manipulations that permitted up/down-regulation of ceramide levels specifically in the mitochondrial compartment. Genetically induced mitochondrial ceramide accumulation led to CoQ depletion, which was accompanied by increased ROS production and diminution of ETC proteins and OXPHOS capacity and impaired insulin action, thereby establishing cause/effect.

Analysis of mitochondria isolated from human muscle biopsies obtained from individuals with disparate metabolic phenotypes revealed a positive correlation between complex I proteins and insulin sensitivity and a negative correlation with mitochondrial ceramide content. While it is likely that many factors contribute to these correlations, the results support the possibility that the ceramide/CoQ mechanism might be relevant to glucose control in humans.

Investigators were responsive to the reviewers' queries and critiques and performed additional experiments to bolster the interpretations and conclusions put forth in the manuscript. These included experiments to confirm that mito-targeted SMPD5 does not cause toxicity in L6 myocytes, and further studies using targeted metabolomic and lipidomic analyses to investigate the impact of ceramide depletion on CoQ levels in mice fed a high-fat diet and treated with P053 (a selective inhibitor of CerS1). The results were consistent with the in vitro findings.

Overall, these important findings offer valuable new insights into mechanisms that connect ceramides to insulin resistance and mitochondrial dysfunction, and could inform new therapeutic approaches towards improved glucose control.

Weaknesses

The mechanistic aspect of the work and conclusions put forth rely heavily on studies performed in cultured myocytes, which are highly glycolytic and generally viewed as an imperfect model for studying muscle metabolism and insulin action. Nonetheless, results from the cell culture model are generally convincing and align with the descriptive data from studies in animal models. Overall, the findings provide a strong rationale for moving this line of investigation into mouse gain/loss of function models.

One caveat of the approach taken is that exposure of cells to palmitate alone is not reflective of in vivo physiology. It would be interesting to know if similar effects on CoQ are observed when cells are exposed to a more physiological mixture of fatty acids that includes a high ratio of palmitate, but better mimics in vivo nutrition.

Reviewer #2 (Public Review):

Summary:

The present study explores the molecular function of LRRC23 in male fertility, specifically in the context of the regulation of spermiogenesis. The author initiates the investigation by identifying LRRC23 mutations as a potential cause of male sterility based on observations made in closely related individuals affected by asthenozoospermia (ASZ). To further investigate the function of LRRC23 in spermatogenesis, mutant mice expressing truncated LRRC23 proteins are created, aligning with the identified mutation site. Consequently, the findings confirm the deleterious effects of LRRC23 mutations on sperm motility in these mice while concurrently observing no significant abnormalities in the overall flagella structure. Furthermore, the study reveals LRRC23's interaction with the RS head protein RSPH9 and its active involvement in the assembly of the axonemal RS. Notably, LRRC23 mutations result in the loss of the RS3 head structure and disruption of the RS2-RS3 junction structure. Therefore, the author claimed that LRRC23 is an indispensable component of the RS3 head structure and suggests that mutations in LRRC23 underlie sterility in mice.

Strengths:

The key contribution of this article lies in confirming LRRC23's involvement in assembling the RS3 head structure in sperm flagella. This finding represents a significant advancement in understanding the complex architecture of the RS3 structural complex, building upon previous studies. Moreover, the article's topic is interesting and originates from clinical research, which holds significant implications for potential clinical applications.

Reviewer #2 (Public Review):

Summary:

Shotgun data have been analysed to obtain fungal and bacterial organisms abundance. Through their metabolic functions and through co-occurrence networks, a functional relationship between the two types of organisms can be inferred. By means of metabolomics, function-related metabolites are studied in order to deepen the fungus-bacteria synergy.

Strengths:

Data obtained in bacteria correlate with data from other authors.<br /> The study of metabolic "interactions" between fungi and bacteria is quite new.<br /> The inclusion of metabolomics data to support the results is a great contribution.

Weaknesses:

Most of them have been solved in the revision, but for the future it will be nice to integrate this data with others from 16s.

Reviewer #2 (Public Review):

The manuscript describes more fully the relationship between zinc fluxes and calcium oscillations during egg activation by directly manipulating the level of zinc ions inside and outside the cell with chelators and ionophores and then measuring resulting changes in Ca++ oscillations. The authors have provided solid evidence consistent with their hypothesis that zinc ions regulate Ca++ oscillations by directly modulating the gating of the IP3-R which is the main calcium channel responsible for calcium release into the cytoplasm. The authors employ well established methods of calcium measurement along with various chelators, ionophores and a wide variety of methods that cause egg activation to demonstrate that an optimal level of zinc ions are required for Ca++ oscillations to occur.

Helpfully, the authors provide a model to explain their observations in Figure 7. In the model, the increase in zinc during maturation is permissive for later IP3-R gating in response to activation. The experiments with TPEN solidly demonstrate that Zn is required because lowering free zinc, (as indicated by Fluozin staining), abrogates Ca++ oscillations. This is true regardless of the method of activation. What is not clearly described in the model or in the manuscript is whether the levels of zinc at MII are simply permissive for IP3-R gating or whether there is a more acute relationship between zinc fluxes and Ca++ oscillations. In the original paper describing the zinc spark (Kim et al., ACS Chem Biol 6:716-723), the authors show that zinc efflux very closely mirrors Ca++ oscillations suggesting a more active relationship.

The role of TRPv3 and Trpm7 in Zn homeostasis during egg activation seems to be minor. Labile zinc accumulation, as measured by fluozin-3 staining, is reduced in the dKO eggs, but is this modest decrease in labile Zn responsible for the changes in Ca release after Tg treatment? There is an increase in the amplitude of Tg-induced Ca release in dKO eggs. This argues that there is not an inhibitory effect in the dKO mice. That it takes a little longer to reach Ca peak could be due to the greater amount of Ca being released.

The effect of PyT on the apparent rise in cytoplasmic Ca++ in Figure 6 is interpreted as caused by an artifact of high Zn concentrations. However, it is not clear that 0.05 uM PyT would necessarily increase cytoplasmic Zn to the point where FURA-2 fluorescence would increase. A simpler interpretation is that PyT allows sufficient Zn to enter the cell and keeps the IP3-R channels open causing a sustained rise in cytoplasmic Ca and preventing oscillations in Ca++. This interpretation would also preclude inhibitory effects of high Zn concentrations as shown in Figure 7 which may or may not be present but are simply speculation.

Overall, this study significantly advances our understanding of egg activation and could lead to better ways of in vitro egg activation in women undergoing assisted reproduction.

Reviewer #2 (Public Review):

Verdikt et al. focused on the influence of Δ9-THC, the most abundant phytocannabinoid, on early embryonic processes. The authors chose an in vitro differentiation system as model, and compared the proliferation rate, metabolic status and transcriptional level in ESCs, exposure to Δ9-THC. They also evaluated the change of metabolism and transcriptome in PGCLCs derived from Δ9-THC-exposed cells. All the methods in this paper do not involve the differentiation of ESCs to lineage specific cells. So the results cannot demonstrate the impact of Δ9-THC on postimplantation developmental stages. In brief, the authors want to explore the impact of Δ9-THC on preimplantation developmental stages, but they only detected the change in ESCs and PGCLCs derived from ESCs, exposure to Δ9-THC, which showed the molecular characterization of the impact of Δ9-THC exposure on ESCs and PGCLCs.

Reviewer #2 (Public Review):

Spermatogenesis is a process of cell differentiation necessary to produce fertile spermatozoa. It consists of three parts, the last of which is called spermiogenesis, in which the size, shape, and organelle composition of the spermatids undergo significant changes that result in the formation of fully elongated spermatozoa. Defects in spermatogenesis or spermiogenesis can lead to male infertility. In this study, Li et al. identified FBXO24 as a highly expressed protein in human and mouse testis that is required for modulating alternative gene splicing in round spermatids through interaction with various splicing factors. They also found that deletion of FBXO24 in mice results in disorganized mitochondrial packing along the midpiece of the tail and chromatoid body architecture, which may account for the observed male sterility. The authors discovered that FBXO24 interacts with the subunits of MIWI and SCF and is required for normal piRNA biogenesis.

The major strengths of the study are the rigorous phenotypic and molecular analysis by using two complementary animal models (knock-out mouse model but also HA-tagged transgenic mouse model) to pinpoint the protein levels and localization in time and space during normal spermatogenesis and when the protein is absent.

The minor weakness of the study is inconsistent use of terminology throughout the manuscript, occasional logic-jump in their flow, and missing detailed description in methodologies used either in the text or Materials and Methods section, which can be easily rectified.

Overall, this study highlights the relevance and importance of FBXO24 in male fertility and provides a better understanding of the MIWI/piRNA pathway, mitochondrial organization, and chromatin condensation in mouse spermatozoa during spermiogenesis.

Reviewer #2 (Public Review):

Steinemann, Stine, and their co-authors studied the noisy accumulation of sensory evidence during perceptual decision-making using Neuropixels recordings in awake, behaving monkeys. Previous work has largely focused on describing the neural underpinnings through which sensory evidence accumulates to inform decisions, a process which on average resembles the systematic drift of a scalar decision variable toward an evidence threshold. The additional order of magnitude in recording throughput permitted by the methodology adopted in this work offers two opportunities to extend this understanding. First, larger-scale recordings allow for the study of relationships between the population activity state and behavior without averaging across trials. The authors' observation here of covariation between the trial-to-trial fluctuations of activity and behavior (choice, reaction time) constitutes interesting new evidence for the claim that neural populations in LIP encode the behaviorally-relevant internal decision variable. Second, using Neuropixels allows the authors to sample LIP neurons with more diverse response properties (e.g. spatial RF location, motion direction selectivity), making the important question of how decision-related computations are structured in LIP amenable to study. For these reasons, the dataset collected in this study is unique and potentially quite valuable.

However, the analyses at present do not convincingly support two of the manuscript's key claims: (1) that "sophisticated analyses of the full neuronal state space" and "a simple average of Tconin neurons' yield roughly equivalent representations of the decision variable; and (2) that direction-selective units in LIP provide the samples of instantaneous evidence that these Tconin neurons integrate. Supporting claim (1) would require results from sophisticated population analyses leveraging the full neuronal state space; however, the current analyses instead focus almost exclusively on 1D projections of the data. Supporting claim (2) convincingly would require larger samples of units overlapping the motion stimulus, as well as additional control analyses.

Specific shortcomings are addressed in further detail below:

1) The key analysis-correlation between trial-by-trial activity fluctuations and behavior, presented in Figure 5-is opaque, and would be more convincing with negative controls:

To strengthen the claim that the relationship between fluctuations in (a projection of) activity and fluctuations in behavior is significant/meaningful, some evidence should be brought that this relationship is specific - e.g. do all projections of activity give rise to this relationship (or not), or what level of leverage is achieved with respect to choice/RT when the trial-by-trial correspondence with activity is broken by shuffling.

2) The choice to perform most analysis on 1D projections of population activity is not wholly appropriate for this unique type of dataset, limiting the novelty of the findings, and the interpretation of similarity between results across choices of projection appears circular:

The bulk of the analyses (Figure 2, Figure 3, part of Figure 4, Figure 5, Figure 6) operate on one of several 1D projections of simultaneously-recorded activity. Unless the embedding dimension of these datasets really does not exceed 1 (dimensionality using e.g. participation ratio in each session is not quantified), it is likely that these projections elide meaningful features of LIP population activity. Further, additional evidence/analysis would help to strengthen the authors' interpretation of the observed similarity of results across these 1D projections. For one, the rationale behind deriving Sramp was based on the ramping historically observed in Tin neurons during this task, so should be expected to resemble Tin. Second, although Tin does not comprise the majority of neurons recorded in each session, it does comprise the largest fraction of the neuron groups (e.g. Tin, Min, etc) sampled during most sessions, so SPC1 should be expected to resemble Tin more than it does the other neuron groups. Additional/control analyses will be important for strongly supporting the claim that the approximate equality between the population DV and the average of Tin units is meaningful. The analysis presented in Figure S7 is an important step toward this, demonstrating that SPC1 isn't just reflecting the activity of Tin, but would make the point more strongly with some additional analysis. Are the magnitudes of weights assigned to units in Tin larger than in the other groups of units with pre-selected response properties? What is their mean weighting magnitude, in comparison with the mean weight magnitude assigned to other groups? What is the null level of correspondence observed between weight magnitude and assignment to Tin (e.g. a negative control, where the identities of units are scrambled)?

A secondary approach could also get at this point (the small Tin group furnishes a DV very similar to the overall population DV) from a different direction: computing SPC1 using only neurons *not* in Tin, and repeating the analysis performed with the other 3 1D projections of the data currently in Figure 5. Observing similar results for this 4th projection would strengthen the evidence supporting the interpretation the authors adopt.

3) The principal components analysis normalization procedure is unclear, and potentially incorrect and misleading:

Why use the chosen normalization window (+/- 25ms around 100ms after motion stimulus onset) for standardizing activity for PCA, rather than the typical choice of mean/standard deviation of activity in the full data window? This choice would specifically squash responses for units with a strong visual response, which distorts the covariance matrix, and thus the principal components that result. This kind of departure from the standard procedure should be clearly justified: what do the principal components look like when a standard procedure is used, and why was this insufficient/incorrect/unsuitable for this setting?

4) Analysis conclusions would generally be stronger with estimates of variability and control analyses: This applies broadly to Figures 2-6.

Reviewer #2 (Public Review):

Summary:<br /> Cells cultured in high glucose tend to repress mitochondrial biogenesis and activity, a prevailing phenotype type called Crabree effect that is observed in different cell types and cancer. Many signaling pathways have been put forward to explain this effect. Vengayil et al proposed a new mechanism involved in Ubp3/Ubp10 and phosphate that controls the glucose repression of mitochondria. The central hypothesis is that ∆ubp3 shifts the glycolysis to trehalose synthesis, therefore leading to the increase of Pi availability in the cytosol, then mitochondria receive more Pi, and therefore the glucose repression is reduced.

Strengths:<br /> The strength is that the authors used an array of different assays to test their hypothesis. Most assays were well-designed and controlled.

Weaknesses:<br /> I think the main conclusions are not strongly supported by the current dataset.

1. Although the authors discovered ∆ubp3 cells have higher Pi and mitochondrial activity than WT in high glucose, it is not known if WT cultured in different glucose concentration also change Pi that correlate with the mitochondrial activity. The focus of the research on ∆ubp3 is somewhat artificial because ∆ubp3 not only affects glycolysis and mitochondria, but many other cellular pathways are also changed. There is no idea whether culturing cells in low glucose, which de-repress the mitochondrial activity, involves Ubp3 or not. Similarly, the shift of glycolysis to trehalose synthesis is also not relevant to the WT cells cultured in a low-glucose situation.

2. The central hypothesis that Pi is the key constraint behind the glucose repression of mitochondrial biogenesis/activity is supported by the data that limiting Pi will suppress mitochondrial activity increase in these conditions (e.g., ∆ubp3). However, increasing the Pi supply failed to increase mitochondrial activity. The explanation put forward by the authors is that increased Pi supply will increase glycolysis activity, and somehow even reduce the mitochondrial Pi. I cannot understand why only the increased Pi supply in ∆ubp3, but not the increased Pi by medium supplement, can increase mitochondrial activity. The authors said "...that ubp3Δ do not increase mitochondrial Pi by merely increasing the Pi transporters, but rather by increasing available Pi pools". They showed that ∆ubp3 mitochondria had higher Pi but WT cells with medium Pi supplement showed lower Pi, it is hard to understand why the same Pi increase in the cytosol had a different outcome in mitochondrial Pi. Later on, they showed that the isolated mito exposed to higher Pi showed increased activity, so why can't increased Pi in intact cells increase mito activity? Moreover, they first showed that ∆ubp3 had a Mir1 increase in Fig3A, then showed no changes in FigS4G. It is very confusing.

3. Given that there is no degradation difference for these glycolytic enzymes in ∆ubp3, and the authors found transcriptional level changes, suggests an alternative possibility where ∆ubp3 may signal through unknown mechanisms to parallelly regulate both mitochondrial biogenesis and glycolytic enzyme expression. The increase of trehalose synthesis usually happens in cells under proteostasis stress, so it is important to rule out whether ∆ubp3 signals these metabolic changes via proteostasis dysregulation. This echoes my first point that it is unknown whether wild-type cells use a similar mechanism as ∆ubp3 cells to regulate the glucose repression of mitochondria.

4. Other major concerns:<br /> a. The authors selectively showed a few proteins in their manuscript to support their conclusion. For example, only Cox2 and Tom70 were used to illustrate mitochondrial biogenesis difference in line 97. Later on, they re-analyzed the previous MS dataset from Isasa et al 2015 and showed a few proteins in Fig3A to support their conclusion that ∆ubp3 increases mitochondrial OXPHOS proteins. However, I checked that MS dataset myself and saw that many key OXPHOS proteins do not change, for example, both ATP1 and ATP2 do not change, which encode the alpha and beta subunits of F1 ATPase. They selectively reported the proteins' change in the direction along with their hypothesis.<br /> b. The authors said they deleted ETC component Cox2 in line 111. I checked their method and table S1, I cannot figure out how they selectively deleted COX2 from mtDNA. This must be a mistake.<br /> c. They used sodium azide in a lot of assays to inhibit complex IV. However, this chemical is nonspecific and broadly affects many ATPases as well. Not sure why they do not use more specific inhibitors that are commonly used to assay OCR in seahorse.<br /> d. The authors measured cellular Pi level by grinding the entire cells to release Pi. However, this will lead to a mix of cytosolic and vacuolar Pi. Related to this caveat, the cytosol has ~50mM Pi, while only 1-2mM of these glycolysis metabolites, I am not sure why the reduction of several glycolysis enzymes will cause significant changes in cytosolic Pi levels and make Pi the limiting factor for mitochondrial respiration. One possibility is that the observed cytosolic Pi level changes were caused by the measurement issue mentioned above.<br /> e. The authors used ∆mir1 and MIR1 OE to show that Pi viability in the mitochondrial matrix is important for mitochondrial activity and biogenesis. This is not surprising as Pi is a key substrate required for OXPHOS activity. I doubt the approach of adding a control to determine whether Pi has a specific regulatory function, while other OXPHOS substrates, like ADP, O2 etc do not have the same effect.

Reviewer #2 (Public Review):

In this manuscript, the authors employ a multilevel approach to investigate the relationship between the hippocampal-prefrontal (HPC-PFC) network and long-term phenotypes resulting from early-life seizures (ELS). Their research begins by establishing an ELS rat model and conducting behavioral and neuropathological studies in adulthood. Subsequently, the manuscript delves into testing hypotheses concerning HPC-PFC network dysfunction. While the results are intriguing, my enthusiasm is tempered by concerns related to the logical flow, sample size, and the potential over-interpretation of results. Detailed comments are provided below:

Focus on Correlations: The manuscript primarily highlights correlations as the most significant findings. For instance, it demonstrates that ELS induces cognitive and sensorimotor impairments. However, it falls short of elucidating why these deficits are specifically linked to HPC-PFC synaptic plasticity/network. Furthermore, the manuscript mentions the involvement of other brain regions like the thalamus in the long-term outcomes of ELS based on immunohistochemistry data. This raises questions about the subjective nature and persuasiveness of the statistical studies presented.

Sample Size Concerns: The manuscript raises concerns about the adequacy of sample sizes in the study. The initial cohort for acute electrophysiology during ELS induction comprised only 5 rats, without a control group. Moreover, the behavioral tests involved 11 control and 14 ELS rats, but these same cohorts were used for over four different experiments. Subsequent electrophysiology and immunohistochemistry experiments used varying numbers of rats (7 to 11). Clarification is needed regarding whether these experiments utilized the same cohort and why the sample sizes differed. A power analysis should have been performed to justify sample sizes, especially given the complexity of the statistical analyses conducted.

Overinterpretation of HPC-PFC Network Dysfunction: The manuscript potentially overinterprets the role of HPC-PFC network dysfunction based on the results. Notably, cognitive deficits are described as subtle, with no evidence of learning deficits and only faint working memory impairments. However, sensorimotor deficits show promise. Consequently, it's essential to justify the emphasis on the HPC-PFC network as the primary mechanism underlying ELS-associated outcomes, especially when enhanced LTP is observed. Additionally, the manuscript seems to sideline neuropathological changes in the thalamus and the thalamus-to-PFC connection. The analysis lacks a direct assessment of the causal relationship between HPC-PFC dysfunction and ELS-associated outcomes, leaving a multitude of multilevel analyses yielding potential correlations without easily interpretable results.

