Reviewer #2 (Public Review):

Summary:

The authors report the discovery of a population of gingival fibroblasts displaying the expression of cellular senescence markers P21 and P16 in human periodontitis samples and a murine ligature-induced periodontitis (LIP) model. They support this finding in the murine model through bulk RNA-sequencing and show that differentially expressed genes are significantly enriched in the SenMayo cellular senescence in an aging dataset. They then show that Ligature-Induced Periodontitis (LIP) mice treated with the senomorphic drug metformin display overall diminished bone damage, reduced histomorphic alterations, and a reduction in P21 and P16 immunostaining signal. To explore the cell types expressing cellular senescence markers in periodontitis, the authors make use of a combination of bioinformatic analyses on publicly available scRNA-seq data, immunostainings on patient samples and their LIP model; as well as in vitro culture of healthy human gingival fibroblasts treated with LPS. They found that fibroblasts are a cell population expressing P16 in periodontitis which are also enriched for SenMayo genes, suggesting they have a senescent phenotype. They then point to a subgroup of fibroblasts expressing CD81+ with the highest enrichment for a SASP geneset in periodontitis. They also show that treatment of LIP mice and human LPS-treated gingival fibroblasts with metformin leads to a reduction of P21 and P16-positive cells, as well as the senescence-associated beta-galactosidase (SA-beta-gal) marker. Finally, they show evidence suggesting that CD81+ senescent fibroblasts are the source of C3 complement protein, which they stipulate signals through the C3AR1 receptor present in neutrophils in periodontitis. The authors observed that both CD81+ fibroblast and C3AR1+ neutrophil populations are expanded in periodontitis, that both populations appear to be in close contact, and that treatment with metformin reduced both C3 and the neutrophil marker MPO in their mouse LIP model.

Strengths:

The study implements several different techniques and tools on human samples, mouse models, fibroblast cultures, and publicly available data to support their conclusions. In summary, the evidence suggests that in the context of periodontitis, there is an expansion of cells expressing senescence markers P21, and P16, as well as members of the SASP, and that this includes CD81+ fibroblasts.

Weaknesses:

The manuscript appears to use as synonyms the terms "senescent cells" and "aging cells", as well as "senescence" and "aging", or "accelerated senescence" and "accelerated aging". This choice of words makes it difficult to understand the objectives of the study and the interpretations the authors are deriving from their results. The current understanding of the role of cellular senescence is that it is only one of the multiple biological aspects that characterize physiological aging. Although deeply intertwined, aging and cellular senescence are widely considered distinct phenomena, but the difference between these concepts seems blurry to me within the manuscript.

After reading the manuscript, my understanding is that the authors are comparing the process of periodontitis to a form of accelerated aging, in which senescent cells are potential drivers or contributors. I believe this to be an interesting point of view. As the authors mention, periodontitis is more common in the elderly, and senescence is strongly implicated in aging. However, I am not entirely sure if the authors were trying to address such a question, and more importantly, the experiments conducted here cannot address the relationships between cellular senescence in periodontitis and aging as (1) they do not conduct an expanded analysis of molecular and cellular features of aging in the oral epithelium beyond cellular senescence, (2) they do not test this hypothesis in vitro and in vivo using models of accelerated or delayed aging (or publicly available datasets of such models), and (3) interpretations regarding the aging process are hindered by the fact that all human healthy patients were young adults, while all human periodontitis patients were middle-aged, while the mouse model did not include different age groups.

The authors also refer to metformin as an "anti-aging" drug. Therefore, to me, it is not clear if the authors intended to use metformin as a senotherapeutic agent to show a correlation between senescence markers and the severity of periodontitis, or if they conceived their experiments and interpreted their results as "delaying the aging process". The latter would be more difficult to determine as cellular senescence is only one of the several aspects of the aging process in tissues. As none of the other molecular and cellular hallmarks that characterize the process of aging (epigenetic alterations, telomere shortening, immunosenescence, mitochondrial dysfunction, stem cell depletion, genomic instability, loss of proteostasis, nutrient sensing disruption, etc.) were studied, I believe this might be just a matter of semantics and rephrasing.