Overall, while the manuscript presents intriguing findings related to the HPC-PFC network and ELS outcomes, it requires a more rigorous experimental design, a more coherent narrative linking results to hypotheses, and careful consideration of alternative interpretations based on the observed data. Addressing these concerns will enhance the manuscript's overall quality and impact.

Reviewer #2 (Public Review):

Summary:

The manuscript by Wankowicz et al. describes updates to qFit, an algorithm for the characterization of conformational heterogeneity of protein molecules based on X-ray diffraction of Cryo-EM data. The work provides a clear description of the algorithm used by qFit. The authors then proceed to validate the performance of qFit by comparing it to deposited X-ray entries in the PDB in the 1.2-1.5 Å resolution range as quantified by Rfree, Rwork-Rfree, detailed examination of the conformations introduced by qFit, and performance on stereochemical measures (MolProbity scores). To examine the effect of experimental resolution of X-ray diffraction data, they start from an ultra high-resolution structure (SARS-CoV2 Nsp3 macrodomain) to determine how the loss of resolution (introduced artificially) degrades the ability of qFit to correctly infer the nature and presence of alternate conformations. The authors observe a gradual loss of ability to correctly infer alternate conformations as resolution degrades past 2 Å. The authors repeat this analysis for a larger set of entries in a more automated fashion and again observe that qFit works well for structures with resolutions better than 2 Å, with a rapid loss of accuracy at lower resolution. Finally, the authors examine the performance of qFit on cryo-EM data. Despite a few prominent examples, the authors find only a handful (8) of datasets for which they can confirm a resolution better than 2.0 Å. The performance of qFit on these maps is encouraging and will be of much interest because cryo-EM maps will, presumably, continue to improve and because of the rapid increase in the availability of such data for many supramolecular biological assemblies. As the authors note, practices in cryo-EM analysis are far from uniform, hampering the development and assessment of tools like qFit.

Strengths:

qFit improves the quality of refined structures at resolutions better than 2.0 A, in terms of reflecting true conformational heterogeneity and geometry. The algorithm is well designed and does not introduce spurious or unnecessary conformational heterogeneity. I was able to install and run the program without a problem within a computing cluster environment. The paper is well written and the validation thorough.<br /> I found the section on cryo-EM particularly enlightening, both because it demonstrates the potential for discovery of conformational heterogeneity from such data by qFit, and because it clearly explains the hurdles towards this becoming common practice, including lack of uniformity in reporting resolution, and differences in map and solvent treatment.

Weaknesses:

The authors begin the results section by claiming that they made "substantial improvement" relative to the previous iteration of qFit, "both algorithmically (e.g., scoring is improved by BIC, sampling of B factors is now included) and computationally (improving the efficiency and reliability of the code)" (bottom of page 3). However, the paper does not provide a comparison to previous iterations of the software or quantitation of the effects of these specific improvements, such as whether scoring is improved by the BIC, how the application of BIC has changed since the previous paper, whether sampling of B factors helps, and whether the code faster. It would help the reader to understand what, if any, the significance of each of these improvements was.

The exclusion of structures containing ligands and multichain protein models in the validation of qFit was puzzling since both are very common in the PDB. This may convey the impression that qFit cannot handle such use cases. (Although it seems that qFit has an algorithm dedicated to modeling ligand heterogeneity and seems to be able to handle multiple chains). The paper would be more effective if it explained how a user of the software would handle scenarios with ligands and multiple chains, and why these would be excluded from analysis here.

It would be helpful to add some guidance on how/whether qFit models can be further refined afterwards in Coot, Phenix, ..., or whether these models are strictly intended as the terminal step in refinement.

Appraisal & Discussion:

Overall, the authors convincingly demonstrate that qFit provides a reliable means to detect and model conformational heterogeneity within high-resolution X-ray diffraction datasets and (based on a smaller sample) in cryo-EM density maps. This represents the state of the art in the field and will be of interest to any structural biologist or biochemist seeking to attain an understanding of the structural basis of the function of their system of interest, including potential allosteric mechanisms-an area where there are still few good solutions. That is, I expect qFit to find widespread use.

Reviewer #2 (Public Review):

Neuroscientists often state that we have no theory of the brain. The example of theoretical physics is often cited, where numerous and quite complex phenomena are explained by a compact mathematical description. Lagrangian and Hamiltonian pictures provide such powerful 'single equation'. These frameworks are referred to as 'energy', an elegant way to turn numerous differential equations into a single compact relationship between observable quantities (state variables like position and speed) and scaling constants (like the gravity constant or the Planck constant). Such energy-pictures have been used in theoretical neuroscience since the 1980s.

The manuscript "neuronal least-action principle for real-time learning in cortical circuits" by Walter Senn and collaborators describes a theoretical framework to link predictive coding, error-based learning, and neuronal dynamics. The central concept is that an energy function combining self-supervised and supervised objectives is optimized by realistic neuronal dynamics and learning rules when considering the state of a neuron as a mixture of the current membrane potential and its rate of change. As compared with previous energy functions in theoretical neuroscience, this theory captures a more extensive range of observations while satisfying normative constraints. Particularly, no theory had to my knowledge related to adaptive dynamics widely observed in the brain (referred to as prospective coding in the text, but is sometimes referred to as adaptive coding or redundancy reduction) with the dynamics of learning rules.

The manuscript first exposes the theory of two previously published papers by the same group on somato-dendritic error with apical and basal dendrites. These dynamics are then related to an energy function, whose optimum recovers the dynamics. The rest of the manuscript illustrates how features of this model fit either normative or observational constraints. Learning follows a combination of self-supervised learning (learning to predict the next step) and supervised learning (learning to predict an external signal). The credit assignment problem is solved by an apical-compartment projecting a set of interneurons with learning rules whose role is to align many weight matrices to avoid having to do multiplexing. An extensive method section and supplementary material expand on mathematical proofs and makes more explicit the mathematical relationship between different frameworks.

Experts would say that much of the article agglomerates previous theoretical papers by the same authors that have been published recently either in archival servers or in conference proceedings. A number of adaptations to previous theoretical results were necessary, so the present article is not easily reduced to a compendium of previous pre-prints. However, the manuscript is by no means easy to read as there are several inconsistencies and it lacks a single thread. Also, there remains a few thorny assumptions (unobserved details of the learning rules or soma-dendrites interactions), but the theory is likely going to be regarded as an important step towards a comprehensive theory of the brain.

Reviewer #2 (Public Review):

Summary:<br /> This paper acknowledges that most development occurs in social contexts, with other social partners. The authors put forth two main frameworks of how development occurs within a social interaction with a caregiver. The first is that although social interaction with mature partners is somewhat bi-directional, mature social partners exogenously influence infant behaviors and attention through "attentional scaffolding", and that in this case infant attention is reactive to caregiver behavior. The second framework posits that caregivers support and guide infant attention by contingently responding to reorientations in infant behavior, thus caregiver behaviors are reactive to infant behavior. The aim of this paper is to use moment-to-moment analysis techniques to understand the directionality of dyadic interaction. It is difficult to determine whether the authors prove their point as the results are not clearly explained as is the motivation for the chosen methods.

Strengths<br /> The question driving this study is interesting and a genuine gap in the literature. Almost all development occurs in the presence of a mature social partner. While it is known that these interactions are critical for development, the directionality of how these interactions unfold in real-time is less known.

The analyses largely seem to be appropriate for the question at hand, capturing small moment-to-moment dynamics in both infant and child behavior, and their relationships with themselves and each other. Autocorrelations and cross-correlations are powerful tools that can uncover small but meaningful patterns in data that may not be uncovered with other more discretized analyses (i.e. regression).

Weaknesses<br /> The major weakness of this paper is that the reader is assumed to understand why these results lead to their claimed findings. The authors need to describe more carefully their reasoning and justification for their analyses and what they hope to show. While a handful of experts would understand why autocorrelations and cross-correlations should be used, they are by no means basic analyses. It would also be helpful to use simulated data or even a simple figure to help the reader more easily understand what a significant result looks like versus an insignificant result.

While the overall question is interesting the introduction does not properly set up the rest of the paper. The authors spend a lot of time talking about oscillatory patterns in general but leave very little discussion to the fact they are using EEG to measure these patterns. The justification for using EEG is also not very well developed. Why did the authors single out fronto-temporal channels instead of using whole brain techniques, which are more standard in the field? This is idiosyncratic and not common.

A worrisome weakness is that the figures are not consistently formatted. The y-axes are not consistent within figures making the data difficult to compare and interpret. Labels are also not consistent and very often the text size is way too small making reading the axes difficult. This is a noticeable lack of attention to detail.

No data is provided to reproduce the figures. This does not need to include the original videos but rather the processed and de-identified data used to generate the figures. Providing the data to support reproducibility is increasingly common in the field of developmental science and the authors are greatly encouraged to do so.

Reviewer #2 (Public Review):

Cell cycle control during nitrogen-fixing symbiosis is an important topic, but our understanding of the process is poor and lacks resolution, as the nodule is a complex organ with many cell types that undergo profound changes. The authors aim to define the cell cycle state of individual plant cells in the emerging nodule primordium, as a transcellular infection thread passes through the meristem to reach cells deep in the incipient nodule and releases bacteria to form symbiosomes. The authors used a number of cell cycle reporters, such as different Histone 3 variants and cyclins, to follow cell cycle progress in exquisite detail. They showed that the host cells in the path of an infection thread exhibit a cell fate distinct from their immediate neighbors: after entering the S phase similar to their neighbors, these cells exit the cell cycle and enter a special differentiated state. This is likely an important shift that allows the proper passage of the infection thread. Although definitive proof needs more investigation, they showed that a pioneering transcription factor, NF-YA1, likely represses these endoreduplicated cells from completing the cell cycle.

Reviewer #2 (Public Review):

The authors aim to investigate how voltage-gated calcium channel number, organization, and subunit composition lead to changes in synaptic activity at tonic and phasic motor neuron terminals, or type Is and Ib motor neurons in Drosophila. These neuron subtypes generate widely different physiological outputs, and many investigations have sought to understand the molecular underpinnings responsible for these differences. Additionally, these authors explore not only static differences that exist during the third-instar larval stage of development but also use a pharmacological approach to induce homeostatic plasticity to explore how these neuronal subtypes dynamically change the structural composition and organization of key synaptic proteins contributing to physiological plasticity. The Drosophila neuromuscular junction (NMJ) is glutamatergic, the main excitatory neurotransmitter in the human brain, so these findings not only expand our understanding of the molecular and physiological mechanisms responsible for differences in motor neuron subtype activity but also contribute to our understanding of how the human brain and nervous system functions.

The authors employ state-of-the-art tools and techniques such as single-molecule localization microscopy 3D STORM and create several novel transgenic animals using CRISPR to expand the molecular tools available for exploration of synaptic biology that will be of wide interest to the field. Additionally, the authors use a robust set of experimental approaches from active zone level resolution functional imaging from live preparations to electrophysiology and immunohistochemical analyses to explore and test their hypotheses. All data appear to be robustly acquired and analyzed using appropriate methodology. The authors make important advancements to our understanding of how the different motor neuron subtypes, phasic and tonic-like, exhibit widely varying electrical output despite the neuromuscular junctions having similar ultrastructural composition in the proteins of interest, voltage gated calcium channel cacophony (cac) and the scaffold protein Bruchpilot (brp). The authors reveal the ratio of brp:cac appears to be a critical determinant of release probability (Pr), and in particular, the packing density of VGCCs and availability of brp. Importantly, the authors demonstrate a brp-dependent increase in VGCC density following acute philanthotoxin perfusion (glutamate receptor inhibitor). This VGCC increase appears to be largely responsible for the presynaptic homeostatic plasticity (PHP) observable at the Drosophila NMJ. Lastly, the authors created several novel CRISPR-tagged transgenic lines to visualize the spatial localization of VGCC subunits in Drosophila. Two of these lines, CaBV5-C and stjV5-N, express in motor neurons and in the nervous system, localize at the NMJ, and most strikingly, strongly correlate with Pr at tonic and phasic-like terminals.

The few limitations in this study could be addressed with some commentary, a few minor follow-up analyses, or experiments. The authors use a postsynaptically expressed calcium indicator (mhc-Gal4>UAS -GCaMP) to calculate Pr, yet do not explore the contribution that glutamate receptors, or other postsynaptic contributors (e.g. components of the postsynaptic density, PSD) may contribute. A previous publication exploring tonic vs phasic-like activity at the drosophila NMJ revealed a dynamic role for GluRII (Aponte-Santiago et al, 2020). Could the speed of GluR accumulation account for differences between neuron subtypes?

The observation that calcium channel density and brp:cac ratio as a critical determinant of Pr is an important one. However, it is surprising that this was not observed in previous investigations of cac intensity (of which there are many). Is this purely a technical limitation of other investigations, or are other possibilities feasible? Additionally, regarding VGCC-SV coupling, the authors conclude that this packing density increases their proximity to SVs and contributes to the steeper relationship between VGCCs and Pr at phasic type Is. Is it possible that brp or other AZ components could account for these differences. The authors possess the tools to address this directly by labeling vesicles with JanellaFluor646; a stronger signal should be present at Is boutons. Additionally, many different studies have used transmission electron microscopy to explore SVs location to AZs (t-bars) at the Drosophila NMJ.

In reference to the contradictory observations that VGCC intensity does not always correlate with, or determine Pr. Previous investigations have also observed other AZ proteins or interactors (e.g. synaptotagmin mutants) critically control release, even when the correlation between cac and release remains constant while Pr dramatically precipitates.

To confirm the observations that lower brp levels results in a significantly higher cac:brp ratio at phasic-like synapses by organizing VGCCs; this argument could be made stronger by analyzing their existing data. By selecting a population of AZs in Ib boutons that endogenously express normal cac and lower brp levels, the Pr from these should be higher than those from within that population, but comparable to Is Pr. I believe the authors should also be able to correlate the cac:brp ratio with Pr from their data set generally; to determine if a strong correlation exists beyond their observation for cac correlation.

For the philanthotoxin induced changes in cac and brp localization underlying PHP, why do the authors not show cac accumulation after PhTx on live dissected preparations (i.e. in real time)? This also be an excellent opportunity to validate their brp:cac theory. Do the authors observe a dynamic change in brp:cac after 1, or 5 minutes; do Is boutons potentiate stronger due to proportional increases in cac and brp? Also regarding PhTx-induced PHP, their observations that stj and α2δ-3are more abundant at Is synapses, suggests that they may also play a role in PhTx induced changes in cac. If either/both are overexpressed during PhTx, brp should increase while cac remains constant. These accessory proteins may determine cac incorporation at AZs.<br /> Taken together this study generates important data-driven, conceptional, and theoretical advancements in our understanding of the molecular underpinnings of different motor neurons, and our understanding of synaptic biology generally. The data are robust, thoroughly analyzed, appropriately depicted. This study not only generates novel findings but also generated novel molecular tools which will aid future investigations and investigators progress in this field.

Reviewer #2 (Public Review):

This manuscript by Lu et al addresses the understudied interplay between structural and functional changes underlying homeostatic plasticity. Using hippocampal organotypic slice cultures allowing chronic imaging of dendritic spines, the authors showed that partial or complete inhibition of AMPA-type glutamate receptors differentially affects spine density, respectively leading to an increase or decrease of spines. Based on that dataset, they built a model where activity-dependent synapse formation is regulated by a biphasic rule and tested it in stimulation- or deprivation-induced homeostatic plasticity. The model matches experimental data (from the authors and the literature) quite well, and provides a framework within which functional and structural changes coexist to regulate firing rate homeostasis.

While the correlation between changes in AMPAR numbers and in spine number/size has been well characterized during Hebbian plasticity, the situation is much less clear in homeostatic plasticity due to multiple studies yielding diverging results. This manuscript adds new experimental results to the existing data and presents a valuable effort to generate a model that can explain these divergences in a unifying and satisfactory framework.

The model and its successive implantation steps are well presented along a clear thread. However, it would have benefited from having an actual timeline of structural changes throughout the three days of AMPAR inhibition, especially as their experimental model allows it. This would have provided additional information on spine dynamics (especially transient spines) and on the respective timescale of the structural and functional changes, and thus led to a better-informed model.

Additionally, the model would have been strengthened by an experimental dataset with homeostatic plasticity induced by higher activity (e.g. with bicuculline). To the best of my knowledge, there is currently no data on structural plasticity following scaling down, and it is also known that scaling up and down are mediated by different molecular pathways. The extension of the model from scaling up (in response to silencing) to scaling down (in response to increased activity) offers an interesting perspective but may be a bit of a stretch.

Finally, the authors are very specific in their definition and distinction of structural and functional homeostatic plasticity for their model. Structural plasticity is limited to spine density and functional plasticity to synaptic scaling, which allows the authors to discuss the interplay between very distinct "synapse number-based structural plasticity" and "synaptic weight-based synaptic scaling", and appears to bypass the fact that spine size regulates the space available for AMPARs at the synapse and thus synaptic weight. The authors are of course aware of the importance of changes in spine size, as they present some intriguing data showing that spine size is differentially affected by partial or complete inhibition of AMPARs and include the putative role of spine size changes in the discussion. However, spine size does not seem to be taken into account in their network simulations, which present synaptic scaling and structural plasticity as completely distinct processes. While the model still offers interesting insights into the interaction of these processes, it would have benefited from a less stringent distinction; this choice and the reasons behind it should be made more explicit in the manuscript.

Reviewer #2 (Public Review):

Since neurocysticercosis is associated with epilepsy, the authors wish to establish how cestode larvae affect neurons. The underlying hypothesis is that the larvae may directly excite neurons and thus favor seizure genesis.

To test this hypothesis, the authors collected biological materials from larvae (from either homogenates or excretory/secretory products), and applied them to hippocampal neurons (rats and mice) and human cortical neurons.

This constitutes a major strength of the paper, providing a direct reading of larvae's biological effects. Another strength is the combination of methods, including patch clamp, Ca, and glutamate imaging.

There are some weaknesses:

1) The main one relates to the statement: "Together, these results indicate that T. crassiceps larvae homogenate results not just in a transient depolarization of cells in the immediate vicinity of application, but can also trigger a wave of excitation that propagates through the brain slice in both space and time. This demonstrates that T. crassiceps homogenate can initiate seizure-like activity under suitable conditions."<br /> The only "evidence" of propagation is an image at two time points. It is one experiment, and there is no quantification. Either increase n's and perform a quantification, or remove such a statement.<br /> Likewise, there is no evidence of seizure genesis. A single cell recording is shown. The presence of a seizure-like event should be evaluated with field recordings.

2) Control puff experiments are lacking for Fig 1. Would puffing ACSF also produce a depolarization, and even firing, as suggested in Fig. 2D? This is needed for at least one species.

3) What is the rationale to use a Cs-based solution? Even in the presence of TTX and with blocking K channels, the depolarization may be sufficient to activate Ca channels (LVGs), which would further contribute to the depolarization. Why not perform voltage clamp recordings to directly the current?

4) Why did you use organotypic slices? Since you wish to model adult epilepsy, it would have been more relevant to use fresh slices from adult rats/mice. At least, discuss the caveat of using a network still in development in vitro.

5) Please include both the number of slices and number of cells recorded in each condition. This is the standard (the number of cells is not enough).

6) Please provide a table with the basic properties of cells (Rin, Rs, etc.). This is standard to assess the quality of the recordings.

7) Please provide a table on patient's profile. This is standard when using human material. Were these TLE cases (and "control" cortex) or epileptogenic cortex?

Globally, the authors achieved their aims. They show convincingly that larvae material can depolarize neurons, with glutamate (and aspartate) as the most likely candidates.<br /> This is important not only because it provides mechanistic insight but also potential therapeutic targets. The result is impactful, as the authors use quasi-naturalistic conditions, to assess what might happen in the human brain. The experimental design is appropriate to address the question. It can be replicated by any interested person.

Reviewer #2 (Public Review):

In this valuable manuscript Li & Jin record from the substantial nigra and dorsal striatum to identify subpopulations of neurons with activity that reflects different dynamics during action selection, and then use optogenetics in transgenic mice to selectively inhibit or excite D1- and D2- expressing spiny projection neurons in the striatum, demonstrating a causal role for each in action selection in an opposing manner. They argue that their findings cannot be explained by current models and propose a new 'triple control' model instead, with one direct and two indirect pathways. These findings will be of broad interest to neuroscientists, but lacks some direct evidence for the proposal of the new model.

Overall there are many strengths to this manuscript including the fact that the empirical data in this manuscript is thorough and the experiments are well-designed.

Reviewer #2 (Public Review):

The manuscript by Bohl et al. is an interesting and carefully done study on the biochemical properties and mode of action of potent autonomous AAA+ disaggregase ClpL from Listeria monocytogenes. ClpL is encoded on plasmids. It shows high thermal stability and provides Listeria monocytogenes food-pathogen substantial increase in resistance to heat. The authors show that ClpL interacts with aggregated proteins through the aromatic residues present in its N-terminal domain and subsequently unfolds proteins from aggregates translocating polypeptide chains through the central pore in its oligomeric ring structure. The structure of ClpL oligomers was also investigated in the manuscript. The results suggest that mono-ring structure and not dimer or trimer of rings, observed in addition to mono-ring structures under EM, is an active species of disaggregase.

Presented experiments are conclusive and well-controlled. Several mutants were created to analyze the importance of a particular ClpL domain.

The study's strength lies in the direct comparison of ClpL biochemical properties with autonomous ClpG disaggregase present in selected Gram-negative bacteria and well-studied E. coli system consisting of ClpB disaggregase and DnaK and its cochaperones. This puts the obtained results in a broader context.

Reviewer #2 (Public Review):

Summary:

This manuscript describes P. falciparum population structure in Zanzibar and mainland Tanzania. 282 samples were typed using molecular inversion probes. The manuscript is overall well-written and shows a clear population structure. It follows a similar manuscript published earlier this year, which typed a similar number of samples collected mostly in the same sites around the same time. The current manuscript extends this work by including a large number of samples from coastal Tanzania, and by including clinical samples, allowing for a comparison with asymptomatic samples.

The two studies made overall very similar findings, including strong small-scale population structure, related infections on Zanzibar and the mainland, near-clonal expansion on Pemba, and frequency of markers of drug resistance. Despite these similarities, the previous study is mentioned a single time in the discussion (in contrast, the previous research from the authors of the current study is more thoroughly discussed). The authors missed an opportunity here to highlight the similar findings of the two studies.

Strengths:

The overall results show a clear pattern of population structure. The finding of highly related infections detected in close proximity shows local transmission and can possibly be leveraged for targeted control.

Weaknesses:

A number of points need clarification:

It is overall quite challenging to keep track of the number of samples analyzed. I believe the number of samples used to study population structure was 282 (line 141), thus this number should be included in the abstract rather than 391. It is unclear where the number 232 on line 205 comes from, I failed to deduct this number from supplementary table 1.

Also, Table 1 and Supplementary Table 1 should be swapped. It is more important for the reader to know the number of samples included in the analysis (as given in Supplementary Table 1) than the number collected. Possibly, the two tables could be combined in a clever way.

Methods<br /> The authors took the somewhat unusual decision to apply K-means clustering to GPS coordinates to determine how to combine their data into a cluster. There is an obvious cluster on Pemba islands and three clusters on Unguja. Based on the map, I assume that one of these three clusters is mostly urban, while the other two are more rural. It would be helpful to have a bit more information about that in the methods. See also comments on maps in Figures 1 and 2 below.

Following this point, in Supplemental Figure 5 I fail to see an inflection point at K=4. If there is one, it will be so weak that it is hardly informative. I think selecting 4 clusters in Zanzibar is fine, but the justification based on this figure is unclear.

For the drug resistance loci, it is stated that "we further removed SNPs with less than 0.005 population frequency." Was the denominator for this analysis the entire population, or were Zanzibar and mainland samples assessed separately? If the latter, as for all markers <200 samples were typed per site, there could not be a meaningful way of applying this threshold. Given data were available for 200-300 samples for each marker, does this simply mean that each SNP needed to be present twice?

Discussion:<br /> I was a bit surprised to read the following statement, given Zanzibar is one of the few places that has an effective reactive case detection program in place: "Thus, directly targeting local malaria transmission, including the asymptomatic reservoir which contributes to sustained transmission (Barry et al., 2021; Sumner et al., 2021), may be an important focus for ultimately achieving malaria control in the archipelago (Björkman & Morris, 2020)." I think the current RACD program should be mentioned and referenced. A number of studies have investigated this program.

The discussion states that "In Zanzibar, we see this both within and between shehias, suggesting that parasite gene flow occurs over both short and long distances." I think the term 'long distances' should be better defined. Figure 4 shows that highly related infections rarely span beyond 20-30 km. In many epidemiological studies, this would still be considered short distances.

Lines 330-331: "Polymorphisms associated with artemisinin resistance did not appear in this population." Do you refer to background mutations here? Otherwise, the sentence seems to repeat lines 324. Please clarify.

Line 344: The opinion paper by Bousema et al. in 2012 was followed by a field trial in Kenya (Bousema et al, 2016) that found that targeting hotspots did NOT have an impact beyond the actual hotspot. This (and other) more recent finding needs to be considered when arguing for hotspot-targeted interventions in Zanzibar.

Figures and Tables:<br /> Table 2: Why not enter '0' if a mutation was not detected? 'ND' is somewhat confusing, as the prevalence is indeed 0%.

Figure 1: Panel A is very hard to read. I don't think there is a meaningful way to display a 3D-panel in 2D. Two panels showing PC1 vs. PC2 and PC1 vs. PC3 would be better. I also believe the legend 'PC2' is placed in the wrong position (along the Y-axis of panel 2).

Supplementary Figure 2B suffers from the same issue.

The maps for Figures 1 and 2 don't correspond. Assuming Kati represents cluster 4 in Figure 2, the name is put in the wrong position. If the grouping of shehias is different between the Figures, please add an explanation of why this is.

Figure 2: In the main panel, please clarify what the lines indicate (median and quartiles?). It is very difficult to see anything except the outliers. I wonder whether another way of displaying these data would be clearer. Maybe a table with medians and confidence intervals would be better (or that data could be added to the plots). The current plots might be misleading as they are dominated by outliers.

In the insert, the cluster number should not only be given as a color code but also added to the map. The current version will be impossible to read for people with color vision impairment, and it is confusing for any reader as the numbers don't appear to follow any logic (e.g. north to south).

The legend for Figure 3 is difficult to follow. I do not understand what the difference in binning was in panels A and B compared to C.

Font sizes for panel C differ, and it is not aligned with the other panels.

Why is Kusini included in Supplemental Figure 4, but not in Figure 1?

Supplemental Figures 6 and 7: What does the width of the line indicate?

What was the motivation not to put these lines on the map, as in Figure 4A? This might make it easier to interpret the data.

Reviewer #2 (Public Review):

Bian et al studied creatine (Cr) in the context of central nervous system (CNS) function. They detected Cr in synaptic vesicles purified from mouse brains with anti-Synaptophysin using capillary electrophoresis-mass spectrometry. Cr levels in the synaptic vesicle fraction was reduced in mice lacking the Cr synthetase AGAT, or the Cr transporter SLC6A8. They provide evidence for Cr release within several minutes after treating brain slices with KCl. This KCl-induced Cr release was partially calcium dependent and was attenuated in slices obtained from AGAT and SLC6A8 mutant mice. Cr application also decreased the excitability of cortical pyramidal cells in one third of the cells tested. Finally, they provide evidence for SLC6A8-dependent Cr uptake into synaptosomes, and ATP-dependent Cr loading into synaptic vesicles. Based on these data, the authors propose that Cr may act as neurotransmitter in the CNS.

Strengths:

1. A major strength of the paper is the broad spectrum of tools used to investigate Cr.<br /> 2. The study provides evidence that Cr is present in/loaded into synaptic vesicles.

Weaknesses (resubmission):

1. There is no significant decrease in Cr content pulled down by anti-Syp in AGAT-/- mice when normalized to IgG controls. Hence, blocking AGAT activity/Cr synthesis does not affect Cr levels in the synaptic vesicle fraction, arguing against a Cr enrichment.<br /> 2. There is no difference in KCl-induced Cr release between SLC6A8-/Y and SLC6A8+/Y when normalizing the data to the respective controls. Thus, the data are not consistent with the idea that depolarization-induced Cr release requires SLC6A8.<br /> 3. The rationale of grouping the excitability data into responders and non-responders is not convincing because the threshold of 10% decrease in AP rate is arbitrary. The data do therefore not support the conclusion that Cr reduces neuronal excitability.

Reviewer #2 (Public Review):

This study investigates how genes in the Gr28 family of gustatory receptors function in the taste system of Drosophila larvae. Gr28 genes are intriguing because they have been implicated in taste as well as other functions, such as sensing temperature and ultraviolet light. This study makes several new findings. First, the authors show that four Gr28 genes are expressed in putative taste neurons, and these neurons can be largely divided into subsets that express Gr28a versus Gr28bc. The authors then demonstrate that these two neuronal subsets drive opposing behaviors (attraction versus avoidance) when activated. The avoidance-promoting neurons respond to bitter compounds and are required for bitter avoidance, and Gr28bc and Gr28ba were specifically implicated in bitter detection in these cells. Together, these findings provide insight into the complexity of taste receptor expression and function in Drosophila, even within a single receptor subfamily.

The conclusions are well-supported by the experimental data. Strengths of the paper include the use of precise genetic tools, thorough analyses of expression patterns, carefully validated behavioral assays, and well-controlled functional imaging experiments. The role of Gr28bc neurons is more thoroughly explored than that of Gr28a neurons. However, a previous study from the same lab (Mishra et al., 2018) showed that Gr28a neurons detect RNA and ribose, which are attractive to larvae. Presumably this is the attractive response that is being recapitulated upon artificial activation of Gr28a neurons.

Reviewer #2 (Public Review):

Milovic, Duong, and Barbour investigate the inflammatory response of three species of small mammals (P. leucopus, M. musculus, and R. norvegicus) to endotoxin lipopolysaccharide (LPS) injection via genome-wide transcriptomics from blood samples. Understanding the inflammation response of P. leucopus is of importance as they are a reservoir for several pathogens. The study is a thorough, controlled, well researched analysis that will be valuable for designing and interpreting future studies. The authors discuss the limitations of the data and the potential directions. Clearly P. leucopus respond differently to the LPS exposure which is very interesting and opens the door for numerous other comparative studies.

The conclusions of the manuscript are thoughtful and supported by the data. The authors addressed my questions about mouse numbers, sex differences, and the presentation of Nos2 and Arg1 data.

Reviewer #2 (Public Review):

In this manuscript, Xiaoxuan Lin and colleagues provide new insights into the dynamics of prestin using H/D exchange coupled with mass spectrometry. The authors aim to reveal how local changes in folding upon anion binding sustain the unique electro-transduction capabilities of prestin.

Prestin is an unusual member of the SLC26 family, that changes its cross-sectional area in the membrane upon binding of a chloride ion. In contrast to SLC26 homologs, prestin is not an anion transporter per se but requires an anion to sense voltage. Binding of Cl- at a conserved binding site located between the end of TM3 and TM10 drives the displacement of a conserved arginine (R399), that causes major conformational changes, transmitting the voltage sensing into a mechanical force exerted on the membrane.

Cryo-EM structures are available for the protein bound to various anions, including Cl-, but these structures do not explain how a conserved couple of positive (R399) and negative (the Cl- anion) charge pair transforms voltage sensitivity into mechanical changes in the membrane. To address this challenge, the authors explore local dynamics of the anion binding site and compare it with that of a "real" anion transporter SLC26A9. The authors make a convincing case that the differences in local dynamics they measure are the molecular basis for voltage sensing and its translation into electromotility.

Practically the authors make a thorough HDX-MS investigation of prestin in the presence of different anions Cl-, SO4-, salicylate as well as in the apo form, and provide insight mostly on local dynamics of the anion binding site. The experiments are well-designed and conducted and their quality and reproducibility allows for quantitative interpretation by deriving ΔΔG values of changes in dynamics at specific sites. Furthermore, the authors show by comparing the apo condition with Cl- bound condition that the absence of Cl- causes fraying of the TM3 and TM10 helices. They deduce that Cl- binding allows for directional helix structuration, leading to local structural changes that cause a rearrangement of the charge configuration at the anion binding site that lays the molecular basis for voltage sensitivity. They demonstrate based on a detailed analysis of their HDX data that such helix fraying is a specific feature of the binding site and differs from the cooperative unfolding happening elsewhere on the prestin.

However, the main question that the authors are addressing is how voltage sensitivity translates at the molecular level in the requirement for a negative-positive charge pair. The interpretation that the binding site instability observed only for prestin is a feature required for this voltage dependent is a bit speculative. Could other lines of evidence support the claim that the charge ion gap is reduced upon Cl- binding and that this leads to cross-section area expansion? An obvious option that comes to mind is MD simulations There are differences in time-scale between HDX and simulations, but the propensity for H-bond destabilization can be quantified even at short timescales. It might be that such data is already available out there but it should be explicit in the discussion. The discussion section itself is a bit narrow in scope at the moment. Discussing the data in the context of the available structures would help the non-specialist reader.

Reviewer #2 (Public Review):

Summary:<br /> In the manuscript "Surprising Features of Nuclear Receptor Interaction Networks Revealed by Live Cell Single Molecule Imaging", Dahal et al combine fast single molecule tracking (SMT) with proximity-assisted photoactivation (PAPA) to study the interaction between RARa and RXRa. The prevalent model in the nuclear receptor field suggests that type II nuclear receptors compete for a limiting pool of their partner RXRa. Contrary to this, the authors find that over-expression of RARa but not RXRa increases the fraction of RXRa molecules bound to chromatin, which leads them to conclude that the limiting factor is the abundance of RARa and not RXRa. The authors also perform experiments with a known RARa agonist, all trans retinoic acid (atRA) which has little effect on the bound fraction. Using PAPA, they show that chromatin binding increases upon dimerization of RARa and RXRa.

Strengths:<br /> In my view, the biggest strength of this study is the use of endogenously tagged RARa and RXRa cell lines. As the authors point out, most previous studies used either in vitro assays or over-expression. I commend the authors on the generation of single-cell clones of knock-in RARa-Halo and Halo-RXRa. The authors then carefully measure the abundance of each protein using FACS, which is very helpful when comparing across conditions. The manuscript is generally well written and figures are easy to follow. The consistent color-scheme used throughout the manuscript is very helpful.

Weaknesses:<br /> 1. Agonist treatment:<br /> The authors test the effect of all trans retinoic acid (atRA) on the bound fraction of RARa and RXRa and find that "These results are consistent with the classic model in which dimerization and chromatin binding of T2NRs are ligand independent." However, all the agonist treatments are done in media containing FBS. FBS is not chemically defined and has been found to have between 10 and 50 nM atRA (see references in PMID 32359651 for example). The addition of 1 nM or 100 nM atRA is unlikely to result in a strong effect since the medium already contains comparable or higher levels of agonist. To test their hypothesis of ligand-independent dimerization, the authors should deplete the media of atRA by growing the cells in a medium containing charcoal-stripped FBS for at least 24 hours before adding agonist.

2. Photobleaching and its effect on bound fraction measurements:<br /> The authors discard the first 500 to 1000 frames due to the high localization density in the initial frames. This will preferentially discard bound molecules that will bleach in the initial frames of the movie and lead to an over-estimation of the unbound fraction.

For experiments with over-expression of RAR-Halo and Halo-RXR, the authors state that the cells were pre-bleached and that these frames were used to calculate the mean intensity of the nuclei. When pre-bleaching, bound molecules will preferentially bleach before the diffusing population. This will again lead to an over-representation of the unbound fraction since this is the population that will remain relatively unaffected by the pre-bleaching. Indeed, the bound fraction for over-expressed RARa and RXRa is significantly lower than that for the corresponding knock in lines. To confirm whether this is a biological result, I suggest that the authors either reduce the amount of dye they use so that this pre-bleaching is not necessary or use the direct reactivation strategy they use for their PAPA experiments to eliminate the pre-bleaching step.

As for the measurement of the nuclear intensity, since the authors have access to multiple HaloTag dyes, they can saturate the HaloTagged proteins with a high concentration of JF646 or JFX650 to measure the mean intensity of the protein while still using the PA-JFX549 for SMT. Together, these will eliminate the need to pre-bleach or discard any frames.

3. Heterogeneous expression of the SNAP fusion proteins:<br /> The cell lines expressing SNAP tagged transgenes shown in Fig S6 have very heterogeneous expression of the SNAP proteins. While the bulk measurements done by Western blotting are useful, while doing single-cell experiments (especially with small numbers - ~20 - of cells), it is important to control for expression levels. Since these transgenic stable lines were not FACS sorted, it would be helpful for the reader to know the spread in the distribution of mean intensities of the SNAP proteins for the cells that the SMT data are presented for. This step is crucial while claiming the absence of an effect upon over-expression and can easily be done with a SNAPTag ligand such as SF650 using the procedure outlined for the over-expressed HaloTag proteins.

4. Definition of bound molecules:<br /> The authors state that molecules with a diffusion coefficient less than 0.15 um2/s are considered bound and those between 1-15 um2/s are considered unbound. Clarification is needed on how this threshold was determined. In previous publications using saSPT, the authors have used a cutoff of 0.1 um2/s (for example, PMID 36066004, 36322456). Do the results rely on a specific cutoff? A diffusion coefficient by itself is only a useful measure of normal diffusion. Bound molecules are unlikely to be undergoing Brownian motion, but the state array method implemented here does not seem to account for non-normal diffusive modes. How valid is this assumption here?

5. Movies:<br /> Since this is an imaging manuscript, I request the authors to provide representative movies for all the presented conditions. This is an essential component for a reader to evaluate the data and for them to benchmark their own images if they are to try to reproduce these findings.

6. Definition of an ROI:<br /> The authors state that "ROI of random size but with maximum possible area was selected to fit into the interior of the nuclei" while imaging. However, the readout speed of the Andor iXon Ultra 897 depends on the size of the defined ROI. If the ROI was variable for every movie, how do the authors ensure the same sampling rate?

Reviewer #2 (Public Review):

Summary:<br /> In this manuscript, Chen et al. investigate the localization of microtubule kinesin-13 MCAK to the microtubule ends. MCAK is a prominent microtubule depolymerase whose molecular mechanisms of action have been extensively studied by a number of labs over the last ~twenty years. Here, the authors use single-molecule approaches to investigate the precise localization of MCAK on growing microtubules and conclude that MCAK preferentially binds to a GDP-Pi-tubulin portion of the microtubule end. The conclusions are speculative and not well substantiated by the data, making the impact of the study in its current form rather limited. Specifically, greater effort should be made to define the region of MCAK binding on microtubule ends, as well as its structural characteristics. Given that MCAK has been previously shown to effectively tip-track growing microtubule ends through an established interaction with EB proteins, the physiological relevance of the present study is unclear. Finally, the manuscript does not cite or properly discuss a number of relevant literature references, the results of which should be directly compared and contrasted to those presented here.

Reviewer #2 (Public Review):

Summary:<br /> P2X receptors play pivotal roles in physiological processes such as neurotransmission and inflammation, making them promising drug targets. This study, through cryo-EM and functional experiments, reveals the structural basis of the competitive inhibition of the PPNDS and PPADS on mammalian P2X7 receptors. Key findings include the identification of the orthosteric site for these antagonists, the revelation of how PPADS/PPNDS binding impedes channel-activating conformational changes, and the pinpointing of specific residues in P2X1 and P2X3 subtypes that determine their heightened sensitivity to these antagonists. These insights present a comprehensive understanding that could guide the development of improved drugs targeting P2X receptors. This work will be a valuable addition to the field.

Strengths and weaknesses:<br /> The combination of structural experiments and mutagenesis analyses offers a deeper understanding of the mechanism. While the inclusion of MD simulation is appreciated, providing more insights from the simulation might further strengthen this already compelling story.

Reviewer #2 (Public Review):

Summary:<br /> Most of this paper concerns scRNA-seq data generated from glioblastoma patients, from three regions: tumor center, tumor periphery, and peripheral blood mononuclear cells. They focus on immune cells, and especially microglia and T-cells, where they look at the presence/absence/changes in different types of immune signatures. The data and analysis are sound and supportive of the conclusions they draw, though future studies with more patients and/or low-throughput validation would strengthen their evidence. This study adds to our knowledge of the immune cell environment in glioblastoma patients and its regional variation.

Strengths:<br /> A key strength of the paper lies in the novelty of the data, which simultaneously examines, at single-cell resolution, gene expression in two different tumor regions (center and periphery) along with peripheral blood. The authors provide numerous detailed and state-of-the-art analyses of this data, including gene differential expression, differential abundance of cell types, gene ontology analyses, tSNE visualizations, etc.