On the other hand, and assuming the authors were only seeking to explore the role of cellular senescence in periodontitis (irrespective of the aging process), I have the following concerns:

Major concerns:

(1) A majority of the bioinformatic analyses regarding cellular senescence were conducted using only the SenMayo geneset reported by Dominik Saul et al. That geneset was developed by literature searching for genes associated with cellular senescence that had been studied in the context of human aging (in bone marrow). Thus, my understanding is that it is not an "aging" gene set as the authors describe it (and possibly interpret it) throughout the manuscript but a gene set of cellular senescence-associated genes that are overrepresented in aging tissues.

The SenMayo geneset specifically excludes important genes like P21, P16, and RELA as they were used for validating that dataset against other datasets. Additionally, most of the genes that comprise SenMayo are cytokines and growth factors. This includes part of the SASP (and the authors also show enrichment for some SASP factors using the Coppé dataset in Figure 5) but excludes many of the core important processes that are known to define cellular senescence, including cell cycle inhibition, lack of cell proliferation, accumulation of DNA damage, activation of the lysosomal compartment and disruption of the nuclear envelope, among others. As the SenMayo geneset was developed for studying senescence in the context of aging, I believe it is important to conduct a more extensive analysis with other published gene sets of cellular senescence. Examples include the cellular senescence and SASP REACTOME pathways, the KEGG cellular senescence pathway, the cellular senescence GO term, the Fridman dataset, SeneQuest, CSGene, CellAge, etc. Most importantly, it will be important to show the enrichment of pathways related to hallmark pathways underlying cellular senescence such as cell cycle inhibition, the DNA damage response and repair pathways, NF-kB signaling, MTOR, and autophagy signaling, etc. Showing the enrichment level of these pathways in the CD81+ fibroblasts in periodontitis would be of utmost importance for backing up the conclusions of this study.

(2) The most important aspect of the definition of cellular senescence is the absence of cell proliferation. Beyond the expression of the p21, p16, and SASP markers, any evidence showing that CD81+ fibroblasts are not proliferating in vivo in humans and mice, and in vitro in the case of LPS experiments, would be of great importance for defining these cells as senescent. Otherwise, conclusions should be toned down to refer to the expression of senescence markers or cells having a "senescent-like" phenotype.

(3) The use of a "relative optic density" metric instead of positive cell counts as a measure for quantifying IHC stainings might pose challenges in reproducing these results, especially for the P21 and P16 stainings which are proteins that despite being possibly also being found in the cytoplasm, should be clearly present in the nucleus of positive cells. The quantification of the levels of these markers is of great importance for the conclusions of this study but I am concerned they would be too difficult to reproduce. In my opinion, cell counts and % of positive cells should be used, with a clear description of the total number of cells counted in the methodology. Otherwise, a strong justification for using OD in the methodology is required in addition to considering the following comments:

a. There is no description in the methodology describing how this relative OD is measured and calculated. It is not clear if the data points shown in the graphs are biological replicates or OD means measured in different histological sections from the same sample.

b. The images of P16 and P21 stainings in Figures 2E and 2F do not appear to resemble the differences in OD between conditions shown in the graphs of Figures 2Gd and 2Ge.

c. The stainings shown for p16 in Figure 2E seem considerably different from those shown in Figure 1D. Additionally, the relative OD of P16 at 14D is around 0.08 in Figure 1D, while the mean for the control appears to be around 0.015 at 14D in Figure 2Gd. The use of OD as a measure is again worrying as this could be impacting interpretations: the difference between the ODs of LIP+MET (around 0.08) and LIP+ddH2O (around 0.015) is reported as significant but the difference in OD between LIP14D in Figure 1D (around 0.07) and LIP+ddH2o in Figure 2Gd (around 0.015) should not be significant as they are supposed to similar control conditions.

d. Irrespective of the measure used, the authors should state exact means and standard deviations, as well as exact P values, the statistical test used, and the number of biological replicates per group in parenthesis in the main text and figure legend.