They focus in particular on differences in immune cell types. There are some suggestive differences in immune cell composition of center versus periphery, although the number of patients (5, one of whom is missing center data) does not allow one to draw a definitive conclusion.

They identified more definitive gene expression differences in center versus peripheral microglia -- differences that were not reflected in other cell types, and which included downregulation of a number of immune response functions. They also identified gene expression differences between two subsets of microglia, although those may partly reflect regional differences (the subsets are differentially enriched in the center versus periphery) or differential representation of different patients.

Finally, they identify differences in CD8+ T cells and NK cells in the center versus the periphery, where the latter were less activated/proliferative/cytotoxic.

Data analysis is performed to a high standard, using best-available methods and in some cases backed up with alternative approaches showing similar results.

Weaknesses:<br /> While the nature of the dataset is novel, the relatively low patient numbers (five) and patient diversity (e.g. with regard to IHD1 status) may be obscuring differences in cell type abundances or cell state between regions.

Most discoveries based on the scRNA-seq discussed in the paper remain to be validated by low-throughput methods in either the same patient samples, if material remains, or in other patients.

Reviewer #2 (Public Review):

Summary:<br /> Chirality of cells, organs, and organisms can stem from the chiral asymmetry of proteins and polymers at a much smaller lengthscale. The intrinsic chirality of actin filaments (F-actin) is implicated in the chiral arrangement and movement of cellular structures including F-actin-based bundles and the nucleus. It is unknown how opposite chiralities can be observed when the chirality of F-actin is invariant. Kwong, Chen, and co-authors explored this problem by studying chiral cell-scale structures in adherent mammalian cultured cells. They controlled the size of adhesive patches, and examined chirality at different timepoints. They made various molecular perturbations and used several quantitative assays. They showed that forces exerted by antiparallel actomyosin bundles on parallel radial bundles are responsible for the chirality of the actomyosin network at the cell scale.

Strengths:<br /> Whereas previously, most effort has been put into understanding radial bundles, this study makes an important distinction that transverse or circumferential bundles are made of antiparallel actomyosin arrays. A minor point that was nice for the paper to make is that between the co-existing chirality of nuclear rotation and radial bundle tilt, it is the F-actin driving nuclear rotation and not the other way around. The paper is clearly written.

Weaknesses:<br /> The paper could benefit from grammatical editing.

Reviewer #2 (Public Review):

Summary: This study utilized a large sample from the UK Biobank which enhanced statistical robustness, employed a prospective design to establish clear temporal relationships, used objective biomarkers for assessing plasma omega-6/omega-3 ratio, and investigated various mortality causes including CVD and cancer for a holistic health understanding.

Strengths: The authors used a large sample size, employed a prospective design, and investigated various mortality.

Weaknesses: Analyzing n-3 and n-6 PUFAs separately might be less instructive. It might not be methodologically sound to treat TG, HDL, LDL, and apolipoproteins as mediators. It's imperative to exercise caution when drawing causal conclusions from the observed correlations. The manuscript might propose potential research trajectories.

Reviewer #2 (Public Review):

Summary:

In this article, the authors discuss an optimal resource allocation strategy to best allocate funding in maximising malaria eradication efforts. Though achieving elimination by only using insecticide-treated bed nets (ITNs) is not the best practice, and countries utilise different interventions simultaneously, this analysis could be relevant in allocating funding for the global malaria elimination effort. To analyse and compare the impact of ITNs on P. falciparum and P. vivax cases and the total populations at risk, the authors use two previously published models (for P. falciparum and P. vivax).

Strengths:

The authors use models for both P. falciparum and P. vivax to analyse the impact of different strategies for allocating ITNs and provide the best strategies for funding to minimise malaria burden across different transmission settings. Using previously published models that account for various malaria aspects, including demography, heterogeneity in bite exposure, immunity, variation in hypnozoite across bites (P. vivax), mosquito larval dynamics, etc., gives a solid foundation for the analysis performed here.

Weaknesses:

Though the objective of the study is to identify the best setting to allocate funding to eradicate malaria, the authors use prevalence estimates (P. falciparum and P. vivax) based on the year 2000 as the baseline. Given their reasoning behind this choice, the analysis would be more relevant or useful if the proposed strategy were compared to the current Global Technical Strategy for Malaria (GTS 2016-2030). That is, using estimates based on around the year 2016.

In settings where both P. falciparum and P. vivax are co-endemic, using models that do not account for the interplay between the species, especially regarding immunity, somewhat underplays the overall disease dynamics. Furthermore, assuming the transmission within each setting (very low, low, moderate, high) is homogenous is also a weakness as there is heterogeneity in transmission intensity, bite exposure, etc, within each setting.

Reviewer #2 (Public Review):

Summary: This paper, titled "Regulation of Chromatin Accessibility and Transcriptional Repression by PfMORC Protein in Plasmodium falciparum," delves into the PfMORC protein's role during the intra-erythrocytic cycle of the malaria parasite, P. falciparum. Le Roch et al. examined PfMORC's interactions with proteins, its genomic distribution in different parasite life stages (rings, trophozoites, schizonts), and the transcriptome's response to PfMORC depletion. They conducted a chromatin conformation capture on PfMORC-depleted parasites and observed significant alterations. Furthermore, they demonstrated that PfMORC depletion is lethal to the parasite.

Strengths: This study significantly advances our understanding of PfMORC's role in establishing heterochromatin. The direct consequences of the PfMORC depletion are addressed using chromatin conformation capture.

Weaknesses: The study only partially addressed the direct effects of PfMORC depletion on other heterochromatin markers.

Reviewer #2 (Public Review):

Anderson et al profiled chromatin features, including active chromatin marks, RNA polymerase II distribution, and histone modifications in the sex chromosomes of spermatogenic cells in Drosophila. The experiments and analyses were well done, by a combination of the latest and appropriate methods. They include appropriate numbers of replicates. Results were parsed by comparing them among wildtype and two mutant with different arrest stages in spermatogenesis, as well as in FACS-sorted spermatocytes. The authors profiled larval wing discs as reference-somatic cells, allowing focus on features associated with germ cells; comparisons to testis somatic cells provided further specificity. Results were further refined by categorizing genes of interest based on available single nucleus RNA seq expression profiles. The authors acknowledge that the paper's interpretations are based on subtractive logic using the mutants, but comment that more precise ways of staging would not have yielded sufficient sample for their methods.

The authors documented differences in the distribution of RNAPIIS2p on some genes in germ cells vs somatic cells, the presence of a uH2A body beginning in early spermatocytes, and high levels of uH2A on the Y chromosome with little or none on the X, which is intriguing because uH2A is usually associated with silencing, yet the Y chromosome is active in spermatogenic cells. All of these are new, interesting, and important. Also importantly, the authors' data provide molecular details consistent with lack of MSCI, and lack of dosage compensation of the X chromosome in Drosophila spermatocytes.

Reviewer #2 (Public Review):

The manuscript from Wappner and Melani labs claims a novel for the exocyst subunits in multiple aspects of secretory granule exocytosis. This an intriguing paper that suggests multiple roles of the exocyst in granule maturation and fusion with roles at the ER/Golgi interface, TGN, and granule homotypic fusion.

A key strength is the breadth of the assays and study of all 8 exocyst subunits in a powerful model system (fly larvae). Many of the assays are quantitated and roles of the exocyst in early phases of granule biogenesis have not been ascribed.

However there are several weaknesses, both in terms of experimental controls, concrete statements about the granules (better resolution), and making a clear conceptual framework.

Namely, why do KD of different exocysts have different effects on presumed granule formation? Why does just overexpression of a single subunit (Sec15) induce granule fusion? While the paper is fascinating, the major comments need to be addressed to really be able to make better sense of this work, which at present is hard to disentangle direct vs. secondary effects, especially as much of the TGN seems to be altered in the KDs. The authors conveniently ascribe many of the results to the holocomplex, but their own data (Fig. 4 and Fig. 6) are at odds with this.

Major Comments:

1. Resolution not sufficient. Identification of "mature secretory granules" (MSG) in Fig. 3 is based on low-resolution images in which the MSG are not clearly seen (see control in Fig. 3A) and rather appear as a diffuse haze, and not as clear granules. There may be granules here, but as shown it is not clear. Thus it would be helpful to acquire images at higher resolution (at the diffraction limit, or higher) to see and count the MSG. (Note: the authors are not clear on which objective was used. The 20x/0.8 NA or 63x/1.4 NA? Maybe the air objective as the resolution appears poor). They need to prove that the diffuse Sgs3-GFP haze is indeed due to MSG. Related it is unclear what are the granule structures that correspond to Immature secretory granules (ISG) and cells with mesh-like structures (MLS)? Similarly, Sgs3 images of KD of 8 exocyst subunits were interpreted to be identical, in Fig. 4, but the resolution is poor.

2. Explanation of variability of exocyst KD on the appearance of MSG. What is remarkable is a highly variable effect of different subunit KD on the percentage of cells with MLS (Fig. 4C). Controls = 100 %, Exo70=~75% (at 19 deg), Sec3 = ~30%, Sec10 = 0%, Exo84 = 100% ... This is interesting for the functional exocyst is an octameric holocomples, thus why the huge subunit variability in the phenotypes? The trivial explanation is either: i) variable exocyst subunit KD (not shown) or ii) variability between experiments (no error bars are shown). Both should be addressed by quantification of the KD of different proteins and secondly by replicating the experiments. If their data holds up then the underlying mechanism here needs to be considered. (Note: there is some precedent from the autophagy field of differential exocyst effects).

3. In the salivary glands the authors state that the exocyst is needed for Sgs3-GFP exit from the ER. First, Pearson's coefficient should be shown so as to quantitate the degree of ER localizations of all KDs. Second, there should be some rescue performed (if possible) to support specificity. Third, importantly other proteins that should traffic to the PM need to be shown to traffic normally so as to rule out a non-specific effect.

4. Golgi: It is unclear from their model (Fig. 5) why after exocyst KD of Sec15 the cis-Golgi is more preserved than the TGN, which appears as large vacuoles. This is not quantitated and not shown for the 8 subunits.

5. Acute/Chronic control: It would be nice to acutely block the exocyst so as to better distinguish if the effects observed are primary or secondary effects (e.g. on a recycling pathway).

6. Higher Resolution imaging (EM or super-resolution) - this would be nice to better understand the morphological interpretations.

7. Granule homotypic fusion. Strangely over-expression of just one subunit, Sec15-GFP, made giant secretory granules (SG) that were over 8 microns big! Why is that, especially if normally the exocyst is normally a holocomplex. Was this an effect that was specific to Sec15 or all exocyst subunits? Is the Sec15 level rate limiting in these cells? It may be that a subcomplex of Sec15/10 plays earlier roles, but in any case this needs to be addressed across all (or many) of the exocyst subcomplex members.

In summary, there are clearly striking effects on secretory granule biogenesis by dysfunction of the exocyst, however right now it is hard to disentangle effects on ERGolgi traffic, loss of the TGN, and a problem in maturation or fusion of granules. It is also confusing if the entire exocyst holocomplex or subcomplex plays a key role.

Reviewer #2 (Public Review):

Summary:

The malaria parasite Plasmodium develops into oocysts and sporozoites inside Anopheles mosquitoes, in a process called sporogony. Sporozoites invade the insect salivary glands in order to be transmitted during a blood meal. An important question regarding malaria transmission is whether all mosquitoes harboring Plasmodium parasites are equally infectious. In this paper, the authors investigated the progression of P. falciparum sporozoite development in Anopheles mosquitoes, using a sensitive qPCR method to quantify sporozoites and an artificial skin system to probe for parasite expelling. They assessed the association between oocyst burden, salivary gland infection intensity, and sporozoites expelled.

The data show that higher sporozoite loads are associated with earlier colonization of salivary glands and a higher prevalence of sporozoite-positive salivary glands and that higher salivary gland sporozoite burdens are associated with higher numbers of expelled sporozoites. Intriguingly, there is no clear association between salivary gland burdens and the prevalence of expelling, suggesting that most infections reach a sufficient threshold to allow parasite expelling during a mosquito bite. This important observation suggests that low-density gametocyte carriers, although less likely to infect mosquitoes, could nevertheless contribute to malaria transmission.

Strengths:

The paper is well written and the work is well conducted. The authors used two experimental models, one using cultured P. falciparum gametocytes and An. stephensi mosquitoes, and the other one using natural gametocyte infections in a field setup with An. coluzzii mosquitoes. Both studies gave similar results, reinforcing the validity of the observations. Parasite quantification relies on a robust and sensitive qPCR method, and parasite expelling was assessed using an innovative experimental setup based on artificial skin.

Weaknesses:

There is no clear association between the prevalence of sporozoite expelling and the parasite burden. However, high total sporozoite burdens are associated with earlier and more efficient colonization of the salivary glands, and higher salivary gland burdens are associated with higher numbers of expelled sporozoites. While these observations suggest that highly infected mosquitoes could transmit/expel parasites earlier, this is not directly addressed in the study. In addition, whether all expelled sporozoites are equally infectious is unknown. The central question, i.e. whether all infected mosquitoes are equally infectious, therefore remains open.

Reviewer #2 (Public Review):

Summary:

The authors aimed to improve the detection of enkephalins, opioid peptides involved in pain modulation, reward, and stress. They used optogenetics, microdialysis, and mass spectrometry to measure enkephalin release during acute stress in freely moving rodents. Their study provided better detection of enkephalins due to the implementation of previously reported derivatization reaction combined with improved sample collection and offered insights into the dynamics and relationship between Met- and Leu-Enkephalin in the Nucleus Accumbens shell during stress.

Strengths:

A strength of this work is the enhanced opioid peptide detection resulting from an improved microdialysis technique coupled with an established derivatization approach and sensitive and quantitative nLC-MS measurements. These improvements allowed basal and stimulated peptide release with higher temporal resolution, lower detection thresholds, and native-state endogenous peptide measurement.

Weaknesses:

The draft incorrectly credits itself for the development of an oxidation method for the stabilization of Met- and Leu-Enk peptides. The use of hydrogen peroxide reaction for the oxidation of Met-Enk in various biological samples, including brain regions, has been reported previously, although the protocols may slightly vary. Specifically, the manuscript writes about "a critical discovery in the stabilization of enkephalin detection" and that they have "developed a method of methionine stabilization." Those statements are incorrect and the preceding papers that relied on hydrogen peroxide reaction for oxidation of Met-Enk and HPLC for quantification of oxidized Enk forms should be cited. One suggested example is Finn A, Agren G, Bjellerup P, Vedin I, Lundeberg T. Production and characterization of antibodies for the specific determination of the opioid peptide Met5-Enkephalin-Arg6-Phe7. Scand J Clin Lab Invest. 2004;64(1):49-56. doi: 10.1080/00365510410004119. PMID: 15025428.

Another suggestion for this draft is to make the method section more comprehensive by adding information on specific tools and parameters used for statistical analysis:

1) Need to define "proteomics data" and explain whether calculations were performed on EIC for each m/z corresponding to specific peptides or as a batch processing for all detected peptides, from which only select findings are reported here. What type of data normalization was used, and other relevant details of data handling? Explain how Met- and Leu-Enk were identified from DIA data, and what tools were used.

2) Simple Linear Regression Analysis: The text mentions that simple linear regression analysis was performed on forward and reverse curves, and line equations were reported, but it lacks details such as the specific variables being regressed (although figures have labels) and any associated statistical parameters (e.g., R-squared values).

3) Violin Plots: The proteomics data is represented as violin plots with quartiles and median lines. This visual representation is mentioned, but there is no detail regarding the software/tools used for creating these plots.

4) Log Transformation: The text states that the data was log-transformed to reduce skewness, which is a common data preprocessing step. However, it does not specify the base of the logarithm used or any information about the distribution before and after transformation.

5) Two-Way ANOVA: Two-way ANOVA was conducted with peptide and treatment as independent variables. This analysis is described, but there is no information regarding the software or statistical tests used, p-values, post-hoc tests, or any results of this analysis.

6) Paired T-Test: A paired t-test was performed on predator odor proteomic data before and after treatment. This step is mentioned, but specific details like sample sizes, and the hypothesis being tested are not provided.

7) Correlation Analysis: The text mentions a simple linear regression analysis to correlate the levels of Met-Enk and Leu-Enk and reports the slopes. However, details such as correlation coefficients, and p-values are missing.

8) Fiber Photometry Data: Z-scores were calculated for fiber photometry data, and a reference to a cited source is provided. This section lacks details about the calculation of z-scores, and their use in the analysis.

9) Averaged Plots: Z-scores from individual animals were averaged and represented with SEM. It is briefly described, but more details about the number of animals, the purpose of averaging, and the significance of SEM are needed.

A more comprehensive and objective interpretation of results could enhance the overall quality of the paper.

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.

Reviewer #2 (Public Review):

Summary:<br /> Mitochondria in synapses are important to support functional needs, such as local protein translation and calcium buffering. Thus, they may be strategically localized to maximize functional efficiency. In this study, the authors examine whether a correlation exists between the positioning of mitochondria and the structure or function of dendritic spines in the visual cortex of a ferret. Unexpectedly, the authors found no correlation between structural measures of synaptic strength to mitochondria positioning, which may indicate that they are not localized only because of the local energy needs. Instead, the authors discover that mitochondria are positioned preferably in spines that display heterogeneous responses, showing that they are localized to support specific functional needs probably distinct from ATP output.

Strengths:<br /> The thorough analysis provides a yet unprecedented insight into the correlation between synaptic tuning and mitochondrial positioning in the visual cortex in vivo.

Weaknesses:<br /> Analysis of this study suggested that mitochondrial volume does not correlate with structural measures of synaptic strength (e.g. spine volume and post-synaptic density (PSD) area), but it remains to be determined if mitochondria localization is also co-related to the frequency of synaptic activity, and what causes the correlation (driven by mitochondrial positioning, or by synaptic activity).

Reviewer #2 (Public Review):

Summary:<br /> In this manuscript, Mahapatra and Takahashi report on the physiological consequences of pharmacologically blocking either clathrin and dynamin function during compensatory endocytosis or of the cortical actin scaffold both in the calyx of Held synapse and hippocampal boutons in acute slice preparations

Strengths:<br /> Although many aspects of these pharmacological interventions have been studied in detail during the past decades, this is a nice comprehensive and comparative study, which reveals some interesting differences between a fast synapse (Calyx of Held) tuned to reliably transmit at several 100 Hz and a more slow hippocampal CA1 synapse. In particular, the authors find that acute disturbance of the synaptic actin network leads to a marked frequency-dependent enhancement of synaptic depression in the Calyx, but not in the hippocampal synapse. This striking difference between both preparations is the most interesting and novel finding.

Weaknesses:<br /> Unfortunately, however, these findings concerning the different consequences of actin depolymerization are not sufficiently discussed in comparison to the literature. My only criticism concerns the interpretation of the ML 141 and Lat B data. With respect to the Calyx data, I am missing a detailed discussion of the effects observed here in light of the different RRP subpools SRP and FRP. This is very important since Lee et al. (2012, PNAS 109 (13) E765-E774) showed earlier that disruption of actin inhibits the rapid transition of SRP SVs to the FRP at the AZ. The whole literature on this important concept is missing. Likewise, the role of actin for the replacement pool at a cerebellar synapse (Miki et al., 2016) is only mentioned in half a sentence. There is quite some evidence that actin is important both at the AZ (SRP to FRP transition, activation of replacement pool) and at the peri-active zone for compensatory endocytosis and release site clearance. Both possible underlying mechanisms (SRP to FRP transition or release site clearance) should be better dissected.

Reviewer #2 (Public Review):

Summary:<br /> Temporal binding, generally considered a timing illusion, results from actions triggering outcomes after a brief delay, distorting perceived timing. The present study investigates the relationship between attention and the perception of timing by employing a series of tasks involving auditory and visual stimuli. The results highlight the role of attention in event timing and the functional relevance of attention in outcome binding.

Strengths:<br /> - Experimental Design: The manuscript details a well-structured sequence of experiments investigating the attention effect in outcome binding. Thoughtful variations in manipulation conditions and stimuli contribute to a thorough and meaningful investigation of the phenomenon.<br /> - Statistical Analysis: The manuscript employs a diverse set of statistical tests, demonstrating careful selection and execution. This statistical approach enhances the reliability of the reported findings.<br /> - Narrative Clarity: Both in-text descriptions and figures provide clear insights into the experiments and their results, facilitating readers in following the logic of the study.

Weaknesses:<br /> - Conceptual Clarity: The manuscript aims to integrate key concepts in human cognitive functions, including attention, timing perception, and sensorimotor processes. However, before introducing experiments, there's a need for clearer definitions and explanations of these concepts and their known and unknown interrelationships. Given the complexity of attention, a more detailed discussion, including specific types and properties, would enhance reader comprehension.

- Computational Modeling: The manuscript lacks clarity in explaining the model architecture and setup, and it's unclear if control comparisons were conducted. These details are critical for readers to properly interpret attention-related findings in the modeling section. Providing a clearer overview of these aspects will improve the overall understanding of the computational models used.

Reviewer #2 (Public Review):

Summary: The study by Millard et al. investigates the effect of nicotine on alpha peak frequency and pain in a very elaborate experimental design. According to the statistical analysis, the authors found a factor-corrected significant effect for prolonged heat pain but not for alpha peak frequency in response to the nicotine treatment.

Strengths: I very much like the study design and that the authors followed their research line by aiming to provide a complete picture of the pain-related cortical impact of alpha peak frequency. This is very important work, even in the absence of any statistical significance. I also appreciate the preregistration of the study and the well-written and balanced introduction. However, it is important to give access to the preregistration beforehand.

Weaknesses: The weakness of the study revolves around three aspects:

(1) I am not entirely convinced that the authors' analysis strategy provides a sufficient signal-to-noise ratio to estimate the peak alpha frequency in each participant reliably. A source separation (ICA or similar) would have been better suited than electrode ROIs to extract the alpha signal. By using a source separation approach, different sources of alpha (mu, occipital alpha, laterality) could be disentangled.

(2) Also, there's a hint in the literature (reference 49 in the manuscript) that the nicotine treatment may not work as intended. Instead, the authors' decision to use nicotine to modulate the peak alpha frequency and pain relied on other, not suitable work on chronic pain and permanent smokers. In the present study, the authors use nicotine treatment and transient painful stimulation on non-smokers.

In my view, the discussion could be more critical for some aspects and the authors speculate towards directions their findings can not provide any evidence. Speculations are indeed very important to generate new ideas but should be restricted to the context of the study (experimental pain, acute interventions). The unfortunate decision to use nicotine severely hampered the authors' aim of the study.

Impact: The impact of the study could be to show what has not worked to answer the research questions of the authors. The authors claim that their approach could be used to define a biomarker of pain. This is highly desirable but requires refined methods and, in order to make the tool really applicable, more accurate approaches at subject level.

Reviewer #2 (Public Review):

Summary:<br /> In this manuscript, Vöröslakos and colleagues describe a new behavioural testing apparatus called ThermoMaze, which should facilitate controlling when a mouse is exploring the environment vs. remaining immobile. The floor of the apparatus is tiled with 25 plates, which can be individually heated, whereas the rest of the environment is cooled. The mouse avoids cooled areas and stays immobile on a heated tile. The authors systematically changed the location of the heated tile to trigger the mouse's exploratory behaviours. The authors showed that if the same plate stays heated longer, the mouse falls into an NREM sleep state. The authors conclude their apparatus allows easy control of triggering behaviours such as running/exploration, immobility and NREM sleep. The authors also carried out single-unit recordings of CA1 hippocampal cells using various silicone probes. They show that the location of a mouse can be decoded with above-chance accuracy from cell activity during sharp wave ripples, which tend to occur when the mouse is immobile or asleep. The authors suggest that consistent with some previous results, SPW-Rs encode the mouse's current location and any other information they may encode (such as past and future locations, usually associated with them).

Strengths:<br /> Overall, the apparatus may open fruitful avenues for future research to uncover the physiology of transitions from different behavioural states such as locomotion, immobility, and sleep. The setup is compatible with neural recordings. No training is required.

Weaknesses:<br /> I have a few concerns related to the authors' methodology and some limitations of the apparatus's current form. Although the authors suggest that switching between the plates forces animal behaviour into an exploratory mode, leading to a better sampling of the enclosure, their example position heat maps and trajectories suggest that the behaviour is still very stereotypical, restricted mostly to the trajectories along the walls or the diagonal ones (between two opposite corners). This may not be ideal for studying spatial responses known to be affected by the stereotypicity of the animal's trajectories. Moreover, given such stereotypicity of the trajectories mice take before and after reaching a specific plate, it may be that the stable activity of SWR-P ripples used for decoding different quadrants may be representing future and/or past trajectories rather than the current locations suggested by the authors. If this is the case, it may be confusing/misleading to call such activity ' place-selective firing', since they don't necessarily encode a given place per se (line 281).

Another main study limitation is the reported instability of the location cells in the Thermomaze. This may be related to the heating procedure, differences in stereotypical sampling of the enclosure, or the enclosure size (too small to properly reveal the place code). It would be helpful if the authors separate pyramidal cells into place and non-place cells to better understand how stable place cell activity is. This information may also help to disambiguate the SPW-R-related limitations outlined above and may help to solve the poor decoding problem reported by the authors (lines 218-221).

Reviewer #2 (Public Review):

Summary: A new toolbox is presented that builds on previous toolboxes to distinguish between real and spurious oscillatory activity, which can be induced by non-sinusoidal waveshapes. Whilst there are many toolboxes that help to distinguish between 1/f noise and oscillations, not many tools are available that help to distinguish true oscillatory activity from spurious oscillatory activity induced in harmonics of the fundamental frequency by non-sinusoidal waveshapes. The authors present a new algorithm which is based on autocorrelation to separate real from spurious oscillatory activity. The algorithm is extensively validated using synthetic (simulated) data, and various empirical datasets from EEG, intracranial EEG in various locations and domains (i.e. auditory cortex, hippocampus, etc.).

Strengths: Distinguishing real from spurious oscillatory activity due to non-sinusoidal waveshapes is an issue that has plagued the field for quite a long time. The presented toolbox addresses this fundamental problem which will be of great use for the community. The paper is written in a very accessible and clear way so that readers less familiar with the intricacies of Fourier transform and signal processing will also be able to follow it. A particular strength is the broad validation of the toolbox, using synthetic, scalp EEG, EcoG, and stereotactic EEG in various locations and paradigms.

Weaknesses: At many parts in the results section critical statistical comparisons are missing (e.g. FOOOF vs CHO). Another weakness concerns the methods part which only superficially describes the algorithm. Finally, a weakness is that the algorithm seems to be quite conservative in identifying oscillatory activity which may render it only useful for analysing very strong oscillatory signals (i.e. alpha), but less suitable for weaker oscillatory signals (i.e. gamma).

Reviewer #2 (Public Review):

Summary:<br /> This paper further investigates the role of self-assembly of ice-binding bacterial proteins in promoting ice-nucleation. For the P. borealis Ice Nucleating Protein (PbINP) studied here, earlier work had already determined clearly distinct roles for different subdomains of the protein in determining activity. Key players are the water-organizing loops (WO-loops) of the central beta-solenoid structure and a set of non-water-organizing C-terminal loops, called the R-loops in view of characteristically located arginines. Previous mutation studies (using nucleation activity as a read-out) had already suggested the R-loops interact with the WO loops, to cause self-assembly of PbINP, which in turn was thought to lead to enhanced ice-nucleating activity. In this paper, the activities of additional mutants are studied, and a bioinformatics analysis on the statistics of the number of WO- and R-loops is presented for a wide range of bacterial ice-nucleating proteins, and additional electron-microscopy results are presented on fibrils formed by the non-mutated PbINP in E coli lysates.

Strengths:<br /> -A very complete set of additional mutants is investigated to further strengthen the earlier hypothesis.<br /> -A nice bioinformatics analysis that underscores that the hypothesis should apply not only to PbINP but to a wide range of (related) bacterial ice-nucleating proteins.<br /> -Convincing data that PbINP overexpressed in E coli forms fibrils (electron microscopy on E coli lysates).

Weaknesses:<br /> -The new data is interesting and further strengthens the hypotheses put forward in the earlier work. However, just as in the earlier work, the proof for the link between self-assembly and ice-nucleation remains indirect. Assembly into fibrils is shown for E coli lysates expressing non-mutated pbINP, hence it is indeed clear that pbINP self-associates. It is not shown however that the mutations that lead to loss of ice-nucleating activity also lead to loss of self-assembly. A more quantitative or additional self-assembly assay could shine light on this, either in the present or in future studies.

-Also the "working model" for the self-assembly of the fibers remains not more than that, just as in the earlier papers, since the mutation-activity relationship does not contain enough information to build a good structural model. Again, a better model would require different kinds of experiments, that yield more detailed structural data on the fibrils.

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 #2 (Public Review):

Summary:<br /> The authors analyze the functions and regulation of Bon, the sole Drosophila ortholog of the TIF1 family of mammalian transcriptional regulators. Bon has been implicated in several developmental programs, however the molecular details of its regulation have not been well understood. Here, the authors reveal the requirement of Bon in oogenesis, thus establishing a previously unknown biological function for this protein. Furthermore, careful molecular analysis convincingly established the role of Bon in transcriptional repression. This repressor function requires interactions with the NuRD complex and histone methyltransferase SetDB1, as well as sumoylation of Bon by the E3 SUMO ligase Su(var)2-10. Overall, this work represents a significant advance in our understanding of the functions and regulation of Bon and, more generally, the TIF1 family. Since Bon is the only TIF1 family member in Drosophila, the regulatory mechanisms delineated in this study may represent the prototypical and important modes of regulation of this protein family. The presented data are rigorous and convincing. As discussed below, this study can be strengthened by a demonstration of a direct association of Bon with its target genes, and by analysis of the biological consequences of the K20R mutation.

Strengths:<br /> 1. This study identified the requirement for Bon in oogenesis, a previously unknown function for this protein.<br /> 2. Identified Bon target genes that are normally repressed in the ovary, and showed that the repression mechanism involves the repressive histone modification mark H3K9me3 deposition on at least some targets.<br /> 3. Showed that Bon physically interacts with the components of the NuRD complex and SetDB1. These protein complexes are likely mediating Bon-dependent repression.<br /> 4. Identified Bon sumoylation site (K20) that is conserved in insects. This site is required for repression in a tethering transcriptional reporter assay, and SUMO itself is required for repression and interaction with SetDB1. Interestingly, the K20-mutant Bon is mislocalized in the nucleus in distinct puncta.<br /> 5. Showed that Su(var)2-10 is a SUMO E3 ligase for Bon and that Su(var)2-10 is required for Bon-mediated repression.

Weaknesses:<br /> The study would be strengthened by demonstrating a direct recruitment of Bon to the target genes identified by RNA-seq. - It appears that the authors have attempted such an experiment, but it was not successful due to the current technical limitations, as the authors describe in their rebuttal.

The second area where the manuscript can be improved is to analyze the biological function of the K20R mutant Bonus protein. The molecular data suggest that this residue is important for function, and it would be important to confirm this in vivo. - Fig. 5G indeed shows that the 3KR mutant is deficient in inducing repression, which partially addresses this concern. In the future, it would be interesting to test if the single K20R is similarly deficient, and to analyze any resulting phenotypes.

Reviewer #2 (Public Review):

The authors have used transcranial magnetic stimulation (TMS) and motor evoked potentials (MEPs) and TMS-electroencephalography (EEG) evoked potentials (TEPs) to determine how experimental heat pain could induce alterations these metrics.
In Experiment 1 thermal stimuli were administered over the forearm, with the first, second and third block of stimuli consisting of warm but non painful (pre-pain block), painful heat (pain block) and warm but non-painful (post-pain block) temperatures respectively. Painful stimuli led to an increase in the amplitude of the fronto-central N45, with a larger increase associated with higher pain ratings. Experiments 2 and 3 studied the correlation between the increase in the N45 in pain and the effects of a sham stimulation protocol/higher stimulation intensity. They found that the centro-frontal N45 TEP was decreased in acute pain. While their results are in line with reductions seen in motor evoked responses during pain and effort was made to address possible confounding factors (study 2 and 3). This study opens the way for the use exploration of cortical excitability outside M1 in acute pain, and potentially in chronic pain instances. While there is still open discussion on the best strategy to handle auditory and mechanical tactile noise, technological and methodological improvements seen in the last years have greatly improved the signal to noise ratio of TMS-EEG.

Reviewer #2 (Public Review):

Summary:<br /> This is a paper entitled "Plasmodium falciparum MORC protein modulates gene expression through interaction with heterochromatin" describes the role of PfMORC during the intra-erythrocytic cycle of Plasmodium falciparum. Garcia et al. investigated the PfMORC-interacting proteins and PfMORC genomic distribution in trophozoites and schizonts. They also examined the transcriptome of the parasites after partial knockdown of the transcript.

Strengths:<br /> This study is a significant advance in the knowledge of the role of PfMORC in heterochromatin assembly. It provides an in-depth analysis of the PfMORC genomic localisation and its correlation with other chromatin marks and ApiAP2 transcription factor binding.

Weaknesses:<br /> However, most of the conclusions are based on the function of interacting proteins and the genomic localisation of the protein. The authors did not investigate the direct effects of PfMORC depletion on heterochromatin marks. Furthermore, the results of the transcriptomic analysis are puzzling as 50% of the transcripts are downregulated, a phenotype not expected for a heterochromatin marker.

Reviewer #2 (Public Review):

Summary:<br /> Latham A.P. et al. apply simulations and FLIM to analyse several di-block elastin-like polypetides and connect their sequence to the micro-structure of coacervates resulting from their phase-separation.

Strengths:<br /> Understanding the molecular grammar of phase separating proteins and the connection with mesoscale properties of the coacervates is highly relevant. This work provides insights into micro-structures of coacervates resulting from di-block polypetides.

Weaknesses:<br /> The results apply to a very specific architecture (di-block polypetides) with specific sequences.

Reviewer #2 (Public Review):

Leeds et al. employ elegant in vitro experiments and sophisticated numerical modeling to investigate the ability of mechanical coupling to coordinate the growth of individual microtubules within microtubule bundles, specifically k-fibers. While individual microtubules naturally polymerize at varying rates, their growth must be tightly regulated to function as a cohesive unit during chromosome segregation. Although this coordination could potentially be achieved biochemically through selective binding of polymerases and depolymerases, the authors demonstrate, using a novel dual laser trap assay, that mechanical coupling alone can also coordinate the growth of in vitro microtubule pairs.

By reanalyzing recordings of single microtubules growing under constant force (data from their own previous work), the authors investigate the stochastic kinetics of pausing and show that pausing is suppressed by tension. Using a constant shared load, the authors then show that filament growth is tightly coordinated when pairs of microtubules are mechanically coupled by a material with sufficient stiffness. In addition, the authors develop a theoretical model to describe both the natural variability and force dependence of growth, using no freely adjustable parameters. Simulations based on this model, which accounts for stochastic force-dependent pausing and intrinsic variability in microtubule growth rate, fit the dual-trap data well.

Overall, this study illuminates the potential of mechanical coupling in coordinating microtubule growth and offers a framework for modeling k-fibers under shared loads. The research exhibits meticulous technical rigor and is presented with exceptional clarity. It provides compelling evidence that a minimal, reconstituted biological system can exhibit complex behavior. As it currently stands, the paper is highly informative and valuable to the field.

Reviewer #2 (Public Review):

In this study, the authors used ANM-LD and GNM-based Transfer Entropy to investigate the allosteric communications network of CFTR. The modeling results are validated with experimental observations. Key residues were identified as pivotal allosteric sources and transducers and may account for disease mutations.

The paper is well written and the results are significant for understanding CFTR biology.

Reviewer #2 (Public Review):

The authors provide solid molecular and cellular evidence that ULK4 and STK36 not only interact, but that STK36 is targeted (transported?) to the cilium by ULK4. Their data helps generate a model for ULK4 acting as a scaffold for both STK36 and its substrate, Gli2, which appear to co-localise through mutual binding to ULK4. This makes sense, given the proposed role of most pseuodkinases as non-catalytic signaling hubs. There is also an important mechanistic analysis performed, in which ULK4 phosphorylation in an acidic consensus by STK36 is demonstrated using IP'd STK36 or an inactive 'AA' mutant, which suggests this phosphorylation is direct.

The major strength of the study is the well-executed combination of logical approaches taken, including expression of various deletion and mutation constructs and the careful (but not always quantified in immunoblot) effects of depleting and adding back various components in the context of both STK36 and ULK3, which broadens the potential impact of the work. The biochemical analysis of ULK4 phosphorylation appears to be solid, and the mutational study at a particular pair of phosphorylation sites upstream of an acidic residue (notably T2023) is further strong evidence of a functional interaction between ULK4/STK36. The possibility that ULK4 requires ATP binding for these mechanisms is not approached, though would provide significant insight: for example it would be useful to ask if Lys39 in ULK4 is involved in any of these processes, because this residue is likely important for shaping the ULK4 substrate-binding site as a consequence of ATP binding; this was originally shown in PMID 24107129 and discussed more recently in PMID: 33147475 in the context of the large amount of ULK4 proteomics data released.

The discussion is excellent, and raises numerous important future work in terms of potential transportation mechanisms of this complex. It also explains why the ULK4 pseudokinase domain is linked to an extended C-terminal region. Does AF2 predict any structural motifs in this region that might support binding to Gli2?

A weakness in the study, which is most evident in Figure 1, where Ulk4 siRNA is performed in the NIH3T3 model (and effects on Shh targets and Gli2 phosphorylation assessed), is that we do not know if ULK4 protein is originally present in these cells in order to actually be depleted. Also, we are not informed if the ULK4 siRNA has an effect on the 'rescue' by HA-ULK4; perhaps the HA-ULK4 plasmid is RNAi resistant, or if not, this explains why phosphorylation of Gli2 never reaches zero? Given the important findings of this study, it would be useful for the authors to comment on this, and perhaps discuss if they have tried to evaluate endogenous levels of ULK4 (and Stk36) in these cells using antibody-based approaches, ideally in the presence and absence of Shh. The authors note early on the large number of binding partners identified for ULK4, and siRNA may unwittingly deplete some other proteins that could also be involved in ULK4 transport/stability in their cellular model.

The sequence of ULK4 siRNAs is not included in the materials and methods as far as I can see, though this is corrected in the next version of the manuscript.

Reviewer #2 (Public Review):

By mapping the sites of the Mcm2-7 replicative helicase loading across the budding yeast genome using high-resolution chromatin endogenous cleavage or ChEC, Bedalov and colleagues find that these markers for origins of DNA replication are much more broadly distributed than previously appreciated. Interestingly, this is consistent with early reconstituted biochemical studies that showed that the ACS was not essential for helicase loading in vitro (e.g. Remus et al., 2009, PMID: 19896182). To accomplish this, they combined the results of 12 independent assays to gain exceptionally deep coverage of Mcm2-7 binding sites. By comparing these sites to previous studies mapping ssDNA generated during replication initiation, they provide evidence that at least a fraction of the 1600 most robustly Mcm2-7-bound sequences act as origins. A weakness of the paper is that the group-based (as opposed to analyzing individual Mcm2-7 binding sites) nature of the analysis prevents the authors from concluding that all of the 1,600 sites mentioned in the title act as origins. The authors also show that the location of Mcm2-7 location after loading are highly similar in the top 500 binding sites, although the mobile nature of loaded Mcm2-7 double hexamers prevents any conclusions about the location of initial loading. Interestingly, by comparing subsets of the Mcm2-7 binding sites, they find that there is a propensity of at least a subset of these sites to be nucleosome depleted, to overlap with at least a partial match to the ACS sequence (found at all of the most well-characterized budding yeast origins), and a GC-skew centered around the site of Mcm loading. Each of these characteristics is related to previously characterized S. cerevisiae origins of replication.

Overall, this manuscript greatly broadens the number of sites that are capable of loading Mcm2-7 in budding yeast cells and shows that a subset of these additional sites act as replication origins. Although these studies show that the sequence specificity of S. cerevisiae replication origins still sets it apart from metazoan origins, the ability to license and initiate replication from sites with increasing sequence divergence suggests a previously unappreciated versatility.

Specific points:

1. The authors need to come up with a consistent name for loaded Mcms at an origin. In the manuscript they variously use 'MCM'(page 3), 'Mcm complexes' (page 4), 'MCM double hexamer' (page 6), and 'double-helicase' (page 8) to describe the Mcm2-7 complexes detected in their ChEC experiments. They should pick one name (Mcm2-7 double hexamer or MCM double hexamer would be the most accurate and clear) and stick with it throughout the manuscript.

2. The authors state that "It is notable that, when Mcm is present, it is present predominantly as a single double-hexamer (right panel of Figure 3A), and that this remains true across the entire range of abundance shown in Figure 3A." This statement would be improved by prefacing it with "Based on the size of the protected regions" or some other clarifying statement that lets the reader know what they should be looking for in the data in 3A.