(4) The conclusions derived from experiments with metformin in mice and cell cultures are not fully supported by the evidence.

First, metformin has multiple molecular targets, as well as multiple organ and tissue targets. The experiments presented in mice do not consider/evaluate the systemic effects of metformin nor local effects in other gingival cell types and this should be discussed.

As mentioned before, these experiments cannot be interpreted as testing metformin in the context of "anti-aging", as this study addresses cellular senescence in periodontitis. However, the results are still relevant as there is considerable evidence showing that metformin has senomorphic activity. In this regard, the authors could make use of a compound that has been more extensively characterized as a senolytic such as ABT-737, ABT-263 (Navitoclax), or the combination of Dasatinib + Quercetin, to show the effect of eliminating senescent cells in their LPS induction fibroblast model.

They could also show the effect of metformin on the activation of other hallmark senescence pathways such as (the NF-kB pathway or the DNA damage response) and in the expression of SASP factors they identified as overexpressed in CD81+ fibroblasts through their analysis against the SenMayo dataset (e.g., IL6, CXCL1, CXCL12). This could be done in their samples from metformin-treated mouse experiments and in their LPS induction fibroblast model.

(5) For the data produced on the authors' human samples, the difference in the age of patient groups is a significant confounding factor. This is because all their periodontitis patient samples came from middle-aged individuals (mean age above 50 years), while all healthy samples were obtained from young adults (mean age 25 years). The authors should justify this selection of age groups and justify why differences in the age of each experimental group could impact the validity of their results regarding the accumulation of senescent cells. Showing the level of P21 and P16 positive cell accumulation in samples from healthy patients from a similar age group (middle-aged) is of great importance to support the validity of their results in humans.

Reviewer #2 (Public Review):

The authors frame the MS-spectrum-based prediction of antimicrobial resistance prediction as a drug recommendation task. Weis et al introduced the dataset this model is tested on and benchmark models which take as input a single species and are trained to predict resistance to a single drug. Instead here, a pair of drug and spectrum are fed to 2 neural network models to predict a resistance probability. In this manner, knowledge from different drugs and species can be shared through the model parameters. Three questions are asked: 1. what is the best way to encode the drugs? 2. does the dual NN outperform the single-spectrum drug?

Overall the paper is well-written and structured. It presents a novel framework for a relevant problem. The work would benefit from more work on evaluation.

Reviewer #2 (Public Review):

Summary:

In the paper, the authors use a cellular Potts model to investigate muscle regeneration. The model is an attempt to combine many contributors to muscle regeneration into one coherent framework. I believe the resulting model has the potential to be very useful in investigating the complex interplay of multiple actors contributing to muscle regeneration.

Strengths:

The manuscript identified relevant model parameters from a long list of biological studies. This collation of a large amount of literature into one framework has the potential to be very useful to other authors. The mathematical methods used for parameterization and validation are transparent.

Comments on revised version:

The authors have satisfactorily addressed my previous comments.

Reviewer #2 (Public Review):

The manuscript by Chen et al from the group of Helen Miranda aims to describe an improved neuromuscular junction (NMJ) model to study synaptic dysfunction in several cases of familial ALS. Overall, the system described in the paper appears as a valid platform to study disease phenotypes with exciting results showing specific effects of GDNF on non-SOD1 ALS patient lines. The strength of the paper lies in the use of myotubes, and motor neurons derived from the same donor. However, the current study: (1) lacks a clear comparison of the current system with numerous previously described systems; (2) is limited by the number of repeat experiments in the study and (3) has no description of the synaptic phenotype observed in the study. These major points are discussed in more detail below.

Major points:

(1) In the introduction the authors state (p. 4): "Finally, recent human NMJ models have been established from PSCs by differentiating these cells into both skeletal muscles and motor neurons in 2D and 3D formats. These previous systems present a remarkable advancement to the studies of human NMJs, however, they require long NMJ formation and maturation time (40 to 60 days), which, restricts their sensitivity and scalability [42]"

In fact, a number of studies have described various in-vitro NMJ systems, with the same timeframes for NMJ formation. For example, in studies by Osaki et al, 2018, Sci Adv; Bellmann et al, 2019, Biomat; Demestre et al, 2015, Stem Cell Res; Badu-Mensah et al, 2022, Biomat (this is just an exemplar selection of the papers); NMJ formation was observed as early as 14 d in culture, in line with or at least slightly longer than reported by Chen et al. With the exception of the study by Osaki et al, all co-culture systems cited above are 2D-based. The authors need to expand on this further or provide a quantitative assessment of why their system is better compared to previously published models.

(2) Further, when comparing their results with other work it is hard to claim how the current system is (p. 5) "more reproducible, and offers a 6-fold increase in scalability compared to previous models [40-43]". The authors need to expand on this further.

(3) Although mentioned, there were no examples of the modularity of the system, which of course would strengthen the paper and help to uncover ALS mechanisms of synaptic formation, for example by combining WT myotubes and fALS motor neurons (see point 4 below). The authors should show how they would adapt to 96 well plate format to showcase the scalability of the system. Based on their data on the efficacy of synaptic formation (60 per 0.7 cm2 area), is further miniaturization allowed?

(4) A lot of a-bungarotoxin staining corresponds to AChR clusters that do not seem to be associated with muscle and do not form normal rings of clustering (pretzel-like) associated with the NMJ in vivo. This is seen clearly in Figure 3B and Figure 5B. Figures 3B and 5B only show low-magnification images which makes it difficult to assess the specificity of localization of the pre-/post-synaptic markers. The authors should clearly show the morphologies of the NMJs formed in WT and fALS lines at high magnification. In addition, the authors should show co-localization images for a-bungarotoxin and myosin-heavy chains to confirm the localization of the bungarotoxin signal on the myotubes.

In addition to that, the authors report that the number of functional synapses formed on a plate varies from 30 (fASL) to 60 (Ctrl) per 10,000 neurons spread over the 0.7 cm2 area (0.6%). How do the authors explain an extensive loss of a-bungarotoxin signal in Figure 5B the majority of which likely corresponds to AChR clusters that are formed outside of neuronal connections? Such clustering can be usually observed in immature co-cultures and in vivo prior to the innervation of myotubes. One explanation could be that myotubes derived from fALS PSC are less capable of synaptic formation. Noteworthy, a study of PSC-derived myotubes and motor neurons from PSC lines with various SOD1 mutations has already been published, but not cited by Chen et al (Badu-Mensah et al). Given the importance of those confounding factors, the authors should test cell-intrinsic (motor neuron-related) vs non-cell-intrinsic mechanisms by co-culturing healthy myotubes with fALS-derived motor neurons followed by NMJ quantification.

(5) The authors present the advantage of optogenetic stimulation, but they only show the proof-of-principle and never really apply it to their studies. Specifically, with regard to Figure 6, are motor units derived from fALS PSCs incapable of being ontogenetically activated to the same extent as control motor units? Does the dysfunction stem from fALS motor neurons or fALS myotubes?

(6) Figures 6 B and C appear to be identical except for the addition of the GDNF effect on the fALS lines. This should all be put in one figure. The authors should also show whether GDNF-induced functional recovery is associated with recovery in the number of motor units or with merely synaptic function by quantifying the NMJ number in the presence of GDNF.

(7) Figure 5 and Figure 6. The authors only use one line per fALS mutation and their corresponding isogenic controls. They state that the n=6 for these experiments represents the technical replication of the experiment. These experiments should be performed at least n=3 times starting from neuronal differentiation, and not by seeding replicate wells representing a true replication of each experiment. This would significantly strengthen their argument that their method is robust and the results are easily reproducible.