3. The revised statements that "We have previously used Southern blotting to demonstrate that approximately 90% of the DNA at one of the most acive known origins (ARS1103) is cut by Mcm-MNase (Foss et al., 2021), and to thereby infer that 90% of cells have a double- helicase loaded at this origin. Using this as a benchmark, we estimate that ~1-2 % cells have an Mcm complex loaded at the Mcm binding sites in the eighth cohort (ranks 1401- 1600)." partially clarifies how the authors came to the 1-2% number, however, the calculation is still unclear. Based on Figure 1A, there are at least three logs (1,00 fold) difference in the number of CBMSs between the best origins (which is what they state the 90% comes from) to anywhere close to the 1400-1600 rank. Seems like the number should be at best 0.1% and probably less. Either way, the authors need to explain this calculation either in the text or in the text. This sort of number tends to get thrown around later and without a clear explanation readers cannot evaluate its credibility. 


4. The authors make the point in the introduction and discussion that recent single-molecule studies of replication origins indicate that as many as 20% of the origins identified are outside of known origins. This is very interesting but there seems to be a missed opportunity of comparing the location of these origins with the CBMSs. It would improve the manuscript to include some sort of comparison rather than using only the much older and less accurate ssDNA analysis.

5. The authors state at the end of the first paragraph on page 6 that the ChEC data is "very reproducible" which does seem to be the case but it is a little confusing for the knowledgeable reader since one would expect quite different results for an HU arrested strain versus a asynchronous or G1 arrested strain. This is hidden in the analysis in Figure S1 since 13 experiments are compared against one in each plot, however, if one x one comparisons were done there would certainly be substantial differences (or if there are not, there is a problem with the data - e.g. HU arrested cells should lack licensing at early firing origins).

6. On page 8 the authors state, "First, clear peaks of ssDNA extend down to the eighth cohort..." This seems to be stretching the data. There are clear peaks for the first five cohorts and then there is a notable change with any peak being much broader, extending over at least 10,000 bp. The authors should reconsider their statement here as it is not well supported by the data.

7. There is one last missing reference. Wherever Eaton et al, 2010 is referenced Berbenetz, et al, 2010 (full ref below) should also be referenced as they come to very similar conclusions.

Berbenetz, N. M., Nislow, C. & Brown, G. W. Diversity of eukaryotic DNA replication origins revealed by genome-wide analysis of chromatin structure. PLoS Genet 6, (2010).

Reviewer #2 (Public Review):

Phage satellites are fascinating elements that have evolved to hijack phages for induction, packaging, and transfer, promoting their widespread dissemination in nature. It is remarkable how different satellites use conserved strategies of parasitism, utilising unrelated proteins that perform similar roles in their cognate elements. In the current manuscript, Dr. Seed and coworkers elucidated the mechanism used by one family of satellites, the PLEs, to produce small capsids, a process that inhibits phage reproduction while increasing PLE transmission. The work is presented beautifully, and the results are astonishing. The authors identified the gene responsible for generating the small capsids, characterised its role in the PLE transfer and phage inhibition, and determined the structure of the PLE-sized small capsids. It is a truly impressive piece of work.

Reviewer #2 (Public Review):

Summary:<br /> The authors investigated how neuronal activity and metrics of plasticity using local electrical stimulation in the GPi were different between Parkinson's disease and dystonia patients.

Strengths:<br /> The introduction highlights the importance of the work and the fundamental background needed to understand the rest of the paper. It also clearly lays out the novelty (i.e., that the dynamics of plastic effects in GPi between dystonia and PD have not been directly compared).

The methods are clearly described and the results are well organized in the figures.

The results are strong with measurements from a large population of patients for each disease group and with distinct findings for each group.

Weaknesses:<br /> The discussion was hard to follow in several places, making it difficult to fully appreciate how well the authors' claims and conclusions are justified by their data, mostly in relation to the plasticity results. It may help to summarize the relevant findings for each section first and then further expand on the interpretation, comparison with prior work, and broader significance. Currently, it is hard to follow each section without knowing which results are being discussed until the very end of the section. With the current wording in the "Neuronal correlates.." section, it is not always clear which results are from the current manuscript, and where the authors are referring to past work.

Also, I felt that more discussion could be used to highlight the significance of the current results by comparing and/or contrasting them to prior relevant work and mechanisms. The novelty or impact is not very clear as written. Could this be further substantiated in the Discussion?

Some specific comments and questions about the Discussion:<br /> Lines 209-211 - This sentence was hard to understand, could it be clarified?<br /> Lines 211-213 - What do phasic and tonic components mean exactly? Could this be specifically defined? Are there specific timescales (as referred to in Intro)?<br /> Lines 215-217 - It's not clear what was delayed in dystonia, and how the authors are trying to contrast this with the faster time course in PD. I think some of this is explained in the introduction, but could also be re-summarized here as relevant to the results discussed.<br /> Lines 223-224 - I'm not sure I follow the implication that network reorganization leads to delayed functional benefits. Could this be further elaborated?

Could the absence of a relationship between FR and disease in PD be discussed?

It wasn't very clear how the direct pathway can be attributed to plasticity changes if the GPi makes up both the direct and indirect pathways. Could this be further clarified?

The mechanism of short- and long-term plasticity as applied in the protocols used in this work are outlined in reference to previous citations [15, 16, 18]. Because this is a central aspect of the current work and interpreting the results, it was difficult to appreciate how these protocols provide distinct metrics of short and long-term plasticity in GPi without some explanation of how it applies to the current work and the specific mechanisms. It would also help to be able to better link how the results fit with the broader conclusions.

In the Conclusion, it was difficult to understand the sentence about microcircuit interaction (line 232) and how it selectively modulates the efficacy of target synapses. Some further explanation here would be helpful. Also, it was not clear how these investigations (line 237) provide cellular-level support for closed-loop targeting. Could the reference to closed-loop targeting also be further explained?

How is the burst index calculated (Methods)?

Figures and figure captions are missing some details:

Fig. 1 - What does shading represent?

Fig. 2 - Can the stimulation artifact be labeled so as not to be confused with the physiological signal? Is A representing the average of all patients or just one example? Are there confidence intervals for this data as it's not clear if the curves are significantly different or not (may not be important to show if just one example)? Same for D. What is being plotted in E? Is this the exponential fitted on data? Can this be stated in the figure citation directly so readers don't have to find it in the text, where it may not be directly obvious which figure the analyses are being applied towards?

What does shading here represent?

Reviewer #2 (Public Review):

Summary<br /> This study replicates a 2017 study in which the authors reviewed papers for four key elements of rigor: inclusion of sex as a biological variable, randomization of subjects, blinding outcomes, and pre-specified sample size estimation. Here they screened 298 published papers for the four elements. Over a 10 year period, rigor (defined as including any of the 4 elements) failed to improve. They could not detect any differences across the journals they surveyed, nor across models. They focused primarily on cardiovascular disease, which both helps focus the research but limits the potential generalizability to a broader range of scientific investigation. There is no reason, however, to believe rigor is any better or worse in other fields, and hence this study is a good 'snapshot' of the progress of improving rigor over time.

Strengths<br /> The authors randomly selected papers from leading journals, e.g., PNAS). Each paper was reviewed by 2 investigators. They pulled papers over a 10-year period, 2011 to 2021, and have a good sample of time over which to look for changes. The analysis followed generally accepted guidelines for a structured review.

Weaknesses<br /> The authors did not use the exact same journals as they did in the 2017 study. This makes comparing the results complicated. Also, they pulled papers from 2011 to 2021, and hence cannot assess the impact of their own prior paper.<br /> The authors write "the proportion of studies including animals of both biological sexes generally increased between 2011 and 2021, though not significantly (R2= 0.0762, F(1,9)= 0.742, p= 0.411 (corrected p=8.2". This statement is not rigorous because the regression result is not statistically significant. Their data supports neither a claim of an increase nor a decrease over time. A similar problem repeats several times in the remainder of their results presentation.<br /> I think the Introduction and the Discussion are somewhat repetitive and the wording could be reduced.

Impact and Context<br /> Lack of reproducibility remains an enormous problem in science, plaguing both basic and translational investigations. With the increased scrutiny on rigor, and requirements at NIH and other funding agencies for more rigor and transparency, one would expect to find increasing rigor, as evidenced by authors including more study design elements (SDEs) that are recommended. This review found no such change, and this is quite disheartening. The data implies that journals-editors and reviewers-will have to increase their scrutiny and standards applied to preclinical and basic studies. This work could also serve as a call to action to investigators outside of cardiovascular science to reflect on their own experiences and when planning future projects.

Reviewer #2 (Public Review):

Summary:<br /> The study's goal is to characterize and validate tumor-reactive T cells in liver metastases of uveal melanoma (UM), which could contribute to enhancing immunotherapy for these patients. The authors used single-cell RNA and TCR sequencing to find potential tumor-reactive T cells and then used patient-derived xenograft (PDX) models and tumor sphere cultures for functional analysis. They discovered that tumor-reactive T cells exist in activated/exhausted T cell subsets and in cytotoxic effector cells. Functional experiments with isolated TILs show that they are capable of killing UM cells in vivo and ex vivo.

Strengths:<br /> The study highlights the potential of using single-cell sequencing and functional analysis to identify T cells that can be useful for cell therapy and marker selection in UM treatment. This is important and novel as conventional immune checkpoint therapies are not highly effective in treating UM. Additionally, the study's strength lies in its validation of findings through functional assays, which underscores the clinical relevance of the research.

Weaknesses:<br /> The manuscript may pose challenges for individuals with limited knowledge of single-cell analysis and immunology markers, making it less accessible to a broader audience.

Reviewer #2 (Public Review):

The manuscript presents a computational model of how an organism might learn a map of the structure of its environment and the location of valuable resources through synaptic plasticity, and how this map could subsequently be used for goal-directed navigation.

The model is composed of 'map cells', which learn the structure of the environment in their recurrent connections, and 'goal-cell' which store the location of valued resources with respect to the map cell population. Each map cell corresponds to a particular location in the environment due to receiving external excitatory input at this location. The synaptic plasticity rule between map cells potentiates synapses when activity above a specified threshold at the pre-synaptic neuron is followed by above-threshold activity at the post-synaptic neuron. The threshold is set such that map neurons are only driven above this plasticity threshold by the external excitatory input, causing synapses to only be potentiated between a pair of map neurons when the organism moves directly between the locations they represent. This causes the weight matrix between the map neurons to learn the adjacency for the graph of locations in the environment, i.e. after learning the synaptic weight matrix matches the environment's adjacency matrix. Recurrent activity in the map neuron population then causes a bump of activity centred on the current location, which drops off exponentially with the diffusion distance on the graph. Each goal cell receives input from the map cells, and also from a 'resource cell' whose activity indicates the presence or absence of a given values resource at the current location. Synaptic plasticity potentiates map-cell to goal-cell synapses in proportion to the activity of the map cells at time-points when the resource cell is active. This causes goal cell activity to increase when the activity of the map cell population is similar to the activity where the resource was obtained. The upshot of all this is that after learning the activity of goal cells decreases exponentially with the diffusion distance from the corresponding goal location. The organism can therefore navigate to a given goal by doing gradient ascent on the activity of the corresponding goal cell. The process of evaluating these gradients and using them to select actions is not modelled explicitly, but the authors point to the similarity of this mechanism to chemotaxis (ascending a gradient of odour concentration to reach the odour source), and the widespread capacity for chemotaxis in the animal kingdom, to argue for its biological plausibility. The ideas are interesting and the presentation of the results in the manuscript is generally clear.

Closely related ideas have been explored in previous work, and there are some aspects of how the work relates to previous literature that it would be useful to clarify. Several lines of work have proposed learning long-range relationships between states in the environment, to enable navigation to rewarding goals by effectively descending distance gradients. The most well-known of these in the neuroscience literature is the Successor Representation (SR) (Dayan 1993), which is defined as the expected discounted future occupancy of each state given the current state. As noted in the discussion, this is closely related to the representation learnt by the map cells in the current model. The key difference is that the successor representation uses state-state transitions under a given policy (a mapping from states to actions), whereas the current model uses the adjacency matrix between states, which depends only on the environment and hence is independent of the policy followed while the representation is learnt (given sufficient exploration). This policy independence is useful, as the SR can fail to generate good routes to goals when these are very different from the policy under which it was learned (see Russek et al. https://doi.org/10.1371/journal.pcbi.1005768). However, there are several prior proposals for policy-independent SR-like mechanisms that it would be useful to discuss. Baram et al. (https://doi.org/10.1101/421461) propose navigating to goals by doing gradient descent on diffusion distances, computed as powers of the adjacency matrix as in the current work. One limitation of using the adjacency matrix is that it does not handle situations where transitions between states are probabilistic, which is not a big issue for navigation in physical space but is for applying the mechanism to cognitive tasks more broadly. There are prior ideas for learning policy-independent representations similar to the SR that do not have this limitation. Kaelbling (Learning to achieve goals, IJCAI, 1993) proposed using an off-policy learning rule similar to Q-learning, to learn shortest path distances between states. Piray and Daw https://doi.org/10.1038/s41467-021-25123-3) consider a default representation, which is a successor-like representation under a generic default policy, building on the Linear Markov Decision Process (LMDP) framework of Todorov (https://doi.org/10.1073/pnas.0710743106). Also relevant to the current study is the work of Fang et al. (https://doi.org/10.7554/eLife.80680) who, as in the current work, propose using recurrent network dynamics to compute a long-range representation (the SR) from synaptic weights that store local transition information.

One other area where I felt the work could be better integrated with the existing literature was the discussion of mapping the model onto brain circuits. An interesting and attractive aspect of the work is the idea that the relatively high-level operation of goal-directed navigation could be built on top of evolutionarily older mechanisms for ascending odour gradients. Given this framing, I was expecting the discussion of brain circuits to consider interactions between spatial mapping systems and regions involved in olfactory processing. However the discussion of mammalian brains focussed exclusively on the hippocampus without any link to olfaction, which feels like a missed opportunity. I am not an expert on olfaction, but one region that seems particularly interesting in this context is the olfactory tubercle (see Wesson & Wilson https://doi.org/10.1016/j.neubiorev.2010.08.004 for a review). This region is contiguous with the ventral striatum and has similar local circuitry, receives strong input from olfactory regions, but also input from the hippocampal formation, and a strong dopaminergic innervation from VTA. This suggests a mapping of the model to brain circuits in which map cells in the hippocampal formation project to goal cells in the olfactory tubercle, with the dopaminergic input acting as resource cells (note that different dopamine neuron populations appear to respond to different reward types, see e.g. https://doi.org/10.1038/s41586-022-04954-0, https://doi.org/10.1101/2023.05.09.540067). I was also surprised not to see any discussion of internally generated sequential activity in the hippocampus as a possible mechanism for the look-ahead needed to evaluate the goal distance gradient, particularly given the authors suggest that vicarious trial and error (VTE) is a behavioural signature of this gradient sampling, and it is known that during VTE hippocampus plays out internally generated sequences of possible future locations (see Redish https://doi.org/10.1038/nrn.2015.30).

Reviewer #2 (Public Review):

In this study, Lewis et al seek to further define the role of ROM1. ROM1 is a tetraspanin protein that oligomerizes with another tetraspanin, PRPH2, to shape the rims of the membrane discs that comprise the light sensitive outer segment of vertebrate photoreceptors. ROM1 knockout mice and several PRPH2 mutant mice are reexamined. The conclusion reached is that ROM1 is redundant to PRPH2 in regulating the size of newly forming discs, although excess PRPH2 is required to compensate for the loss of ROM1.

This replicates earlier findings, while adding rigor using a mass spectrometry-based approach to quantitate the ratio of ROM1 and PRPH2 to rhodopsin (the protein packed in the body of the disc membranes) and careful analysis of tannic acid labeled newly forming discs using transmission electron microscopy.

In ROM1 knockout mice PRPH2 expression was found to be increased so that the level of PRPH2 in those mice matches the combined amount of PRPH2 and ROM1 in wildtype mice. Despite this, there are defects in disc formation that are resolved when the ROM1 knockout is crossed to a PRPH2 overexpressing line. A weakness of the study is that the molar ratios between ROM1, PRPH2 and rhodopsin were not measured in the PRPH2 overexpressing mice. This would have allowed the authors to be more precise in their conclusion that a sufficient excess of PRPH2 can compensate for defects in ROM1.

Reviewer #2 (Public Review):

Summary:<br /> Here the authors address the idea that postural and movement control are differentially impacted with stroke. Specifically, they examined whether resting postural forces influenced several metrics of sensorimotor control (e.g., initial reach angle, maximum lateral hand deviation following a perturbation, etc.) during movement or posture. The authors found that resting postural forces influenced control only following the posture perturbation for the paretic arm of stroke patients, but not during movement. They also found that resting postural forces were greater when the arm was unsupported, which correlated with abnormal synergies (as assessed by the Fugl-Meyer). The authors suggest that these findings can be explained by the idea that the neural circuitry associated with posture is relatively more impacted by stroke than the neural circuitry associated with movement. They also propose a conceptual model that differentially weights the reticulospinal tract (RST) and corticospinal tract (CST) to explain greater relative impairments with posture control relative to movement control, due to abnormal synergies, in those with stroke.

Strengths:<br /> The strength of the paper is that they clearly demonstrate with the posture task (i.e., active holding against a load) that the resting postural forces influence subsequent control (i.e., the path to stabilize, time to stabilize, max. deviation) following a sudden perturbation (i.e., suddenly removal of the load). Further, they can explain their findings with a conceptual model, which is depicted in Figure 9.

Weaknesses:<br /> Current weaknesses and potential concerns relate to i) not displaying or reporting the results of healthy controls and non-paretic arm in Experiment 2 and ii) large differences in force perturbation waveforms between movement (sudden onset) and posture (sudden release), which could potentially influence the results and or interpretation.

Larger concerns<br /> 1. Additional analyses to further support the interpretation. In Experiment 1 the authors present the results for the paretic arm, non-paretic arm, and controls. However, in Experiment 2 for several key analyses, they only report summary statistics for the paretic arm (Figure 5D-I; Figure 6D-E; Figure 7F). It is understood that the controls have much smaller resting postural force biases, but they are still present (Figure 3B). It would strengthen the position of the paper to show that controls and the non-paretic arm are not influenced by resting postural force biases during movement and particularly during posture, while acknowledging the caveat that the resting positional forces are smaller in these groups. It is recommended that the authors report and display the results shown in Figure 5D-I; Figure 6D-E; Figure 7F for the controls and non-paretic arm. If these results are all null, the authors could alternatively place these results in an additional supplementary.

Further, the results could be further boosted by reporting/displaying additional analyses. In Figure 6D the authors performed a correlation analysis. Can they also display the same analysis for initial deviation and endpoint deviation for the data shown in Figure 5D-F & 5G-I, as well for 7F for the path to stabilization, time to stabilization, and max deviation? This will also create consistency in the analyses performed for each dependent variable across the paper.

2. Inconsistency in perturbations that would differentially impact muscle and limb states during movement and posture. It is well known that differences in muscle state (activation / preloaded, muscle fiber length and velocity) and limb state (position and velocity) impact sensorimotor control (Pruszynski, J. A., & Scott, S. H. (2012). Experimental brain research, 218, 341-359.). Of course, it is appreciated that it is not possible to completely control all states when comparing movement and posture (i.e., muscle and limb velocity). However, using different perturbations differentially impacts muscle and limb states. Within this paper, the authors used very different force waveforms for movement perturbations (i.e., 12 N peak, bell-shaped, 0.7ms duration -> sudden force onset to push the limb; Figure 6A) and posture perturbations (i.e., 6N, 2s ramp up -> 3s hold -> sudden force release that resulted in limb movement; Figure 4) that would differentially impact muscle (and limb) states. Preloaded muscle (as in the posture perturbation) has a very different response compared to muscle that has little preload (as in the movement perturbations, where muscles that would resist a sudden lateral perturbation would likely be less activated since they are not contributing to the forward movement). Would the results hold if the same perturbation had been used for both posture and movement (e.g., 12 N pulse for both experiments)? It is recommended that the authors comment and discuss in the paper why they chose different perturbations and how that might impact the results.

Relatedly, an alternative interpretation of the results is that preloading muscle for stroke patients, whether by supporting the weight of one's arm (experiment 1) or statically resisting a load prior to force release (experiment 2), leads to a greater postural force bias that can subsequently influence control. It is recommended that the authors comment on this.

Reviewer #2 (Public Review):

The present study by Ye et al. characterizes some of the major effects of ferroptotic stress on tooth morphogenesis.