(8) In the discussion the authors may want to mention that the lack of function of GDNF on the SOD1 lines may relate to the fact that SOD1 mutations do not lead to TDP43 pathology. Although speculative this suggests that in cases with TDP43 mutations (their data) or sporadic disease GDNF may be effective.

(9) Although beyond the scope of this paper, it would of course be interesting to see if sporadic forms of ALS had this same phenotype.

Reviewer #2 (Public Review):

Summary:

In this contribution, the authors investigate the degree of alternative splicing across the evolutionary tree and identify a trend of increasing alternative splicing as you move from the base of the tree (here, only prokaryotes are considered) towards the tips of the tree. In particular, the authors investigate how the degree of alternative splicing (roughly speaking, the number of different proteins made from a single ORF (open reading frame) via alternative splicing) relates to three genomic variables: the genome size, the gene content (meaning the fraction of the genome composed of ORFs), and finally, the coding percentage of ORFs, meaning the ratio between exons and total DNA in the ORF. When correlating the degree of alternative splicing with these three variables, they find that the different taxonomic groups have a different correlation coefficient, and identify a "progressive pattern" among metazoan groups, namely that the correlation coefficient mostly increases when moving from flowering plants to arthropods, fish, birds, and finally mammals. They conclude that therefore the amount of splicing that is performed by an organismal group could be used as a measure of its complexity.

Weaknesses:

While I find the analysis of alternative splicing interesting, I also find that it is a very imperfect measure of organismal complexity and that the manuscript as a whole is filled with unsupported statements. First, I think it is clear to anyone studying evolution over the tree of life that it is the complexity of gene regulation that is at the origin of much of organismal structural and behavioral complexity. Arguably, creating different isoforms out of a single ORF is just one example of complex gene regulation. However, the complexity of gene regulation is barely mentioned by the authors. Further, it is clear that none of their correlation coefficients actually show a simple trend (see Table 3). According to these coefficients, birds are more complex than mammals for 3 out of 4 measures. It is also not clear why the correlation coefficient between alternative splicing ratio and genome length, gene content, and coding percentage should display such a trend, rather than the absolute value. There are only vague mechanistic arguments.

Much more troubling, however, is the statement that the data supports "lineage-specific trends" (lines 299-300). Either this is just an ambiguous formulation, or the authors claim that you can see trends *within* lineages. The latter is clearly not the case. In fact, within each lineage, there is a tremendous amount of variation, to such an extent that many of the coefficients given in Table 3 are close to meaningless. Note that no error bars or p-values are presented for the values shown in Table 3. Figure 2 shows the actual correlation, and the coefficient for flowering plants there is given as 0.151, with a p-value of 0.193. Table 3 seems to quote r=0.174 instead. It should be clear that a correlation within a lineage or species is not a sign of a trend.

There are several wrong or unsupported statements in the manuscript. Early on, the authors state that the alternative splicing ratio (a number greater or equal to one that can be roughly understood as the number of different isoforms per ORF) "quantifies the number of different isoforms that can be transcribed using the same amount of information" (lines 51-52). But in many cases, this is incorrect, because the same sequence can represent different amounts of information depending on the context. So, if a changed context gives rise to a different alternative splice, it is because the genetic sequence has a different meaning in the changed context: the information has changed. In line 149, the authors state that "the energetic cost of having large genomes is high". No citation is given, and while such a statement seems logical, it does not have very solid support. If there was indeed a strong selective force to reduce genome size, we would not see the stunning diversity of genome sizes even within lineages. This statement is repeated (without support) several times in the manuscript, apparently in support of the idea that mammals had "no choice" to increase complexity via alternative splicing because they can't increase it by having longer genomes. I don't think this reasoning can be supported. Even more problematic is the statement that "the amount of protein-coding DNA seems to be limited to a size of about 10MB" (line 219). There is no evidence whatsoever for this statement. The reference that is cited (Choi et al 2020) suggests that there is a maximum of 150GB in total genome size due to physiological constraints. In lines 257-258, the authors write that "plants are less restricted in terms of storing DNA sequences compared to animals" (without providing evidence or a citation). I believe this statement is made due to the observation that plants tend to have large intergenic regions. But without examining the functionality of these interagency regions (they might host long non-coding RNA stretches that are used to regulate the expression of other genes, for example) it is quite adventurous to use such a simple measure as being evidence that plants "are less restricted in terms of storing DNA sequences", whatever that even means. I do not think the authors mean that plants have better access to -80 freezers. The authors conclude that "plant's primary mechanism of genome evolution is by expanding their genome". This statement itself is empty: we know that plants are prone to whole genome duplication, but this duplication is not, as far as we understand, contributing to complexity. It is not a "primary mechanism of genome evolution". In lines 293-294, the authors claim that "alternative splicing is maximized in mammalian genomes". There is no evidence that this ratio cannot be increased. So, to conclude (on lines 302-303) that alternative splicing ratios are "a potential candidate to quantify organismal complexity" seems, based on this evidence, both far-fetched and weak at the same time.

I am also not very comfortable with the data analysis. The authors, for example, say that they have eliminated from their analysis a number of "outlier species". They mention one: Emmer wheat because it has a genome size of 900 Mb (line 367). Since 900MB does not appear to be extreme, perhaps the authors meant to write 900 Gb. When I consulted the paper that sequenced Triticum dicoccoides, they noted that 14 chromosomes are about 10GB. Even a tetraploid species would then not be near 900Gb. But more importantly, such a study needs to state precisely which species were left out, and what the criteria are for leaving out data, lest they be accused of selecting data to fit their hypothesis.

I understand that Methods are often put at the end of a manuscript, but the measures discussed here are so fundamental to the analysis that a brief description of what the different measures are (in particular, the "alternative splicing ratio") should be in the main text, even when the mathematical definition can remain in the Methods.

Finally, a few words on presentation. I understand that the following comments might read differently after the authors change their presentation. This manuscript was at the border of being comprehensible. In many cases, I could discern the meaning of words and sentences in contexts but sometimes even that failed (as an example above, about "species-specific trends", illustrates). The authors introduced jargon that does not have any meaning in the English language, and they do this over and over again.

Note that I completely agree with all the comments by the other reviewer, who alerted me to problems I did not catch, including the possible correlation with effective population size: a possible non-adaptive explanation for the results.

Reviewer #2 (Public Review):

Summary:

In this manuscript, the authors provide a method aiming to accurately reflect the individual deviation of longitudinal/temporal change compared to the normal temporal change characterized based on pre-trained population normative model (i.e., a Bayesian linear regression normative model), which was built based on cross-sectional data. This manuscript aims to solve a recently identified problem of using normative models based on cross-sectional data to make inferences about longitudinal change.

Although the proposed method was implemented with real data and shown to be more sensitive in capturing the differences confirmed by previous studies than conventional methods, there is still a lack of simulation studies to formally evaluate the performance of the proposed method in making accurate estimations and inferences about the longitudinal changes.

Strengths:

The efforts of this work make a good contribution to addressing an important question of normative modeling. With the greater availability of cross-sectional studies for normative modeling than longitudinal studies, and the inappropriateness of making inferences about longitudinal subject-specific changes using these cross-sectional data-based normative models, it's meaningful to try to address this gap from the perspective of methodological development.

Weaknesses:

• The organization and clarity of this manuscript need enhancement for better comprehension and flow. For example, in the first few paragraphs of the introduction, the wording is quite vague. A lot of information was scattered and repeated in the latter part of the introduction, and the actual challenges/motivation of this work were not introduced until the 5th paragraph.

• There are no simulation studies to evaluate whether the adjustment of the cross-sectional normative model to longitudinal data can make accurate estimations and inferences regarding the longitudinal changes. Also, there are some assumptions involved in the modeling procedure, for example, the deviation of a healthy control from the population over time is purely caused by noise and constant variability of error/noise across x_n, and these seem to be quite strong assumptions. The presentation of this work's method development would be strengthened if the authors can conduct a formal simulation study to evaluate the method's performance when such assumptions are violated, and, ideally, propose some methods to check these assumptions before performing the analyses.