The strengths of this study are its innovative nature and the beautiful histology. Mechanistic data are convincing Overall, the study is well done.

Reviewer #2 (Public Review):

The formation of long-term memory representations requires the continuous updating of ongoing representations. Various studies have shown that the left angular gyrus (AG) may support this cognitive operation. However, this study demonstrates that this brain region plays a causal role in the formation of long-term memory representations, affecting both the neural and behavioural measures of information binding.

A significant strength of this work is that it is the first one to test the hypothesis that the left angular gyrus has a causal role in the reconfiguration and binding of long-term memory representations by comparing when insights are primarily derived from direct observation versus imagination. Consequently, the results from this manuscript have the potential to be informative for all areas of cognitive research, including basic perception, language cognition, and memory.

Furthermore, this study presents a comprehensive set of measurements on the same individuals, encompassing various task-related behavioural measures, EEG data, and questionnaire responses.

There are, however, some weaknesses. One of them pertains to the link between the observed results and the conclusions. While the observed memory reconfiguration/changes are attributed to the angular gyrus in this study, it remains unclear whether these effects are solely a result of the AG's role in reconfiguration processes or to what extent the hippocampus might also mediate these memory effects (e.g., Tambini et al., 2018; Hermiller et al., 2019).

Another weakness in this manuscript is the use of different groups of participants for the key TMS intervention, along with underspecified or incomplete hypotheses/predictions. Furthermore, in some instances, the types of analyses used do not appear to be suitable for addressing the questions posed by the current study, and there is limited explanation provided for the choice of analyses and questionnaires.

Reviewer #2 (Public Review):

The MS describes an approach to monitor microglial structural dynamics and correlate it to ongoing changes in brain state during sleep-wake cycles. The main novelty here is the use of miniaturized 2p microscopy, which allows tracking microglia surveillance over long periods of hours, while the mice are allowed to freely behave. Accordingly, this experimental setup would permit to explore long-lasting changes in microglia in more naturalistic environment, which were previously not possible to identify otherwise. The findings provide key advances to the research of microglia during natural sleep and wakefulness, as opposed to anesthesia. The main findings of the paper are that microglia increase their process motility and surveillance during REM and NREM sleep as compared to the awake state. The authors further show that sleep deprivation induces opposite changes in microglia dynamics- limiting their surveillance and size. The authors then demonstrate potential causal role for norepinephrine secretion from the locus coeruleus (LC) which is driven by beta 2 adrenergic receptors (b2AR) on microglia. '

The authors have nicely demonstrated and technically validated their main conclusions. In particular, they demonstrate the utility of miniaturized 2p imaging for long lasting imaging of microglia structural changes according to sleep state over the time course of hours. The authors have done a good job in addressing all my previous concerns and provide sound evidence for sleep state induced dynamics of microglia, which is modulated by NE and depends on b2AR.

One impressive point is the ability to longitudinally track the same microglial cells in the field of view for many hours, which is highly valuable and was impossible to achieve with head fixed imaging.

The authors support their observation by using a global b2AR KO mice, which ravel impaired microglial dynamics during sleep states.

While previous evidence supports high expression and function of b2AR in microglia, these receptors are expressed throughout the brain and periphery. Therefore, the authors correctly state that the current data they show, using global b2AR KO mice, cannot be used to state a direct effect on microglia dynamics and this would warrant future experiments with cell-specific genomic manipulation.

To summarize, the main conclusions of the paper are well validated and supported with the experimental layout and analysis.

Reviewer #2 (Public Review):

Haoyang Wu et al. have shown that the symmetric arginine methyltransferase PRMT5 binds to the promoter region of several essential genes and represses their expression, leading to neuronal cell death. Knocking down PRMT5 in HT-22 cells by shRNA leads to pertinent improvement in cell survival after oxygen-glucose deprivation (OGD) conditions. In another set of experiments, inhibition of the catalytic activity of PRMT5 by a specific inhibitor, EPZ015666, in a middle cerebral artery occlusion (MCAO) mice model also showed protective effects against neuronal cell death. In this manuscript, the authors have established the negative role of PRMT5 in cerebral ischemia both in vitro and in vivo.

However, my primary concern is the novelty of the manuscript. It has already been reported that inhibition of PRMT5 attenuates cerebral ischemia/reperfusion condition (Inhibition of PRMT5 attenuates cerebral ischemia/reperfusion-induced inflammation and pyroptosis through suppression of NF-κB/NLRP3 axis. Xiang Wu et al. Neuroscience Letters, Volume 776, 2022, 136576, ISSN 0304-3940, https://doi.org/10.1016/j.neulet.2022.136576.). Even these authors have also shown that treatment of PRMT5 specific catalytic inhibitor, LLY-283, could rescue ischemia-induced over-expression of inflammation-related factors.

However, it would be better to verify the specificity of the inhibitor, EPZ015666, using other methyltransferases to be sure that the rescue is indeed mediated by PRMT5 catalytic inhibition.

Reviewer #2 (Public Review):

Summary: The idea of harnessing small molecules that may affect protein-protein interactions to promote axon regeneration is interesting and worthy of study. In this manuscript Liu et al. explore a 14-3-3-Spastin complex and its role in axon regeneration.

Strengths: Some of the effects of FC-A on locomotor recovery after spinal cord contusion look interesting

Weaknesses: The manuscript falls short of establishing that a 14-3-3-Spastin complex is important for any FC-A-dependent effects and there are several issues with data quality that make it difficult to interpret the results. Importantly, the effects of the spastin inhibitor has a major impact on neurite outgrowth suggesting that cells simply cannot grow in the presence of the inhibitor and raising serious questions about any selectivity for FC-A - dependent growth. Aspects of the histology following spinal cord injury were not convincing.

Reviewer #2 (Public Review):

Summary:

We often have prior expectations about how the sensory world will change, but it remains an open question as to how these expectations are integrated into perceptual decisions. In particular, scientists have debated whether prior knowledge principally changes the decisions we make about the perceptual world, or directly alters our perceptual encoding of incoming sensory evidence.

The authors aimed to shed light on this conundrum by using a novel psychophysical task while measuring EEG signals that have previously been linked to either the sensory encoding or response selection phase of perceptual choice. The results convincingly demonstrate that both features of perceptual decision-making are modulated by prior expectations - but that these biases in neural process emerge over different time courses (i.e., decisional signals are shaped early in learning, but biases in sensory processing are slower to emerge).

Another interesting observation unearthed in the study - though not strictly linked to this perceptual/decisional puzzle - is that neural signatures of focused attention are exaggerated on trials where participants are given neutral (i.e. uninformative) cues. This is consistent with the idea that observers are more attentive to incoming sensory evidence when they cannot rely on their expectations.

In general, I think the study makes a strong contribution to the literature and does an excellent job of separating 'perceiving' from 'responding'. More perhaps could have been done though to separate 'perceiving' and 'responding' from 'deciding' (see below).

Strengths:

The work is executed expertly and focuses cleverly on two features of the EEG signals that can be closely connected to specific loci of the perceptual decision-making process - the SSVEP which connects closely to sensory (visual) encoding, and Mu-Beta lateralisation which connects closely to movement preparation. This is a very appropriate design choice given the authors' research question.

Another advantage of the design is the use of an unusually long training regime (i.e., for humans) - which makes it possible to probe the emergence of different expectation biases in the brain over different timecourses, and in a way that may be more comparable to work with nonhuman animals (who are routinely trained for much longer than humans).

Weaknesses:

In my view, the principal shortcoming of this study is that the experimental task confounds expectations about stimulus identity with expectations about to-be-performed responses. That is, cues in the task don't just tell participants what they will (probably) see, but what they (probably) should do.

In many respects, this feature of the paradigm might seem inevitable, as if specific stimuli are not connected to specific responses, it is not possible to observe motor preparation of this kind (e.g., de Lange, Rahnev, Donner & Lau, 2013 - JoN).

However, the theoretical models that the authors focus on (e.g., drift-diffusion models) are models of decision (i.e., commitment to a proposition about the world) as much as they are models of choice (i.e., commitment to action). Expectation researchers interested in these models are often interested in asking whether predictions influence perceptual processing, perceptual decision, and/or response selection stages (e.g., Feuerriegel, Blom & Hoogendorn, 2021 - Cortex), and other researchers have shown that parameters like drift bias and start point bias can be shifted in paradigms where observers cannot possibly prepare a response (e.g., Thomas, Yon, de Lange & Press, 2020 - Psych Sci).

The present paradigm used by Walsh et al makes it possible to disentangle sensory processing from later decisional processes, but it blurs together the processes of deciding about the stimulus and choosing/initiating the response. This ultimately limits the insights we can draw from this study - as it remains unclear whether rapid changes in motor preparation we see reflect rapid acquisition of new decision criterion or simple cue-action learning. I think this would be important for comprehensively testing the models the authors target - and a good avenue for future work.

Reviewer #2 (Public Review):

In this study, the researchers utilized ribotag-based RNA sequencing to examine the gene expression response, presumably involving actively translated RNAs, in dorsal root ganglia (DRGs) after an injury. They generated multiple lines of mice capable of expressing a fluorescent protein (FP) reporter, tdTomato, along with a ribotag marked by a modified Rpl22 allele (Rpl22-HA). These genetic constructs were controlled by specific promoters that selectively labeled four distinct cell types associated with axons in the peripheral nerve. Hence, the fluorescent protein (FP) will function to label the axons for the purpose of studying their regrowth potential, while the ribotag will be used for the selective isolation of ribosomes associated with the bound mRNAs. The experiments used four transgenic lines, each utilizing distinct gene promoters to target specific cell types: ChAT for motor neurons, Parvalbumin for proprioceptors, Npy2r for cutaneous mechanoreceptors, and TRPV1 for nociceptors.

The authors effectively demonstrate the selectivity of their transgenic lines towards distinct subtypes of DRG neurons. Their utilization of Ribotag, primarily designed for investigating translational activity (translator) within specific cell types, offers a unique perspective on alterations in gene expression.

The results can be categorized into two main types: firstly, a description of axon growth observed at 7 and 9 days following a sciatic nerve crush, and secondly, the RNA sequencing data obtained at 7 days post-crush, particularly concerning axon growth in specific cell types, followed by bioinformatic analysis. Finally, some in vitro experiments were conducted to explore potential causal relationships.

It seems that the most intriguing outcome of this paper revolves around the role of Med12 in nerve regeneration. The authors should prioritize this finding. Drawing a conclusion regarding Med12's role in proprioceptor regeneration based solely on this in vitro model may be insufficient. This noteworthy result requires further investigation using more animal models of nerve regeneration.

One critique revolves around the authors' examination of only a single time point within the dynamic and continuously evolving process of regeneration/reinnervation. Given that this process is characterized by dynamic changes, some of which may not be directly associated with active axon growth during regeneration, and encompasses a wide range of molecular alterations throughout reinnervation, concentrating solely on a single time point could result in the omission of critical molecular events.

Reviewer #2 (Public Review):

Summary:<br /> In this work, the authors show that dopaminergic neurons (DANs) from the DL1 cluster in Drosophila larvae are required for the formation of aversive memories. DL1 DANs complement pPAM cluster neurons which are required for the formation of attractive memories. This shows the compartmentalized network organization of how an insect learning center (the mushroom body) encodes memory by integrating olfactory stimuli with aversive or attractive teaching signals. Interestingly, the authors found that the 4 main dopaminergic DL1 neurons act redundantly, and that single-cell ablation did not result in aversive memory defects. However, ablation or silencing of a specific DL1 subset (DAN-f1,g1) resulted in reduced salt aversion learning, which was specific to salt but no other aversive teaching stimuli were tested. Importantly, activation of these DANs using an optogenetic approach was also sufficient to induce aversive learning in the presence of high salt. Together with the functional imaging of salt and fructose responses of the individual DANs and the implemented connectome analysis of sensory (and other) inputs to DL1/pPAM DANs, this represents a very comprehensive study linking the structural, functional, and behavioral role of DL1 DANs. This provides fundamental insight into the function of a simple yet efficiently organized learning center which displays highly conserved features of integrating teaching signals with other sensory cues via dopaminergic signaling.

Strengths:<br /> This is a very careful, precise, and meticulous study identifying the main larval DANs involved in aversive learning using high salt as a teaching signal. This is highly interesting because it allows us to define the cellular substrates and pathways of aversive learning down to the single-cell level in a system without much redundancy. It therefore sets the basis to conduct even more sophisticated experiments and together with the neat connectome analysis opens the possibility of unraveling different sensory processing pathways within the DL1 cluster and integration with the higher-order circuit elements (Kenyon cells and MBONs). The authors' claims are well substantiated by the data and clearly discussed in the appropriate context. The authors also implement neat pathway analyses using the larval connectome data to its full advantage, thus providing network pathways that contribute towards explaining the obtained results.

Weaknesses:<br /> While there is certainly room for further analysis in the future, the study is very complete as it stands. Suggestions for clarification are minor in nature.

Reviewer #2 (Public Review):

Summary:<br /> In this set of studies, the authors identify cFos activation in neurons in female mice that mated with males, and after experiencing male sexual behavior that is either restricted to appetitive behavior or including ejaculation. The medial preoptic nucleus was identified as an area with high cFos induction following ejaculation. Characterization of neurochemical phenotypes of cfos-expressing neurons showed a heterogenous distribution of activated neurons in the MPOA, including both inhibitory and excitatory cell types. Next, in vivo calcium imaging was used to show activation of Vgat and Vglut neurons in female mice MPOA after displaying sniffing of the male, experiencing male appetitive, or male consummatory sexual behavior, demonstrating significantly higher activation and of a greater subpopulation of Vgat neurons than Vglut neurons. Moreover, the greatest activation of Vgat neurons was detected following experiencing ejaculation, and ejaculation activated different subpopulations of MPOA cells than consummatory or appetitive sexual behaviors experienced by the female. Finally, pharmaco-genetic activation of the subpopulation of MPOA neurons that were previously activated following ejaculation resulted in a significant reduction of approach behavior by the female mice towards the male, interpreted as suppression of female sexual motivation. In conclusion, a subpopulation of inhibitory cells in the MPOA is activated in female mice after experiencing ejaculation, in turn contributing to the suppression of sexual approach behavior.

Strengths:<br /> The current set of studies replicates previous findings that ejaculation causes longer latencies to initiate interactions with a male after receiving an ejaculation in a paced mating paradigm, which is widely validated and extensively used to investigate sexual behavior in female rodents. Studies also confirm that ejaculation increases cFos expression in the MPOA while extending prior findings with a careful analysis of the neurochemical phenotype of activated neurons. A major strength of the studies is the use of cell-specific in vivo imaging and pharmaco-genetic activation to reveal a functional role of specific neuronal ensemble within the MPOA for post-ejaculatory female sexual behavior.

Weaknesses:<br /> The authors include an elegant manipulation of ejaculation-activated neurons in the MPOA using DREADD. However, this study was limited to show that activation of previously activated cells was sufficient to reduce approach behavior in a paced mating paradigm and receiving intromissions in a home cage mating paradigm. An inhibition approach using DREADD would have been a great complement to this study as it would have examined if activation of the cells was required. Moreover, additional tests for sexual motivation would have greatly strengthened the overall conclusions.

Reviewer #2 (Public Review):

Summary:<br /> The authors developed DNL343, a CNS-penetrant small molecule integrated stress response (ISR) inhibitor, to treat neurodegenerative diseases caused by ISR.

Strengths:<br /> DNL343 is an investigational CNS-penetrant small molecule integrated stress response (ISR) inhibitor designed to activate the eukaryotic initiation factor 2B (eIF2B) and suppress aberrant ISR activation. The therapeutic efficacy of DNL343 has been extensively characterized in two animal models. Importantly, plasma biomarkers of neuroinflammation and neurodegeneration can be reversed with DNL343 treatment. Remarkably, several of these biomarkers show differential levels in CSF and plasma from patients with vanishing white matter disease (VWMD) upon DNL343 treatment. Overall, this is a very exciting study to target ISR for therapeutic interventions.

Weaknesses:<br /> My main questions center around the characterization of DNL343.

1. Is there any biochemical evidence showing DNL343 activates eIF2B, such as binding assays or in vitro biochemical activity assays? A conference presentation was cited - "Osipov, M. (2022). Discovery of DNL343: a Potent Selective and Brain-penetrant eIF2B Activator Designed for the Treatment of Neurodegenerative Diseases. Medicinal Chemistry Gordon Research Conference. New London, NH." However, there needs to be public information about this presentation.

2. How was the selectivity of DNL343 demonstrated? What are the off-targets of DNL343, in particular when DNL343 is administered at a high dose? Thermal-proteasome profiling or photoaffinity labeling experiments could be considered.

3. What are the total drug concentrations in the brain and plasma? What are the unbound ratios?

4. If DNL343 is given intravenously, what are the concentrations in the brain and plasma after 5 minutes and 1 hour or longer time points? In other words, does DNL343 cross BBB through passive diffusion or an active process?

5. What is the complete PK profile of DNL343 for intravenous and oral dosing?

6. Are there any major drug metabolites that could be of concern?

Reviewer #2 (Public Review):

Summary:<br /> In their paper Rawson et al investigate the nanomechanical properties of the lambda bacteriophage packaging motor in terms of its ability to allow either the slippage of DNA out of the capsid or exerting a grip on the DNA, thereby preventing the slipping. They use a fascinatingly elegant single-molecule biophysics approach, in which gentle forces, generated and controlled by optical tweezers, are used to pull on the DNA molecule about to be packaged by the virus. A microfluidic device is then used to change the nucleotide environment of the reaction, so that the packaging motor can be investigated in its nucleotide-free (apo), ADP-, and non-hydrolyzable ATP-analog-bound states. The authors show that the apo state is dominated by DNA slippage which is impeded by friction. The slippage is stochastically halted by gripping stages. In ADP the DNA-gripped state becomes overwhelming, resulting in a much slowed DNA slippage. In non-hydrolyzable ATP analogs, the DNA slippage is essentially halted and the gripped state becomes exclusive. The authors also show that the slipping and gripping states are controlled not only by nucleotides but also by the force exerted on DNA. Altogether, DNA transport through/by the lambda-phage packaging motor is regulated by nucleotides and mechanical force. Furthermore, the authors document an intriguingly interesting DNA end-clamping mechanism that prevents the DNA from slipping entirely out of the capsid, which would make the packaging process inefficient even on the statistical level. The authors claim that their findings are likely related to the function of a small terminase subunit (TerS) in the lambda-phage motor, which may act as a sliding clamp.

Strengths:<br /> Altogether this is a very elegantly executed, thought-provoking, and interesting work with numerous significant practical implications. The paper is well-written and nicely documented.

Weaknesses:<br /> There are really no major weaknesses, apart from a few minor issues detailed below in my recommendations.

Reviewer #2 (Public Review):

Summary:<br /> This manuscript examined the underlying mechanisms between senescent osteoclasts (SnOCs) and lumbar spine instability (LSI) or aging. They first showed that greater numbers of SnOCs are observed in mouse models of LSI or aging, and these SnOCs are associated with induced sensory nerve innervation, as well as the growth of H-type vessels, in the porous endplate. Then, the deletion of senescent cells by administration of the senolytic drug Navitoclax (ABT263) results in significantly less spinal hypersensitivity, spinal degeneration, porosity of the endplate, sensory nerve innervation, and H-type vessel growth in the endplate. Finally, they also found that there is greater SnOC-mediated secretion of Netrin-1 and NGF, two well-established sensory nerve growth factors, compared to non-senescent OCs. The study is well conducted and data strongly support the idea. However, some minor issues need to be addressed.

Reviewer #2 (Public Review):

This study proposed the AG fibroblast-neutrophil-ILC3 axis as a mechanism contributing to pathological inflammation in periodontitis. In this study single-cell transcriptomic analysis was performed. But the signal mechanism behind them was not evaluated.

The authors achieved their aims, and the results partially support their conclusions.

The mouse ligatured periodontitis models differ from clinical periodontitis in human, this study supplies the basis for future research in human.

Reviewer #2 (Public Review):

Tuller et al. first made the curious observation, that the first ∼30-50 codons in most organisms are encoded by scarce tRNAs and appear to be translated slower than the rest of the coding sequences (CDS). They speculated that this has evolved to pace ribosomes on CDS and prevent ribosome collisions during elongation - the "Ramp" hypothesis. Various aspects of this hypothesis, both factual and in terms of interpreting the results, have been challenged ever since. Sejour et al. present compelling results confirming the slower translation of the first ~40 codons in S. cerevisiae but providing an alternative explanation for this phenomenon. Specifically, they show that the higher amino acid sequence divergence of N-terminal ends of proteins and accompanying lower purifying selection (perhaps the result of de novo evolution) is sufficient to explain the prevalence of rare slow codons in these regions. These results are an important contribution in understanding how aspects of the evolution of protein coding regions can affect translation efficiency on these sequences and directly challenge the "Ramp" hypothesis proposed by Tuller et al.

I believe the data is presented clearly and the results generally justify the conclusions.

Reviewer #2 (Public Review):

This manuscript by Xu et al. explores the potential joint storage/retrieval of associated signals in learning/memory and how that is encoded by some associative memory neurons using a mouse model. The authors examined mouse associative learning by pairing multimodal mouse learning including olfactory, tactile, gustatory, and pain/tail heating signals. The key finding is that after associative learning, barrel neurons respond to other multi-model stimulations. They found these barrel cortical neurons interconnect with other structures including piriform cortex, S1-Tr and gustatory cortical neurons. Further studies showed that Neuroligin 3 mediated the recruitment of associative memory neurons during paired stimulation group. The authors found that knockdown Neuroligin 3 in the barrel cortex suppressed the associative memory cell recruitment in the paired stimulation learning. Overall, this is an interesting study that reveals novel modalities associative learning involving multiple functionally connective cortical regions. Data presented are in general supporting their conclusions after revision.

Reviewer #2 (Public Review):

In this study the authors sought to understand the extent of similarity among species in intraspecific adaptation to environmental heterogeneity at the phenotypic and genetic levels. A particular focus was to evaluate if regions that were associated with adaptation within putative inversions in one species were also candidates for adaptation in another species that lacked those inversions. This study is timely for the field of evolutionary genomics, due to recent interest surrounding how inversions arise and become established in adaptation.

Major strengths-

Their study system was well suited to addressing the aims, given that the different species of sunflower all had GWAS data on the same phenotypes from common garden experiments as well as landscape genomic data, and orthologous SNPs could be identified. Organizing a dataset of this magnitude is no small feat. The authors integrate many state-of-the-art statistical methods that they have developed in previous research into a framework for correlating genomic Windows of Repeated Association (WRA, also amalgamated into Clusters of Repeated Association based on LD among windows) with Similarity In Phenotype-Environment Correlation (SIPEC). The WRA/CRA methods are very useful and the authors do an excellent job at outlining the rationale for these methods.

Weaknesses-

The authors did an excellent job responding to the first set of reviews and overall I found the manuscript more streamlined and easier to read. The main weakness in the manuscript is that correlations among environmental variables were not controlled for in their results, and is a source of potential pseudoreplication. The authors are clear about the results that are affected by pseudoreplication.

The manuscript shows how to integrate many recent methods to study the repeatability of adaptation, and the methods and data are likely to be used in similar studies.

Reviewer #2 (Public Review):

Davidsen and Sullivan present an improved method for quantifying tRNA aminoacylation levels by deep sequencing. By combining recent advances in tRNA sequencing with lysine-based chemistry that is more gentle on RNA, splint oligo-based adapter ligation, and full alignment of tRNA reads, they generate an interesting new protocol. The lab protocol is complemented by a software tool that is openly available on Github. Many of the points highlighted in this protocol are not new but have been used in recent protocols such as Behrens et al. (2021) or McGlincy and Ingolia (2017). Nevertheless, a strength of this study is that the authors carefully test different conditions to optimize their protocol using a set of well-designed controls.

The conclusions of the manuscript appear to be well supported by the data presented. However, there are a few points that need to be clarified.

1) One point that remains unsatisfactory is a better benchmarking against the state of the art. It is currently impossible to estimate how much the results of this new protocol differ from alternative methods and in particular from Behrens et al. (2021). Here it will be helpful to perform experiments with samples similar to those used in the mim-tRNAseq study and not with H1299 cells.

2) While the protocol aims to implement an improved method for quantification of tRNA aminoacylation, it can also be used for tRNA quantification and analysis of tRNA modifications. It will increase the impact of this study if the authors benchmark the outcomes of their protocol with other tRNA sequencing protocols with samples similar to these papers, which will be important for certain research teams that are unlikely to implement two different tRNA sequencing methods. Are there any possible adaptations that would allow the analysis of tRNA fragments?

3) Like Behrens et al. (2021), Davidsen and Sullivan use TGIRT-III RT for their analyses. The enzyme is not currently available in a form suitable for tRNA-seq. It would be very helpful to test different new RT enzymes that are commercially available. The example of Maxima RT - Figure 2 Supp 6 - shows significantly lower performance than the presented TGIRT-III RT data. In lines 296-298, the authors mention improvements to the protocol by using ornithine. Why are these improvements not included?

4) A technical concern: The samples are purified multiple times using a specific RNA purification kit. Did the authors test different methods to purify the RNA and does this influence the result of the method?

5) The study would benefit from an explicit step-by-step protocol, including the choice of adapters that are shown to work best in the protocol.

Reviewer #2 (Public Review):

Summary:<br /> This study provided a neural network emulator of the human ventricular cardiomyocyte action potential. The inputs are the corresponding maximum conductances and the output is the action potential (AP). It used the forward and inverse problems to evaluate the model. The forward problem was solved for synthetic data, while the inverse problem was solved for both synthetic and experimental data. The NN emulator tool enables the acceleration of simulations, maintains high accuracy in modeling APs, effectively handles experimental data, and enhances the overall efficiency of pharmacological studies. This, in turn, has the potential to advance drug development and safety assessment in the field of cardiac electrophysiology.

Strengths:<br /> (1) Low computational cost: The NN emulator demonstrated a massive speed-up of more than 10,000 times compared to the simulator. This substantial increase in computational speed has the potential to expedite research and drug development processes

(2) High accuracy in the forward problem: The NN emulator exhibited high accuracy in solving the forward problem when tested with synthetic data. It accurately predicted normal APs and, to a large extent, abnormal APs with early afterdepolarizations (EADs). High accuracy is a notable advantage over existing emulation methods, as it ensures reliable modeling and prediction of AP behavior

Weaknesses:<br /> (1) Input space constraints: The emulator relies on maximum conductances as inputs, which explain a significant portion of the AP variability between cardiomyocytes. Expanding the input space to include channel kinetics parameters might be challenging when solving the inverse problem with only AP data available.

(2) Simplified drug-target interaction: In reality, drug interactions can be time-, voltage-, and channel state-dependent, requiring more complex models with multiple parameters compared to the oversimplified model that represents the drug-target interactions by scaling the maximum conductance at control. The complex model could also pose challenges when solving the inverse problem using only AP data.

(3) Limited data variety: The inverse problem was solved using AP data obtained from a single stimulation protocol, potentially limiting the accuracy of parameter estimates. Including AP data from various stimulation protocols and incorporating pacing cycle length as an additional input could improve parameter identifiability and the accuracy of predictions.

(4) Larger inaccuracies in the inverse problem using experimental data: The reasons for this result are not quite clear. Hypotheses suggest that it may be attributed to the low parameter identifiability or the training data set were collected in small tissue preparation.

Reviewer #2 (Public Review):

Bhanja et al have examined how actin polymerization switch B-cell receptor (BCR) signaling from amplification to attenuation. The authors have examined B cell spreading and contraction using lipid bilayers to assess the molecular regulation of BCR signalling during the contraction phase. Their data provide evidence for that N-WASP activated Arp2/3 generates centripetally moving actin foci and contractile actomyosin from lamellipodia actin networks. This generates BCR dense foci that pushes out both stimulatory kinases and inhibitory phosphatases. The study provides novel insight into how B cells upon activation attenuate BCR signalling by contraction of the actin cytoskeleton and clustering of BCR foci and this dynamic response is mediated by N-WASP and Arp2/3.

Strengths: The manuscript is well written and results, methods, figures and legends described in detail making it easy to follow the experimental setup, analysis, and conclusions. The authors achieved their aims, and the results support their conclusions.

Weaknesses: Minor. The working hypothesis of molecular crowding as a way to push out signalling molecules from the BCR dense foci is interesting. The authors provide evidence for that this is an active process mediated by N-WASP - Arp2/3 induced actin foci. Another possibility discussed in the revised version is that BCR dense foci formation is an indirect consequence of lamellipodia retraction. Future works should define the specific role of N-WASP, Arp2/3 and actin in the process to form BCR dense foci, especially as the BCR continue to signal in the cytoplasm.

Reviewer #2 (Public Review):

Summary:

Tissue-resident macrophages are more and more thought to exert key homeostatic functions and contribute to physiological responses. In the report of O'Brien and Colleagues, the idea that the macrophage-expressed scavenger receptor MARCO could regulate adrenal corticosteroid output at steady-state was explored. The authors found that male MARCO-deficient mice exhibited higher plasma aldosterone levels and higher lung ACE expression as compared to wild-type mice, while the availability of cholesterol and the machinery required to produce aldosterone in the adrenal gland were not affected by MARCO deficiency. The authors take these data to conclude that MARCO in alveolar macrophages can negatively regulate ACE expression and aldosterone production at steady-state and that MARCO-deficient mice suffer from secondary hyperaldosteronism.

Strengths:

If properly demonstrated and validated, the fact that tissue-resident macrophages can exert physiological functions and influence endocrine systems would be highly significant and could be amenable to novel therapies.

Weaknesses:

The data provided by the authors currently do not support the major claim of the authors that alveolar macrophages, via MARCO, are involved in the regulation of a hormonal output in vivo at steady-state. At this point, there are two interesting but descriptive observations in male, but not female, MARCO-deficient animals, and overall, the study lacks key controls and validation experiments, as detailed below.

Major weaknesses:

1) According to the reviewer's own experience, the comparison between C57BL/6J wild-type mice and knock-out mice for which precise information about the genetic background and the history of breedings and crossings is lacking, can lead to misinterpretations of the results obtained. Hence, MARCO-deficient mice should be compared with true littermate controls.

2) The use of mice globally deficient for MARCO combined with the fact that alveolar macrophages produce high levels of MARCO is not sufficient to prove that the phenotype observed is linked to alveolar macrophage-expressed MARCO (see below for suggestions of experiments).

3) If the hypothesis of the authors is correct, then additional read-outs could be performed to reinforce their claims: levels of Angiotensin I would be lower in MARCO-deficient mice, levels of Antiotensin II would be higher in MARCO-deficient mice, Arterial blood pressure would be higher in MARCO-deficient mice, natremia would be higher in MARCO-deficient mice, while kaliemia would be lower in MARCO-deficient mice. In addition, co-culture experiments between MARCO-sufficient or deficient alveolar macrophages and lung endothelial cells, combined with the assessment of ACE expression, would allow the authors to evaluate whether the AM-expressed MARCO can directly regulate ACE expression.

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 #2 (Public Review):

The authors introduce "HAMA", a new automated pipeline for architectural analysis of the bacterial cell wall. Using MS/MS fragmentation and a computational pipeline, they validate the approach using well-characterized model organisms and then apply the platform to elucidate the PG architecture of several members of the human gut microbiota. They discover differences in the length of peptide crossbridges between two species of the genus Bifidobacterium and then show that these species also differ in cell envelope stiffness, resulting in the conclusion that PG "compactness" determines stiffness.

The pipeline is solid and revealing the poorly characterized PG architecture of the human gut microbiota is worthwhile and significant. However, it is unclear if or how their pipeline is superior to other existing techniques - PG architecture analysis is routinely done by many other labs; the only difference here seems to be that the authors chose gut microbes to interrogate.

I do not agree with their conclusions about the correlation between compactness and cell envelope stiffness. These experiments are done on two different species of bacteria and their experimental setup therefore does not allow them to isolate crossbridge length (which they propose indicates more or less compact PG) as the only differential property that can influence stiffness. These two species likely also differ in other ways that could modulate stiffness, e.g. turgor pressure, overall PG architecture (not just crossbridge length), membrane properties, teichoic acid composition etc.

Reviewer #2 (Public Review):

Unconventional secretion refers to the release of cargoes without a signal peptide and is performed independent of ER-Golgi trafficking. One essential type of unconventional secretion is type I, in which a cargo can translocate directly across the plasma membrane. FGF2 is one excellent mode to study type I translocation and the authors have focused on FGF2 secretion for decades. Many beautiful works have been performed to reveal the mechanism of FGF2 translocation step by step. And the picture is getting clearer which time a new work from the lab is published. In the current work, the authors characterized the importance of disulfate bond formation on C95 of FGF2 in lipid binding and translocation. In addition, they clearified the role of another C77 which is require for binding to the Na/K -ATPase that regulates the early step of FGF2 binding to the membrane. The authors also employed structural approaches and MD to provide mechanistic insights into the translocation process. In general it is an important advance regarding the translocation of FGF2 and data provided are brief, clear and convincing.

Reviewer #2 (Public Review):

The authors have done a number of additional experiments and textual changes to address referee comments from the first round of review that have improved some aspects of the manuscript. However, they did not fully address two major issues brought up in my previous public review, reiterated below.

1) What is the specific role for HSP90a/b in regulating protein translation during chronic stress through the ISR or related pathways? The authors indicate that the induction of the eIF2a phosphatase GADD34 is not impacted in HSP90-deficient cells, so what role does HSP90 have in this process. Is HSP90 required for proper folding of GADD34? Would you see similar effects in protein translation recovery if other ISR activators are used in HSP90-deficient cells?

2) Are similar effects observed in non-dividing cells?' Does chronic stress lead to increases of size and regulation of protein translation in primary cell models that are not undergoing division.

This leaves the study as an interesting observational study that correlates increases in cell size and protein translation. However, it doesn't really answer some of the most important questions related to mechanisms defining this correlation. Regardless, this remains an interesting jumping off point to continue exploring this interesting finding correlating cell size and stress signaling that will be further pursued in subsequent manuscripts, which will likely continue to reveal the importance and mechanistic basis of this 'rewiring stress response' during stress and in disease.

Reviewer #2 (Public Review):

An important paper that confirms the validity of the initial findings of Chretien et al regarding the hot temperatures at which the mitochondrion is operating. The authors responded adequately to the reviewers' concerns.

Reviewer #2 (Public Review):

Summary:<br /> The manuscript titled 'Proteolytic cleavage and inactivation of the TRMT1 tRNA modification enzyme by SARS-CoV-2 main protease' from K. Zhang et al. demonstrates that several RNA modifications are downregulated during SARS-CoV-2 infection including the widespread m2,2G methylation, which potentially contributes to changes in host translation. To understand the molecular basis behind this global hypomodification of RNA during infection, the authors focused on the human methyltransferase TRMT1 that catalyzes the m2,2G modification. They reveal that TRMT1 not only interacts with the main SARS-CoV-2 protease (Nsp5) in human cells but is also cleaved by Nsp5. To establish if TRMT1 cleavage by Nsp5 contributes to the reduction in m2,2G levels, the authors show compelling evidence that the TRMT1 fragments are incapable of methylating the RNA substrates due to loss of RNA binding by the catalytic domain. They further determine that expression of full-length TRMT1 is required for optimal SARS-CoV-2 replication in 293T cells. Nevertheless, the cleavage of TRMT1 was dispensable for SARS-CoV-2 replication hinting at the possibility that TRMT1 could be an off-target or fortuitous substrate of Nsp5. Overall, this study will be of interest to virologists and biologists studying the role of RNA modification and RNA modifying enzymes in viral infection.

Strengths:<br /> • The authors use a state-of-the-art mass spectrometry approach to quantify RNA modifications in human cells infected with SARS-CoV-2.<br /> • The authors go to great length to demonstrate that SARS-CoV-2 main protease, Nsp5, interacts, and cleaves TRMT1 in cells and perform important controls when needed. They use a series of overexpression with strategically placed tags on both TRMT1 and Nsp5 to strengthen their observations.<br /> • The use of an inactive Nsp5 mutant (C145A) strongly supports the claim of the authors that Nsp5 is solely responsible for TRMT1 cleavage in cells.<br /> • Although the direct cleavage was not experimentally determined, the authors convincingly show that TRMT1 Q530N is not cleaved by Nsp5 suggesting that the predicted cleavage site at this position is most likely the bona fide region processed by Nsp5 in cells.<br /> • To understand the impact of TRMT1 cleavage on its RNA methylation activity, the authors rigorously test four protein constructs for their capacity not only to bind RNA but also to introduce the m2,2G modification. They demonstrate that the fragments resulting from TRMT1 cleavage are inactive and cannot methylate RNA. They further establish that the C-terminal region of TRMT1 (containing a zinc-finger domain) is the main binding site for RNA.<br /> • While 293T cells are unlikely an ideal model system to study SARS-CoV-2 infection, the authors use two cell lines and well-designed rescue experiments to uncover that TRMT1 is required for optimal SARS-CoV-2 replication.

Weaknesses:<br /> • Immunoblotting is extensively used to probe for TRMT1 degradation by Nsp5 in this study. Regretfully, the polyclonal antibody used by the authors shows strong non-specific binding to other epitopes. This complicates the data interpretation and quantification since the cleaved TRMT1 band migrates very closely to a main non-specific band detected by the antibody (for instance Fig 3A). While this reviewer is concerned about the cross-contamination during quantification of the N-TRMT1, the loss of this faint cleaved band with the TRMT1 Q530N mutant is reassuring. Nevertheless, the poor behavior of this antibody for TRMT1 detection was already reported and the authors should have taken better precautions or designed a different strategy to circumvent the limitation of this antibody by relying on additional tags.

• While 293T cells are convenient to use, it is not a well-suited model system to study SARS-CoV-2 infection and replication. Therefore, some of the conclusions from this study might not apply to better-suited cell systems such as Vero E6 cells or might not be observed in patient-infected cells.

• The reduction of bulk TRMT1 levels is minor during infection of MRC5 cells with SARS-CoV-2 (Fig 1). This does not seem to agree with the more dramatic reduction in m2,2G modification levels. Cellular Localization experiments of TRMT1 would help clarify this. While TRMT1 is found in the cytoplasm and nucleus, it is possible that TRMT1 is more dramatically degraded in the cytoplasm due to easier access by Nsp5.

• In Fig 6, the authors show that TRMT1 is required for optimal SARS-CoV-2 replication. This can be rescued by expressing TRMT1 (Fig 7). Nevertheless, it is unknown if the methylation activity of TRMT1 is required. The authors could have expressed an inactive TRMT1 mutant (by disrupting the SAM binding site) to establish if the RNA modification by TRMT1 is important for SARS-CoV-2 replication or if it is the protein backbone that might contribute to other processes.

• Fig 7, the authors used the Q530N variant to rescue SARS-CoV-2 replication in TRMT1 KO cells. This is an important experiment and unexpectedly reveals that TRMT1 cleavage by Nsp5 is not required for viral replication. To strengthen the claim of the authors that TRMT1 is required to promote viral replication and that its cleavage inhibits RNA methylation, the authors could express the TRMT1 N-terminal construct in the TRMT1 KO cells to assess if viral replication is restored or not to similar levels as WT TRMT1. This will further validate the potential biological importance of TRMT1 cleavage by Nsp5.

• Fig 7 shows that the TRMT1 Q530N variant rescues SARS-CoV-2 replication to greater levels then WT TRMT1. The authors should discuss this in greater detail and its possible implications with their proposed statement. For instance, are m2,2G levels higher in Q530N compared to WT? Does Q530N co-elute with Nsp5 or is the interaction disrupted in cells?

Reviewer #2 (Public Review):

Summary:<br /> The manuscript focuses on the comparison of two PLP-dependent enzyme classes that perform amino acyl decarboxylations. The goal of the work is to understand the substrate specificity and factors that influence the catalytic rate in an enzyme linked to theanine production in tea plants.

Strengths:<br /> The work includes x-ray crystal structures of modest resolution of the enzymes of interest. These structures provide the basis for the design of mutagenesis experiments to test hypotheses about substrate specificity and the factors that control catalytic rate. These ideas are tested via mutagenesis and activity assays, in some cases both in vitro and in plants.

Weaknesses:<br /> The manuscript could be more clear in explaining the contents of the x-ray structures and how the complexes studied relate to the reactant and product complexes. The structure and mechanism section would also be strengthened by including a diagram of the reaction mechanism and including context about reactivity. As it stands, much of the structural results section consists of lists of amino acids interacting with certain ligands without any explanation of why these interactions are important or the role they play in catalysis. The experiments testing the function of a novel Zn(II)-binding domain also have serious flaws. I don't think anything can be said at this point about the function of the Zn(II) due to a lack of key controls and problems with experimental design.