• The proposed "z-diff score" still falls in the common form of z-score to describe the individual deviation from the population/reference level, but now is just specifically used to quantify the deviation of individual temporal change from the population level. The authors need to further highlight the difference between the "z-score" and "z-diff score", ideally at its first mention, in case readers get confused (I was confused at first until I reached the latter part of the manuscript). The z-score can also be called a measure of "standardized difference" which kind of collides with what "z-diff" implies by its name.

• Explaining that one component of the variance is related to the estimation of the model and the other is due to prediction would be helpful for non-statistical readers.

• It would be easier for the non-statistical reader if the authors consistently used precision or variance for all variance parameters. Probably variance would be more accessible.

• The functions psi were never explicitly described. This would be helpful to have in the supplement with a reference to that in the paper.

• What is the goal of equations (13) and (14)? The authors should clarify what the point of writing these equations is prior to showing the math. It seems like it is to obtain an estimate of \sigma_{\ksi}^2, which the reader only learns at the end.

• What is the definition of "adaption" as used to describe equation (15)? In this equation, I think norm on subsample was not defined.

• "(the sandwich part with A)" - maybe call this an inner product so that it is not confused with a sandwich variance estimator. This is a bit unclear. Equation (8) does have the inner product involving A and \beta^{-1} does include variability of \eta. It seems like you mean that equation (8) incorrectly includes variability of \eta and does not have the right term vector component of the inner product involving A, but this needs clarifying.

• One challenge with the z-diff score is that it does not account for whether a person sits above or below zero at the first time point. It might make it difficult to interpret the results, as the results for a particular pathology could change depending on what stage of the lifespan a person is in. I am not sure how the authors would address those challenges.

Reviewer #2 (Public Review):

HIV infection is characterized by viral integration into permissive host cells - an event that occurs very early in viral-host encounter. This constitutes the HIV proviral reservoir and is a feature of HIV infection that provides the greatest challenge for eradicating HIV-1 infection once an individual is infected.

This study looks at how starting HIV treatment very early after infection, which substantially reduces the peak viral load detectable (compared to untreated infection), affects the amount and characteristics of the viral reservoir. The authors studied 35 women in South Africa who were at high risk of getting HIV. Some of these women started HIV treatment very soon after getting infected, while others started later. This study is well-designed and has as its focus a very well-characterized cohort. Comparison groups are appropriately selected to address reservoir characterization and dynamics in the context of acute and chronic treated HIV-1. The amount of HIV and various characteristics of the genetic makeup of the virus (intact/defective proviral reservoir) were evaluated over one year of treatment. Methods employed for reservoir characterization are state-of-the-art and provide in-depth insights into the reservoir in peripheral blood.

While starting treatment early didn't reduce the amount of HIV DNA at the outset, it did lead to a gradual decrease in total HIV DNA quantity over time. In contrast, those who started treatment later didn't see much change in this parameter. Starting treatment early led to a faster decrease in intact provirus (a measure of replication-competence), compared to starting treatment later. Additionally, early treatment reduced the genetic diversity of the viral DNA and resulted in fewer immune escape variants within intact genomes. This suggests that collectively having a smaller intact replication-competent reservoir, less viral variability, and less opportunity for the virus to evade the immune system - are all features that are likely to facilitate more effective clearance of viral reservoir, especially when combined with other intervention strategies.

Major strengths of the study include the cohort of very early treated persons with HIV and the depth of study. These are important findings, particularly as the study was conducted in HIV-1 subtype C infected women (more cure studies have focussed on men and with subtype B infection)- and in populations most affected by HIV and in need of HIV cure interventions. This is highly relevant because it cannot be assumed that any interventions employed for reducing/clearing the HIV reservoir would perform similarly in men and women or across different populations. Other factors also deserve consideration and include age, and environment (e.g. other comorbidities and coinfections).

Reviewer #3 (Public Review):

Summary:

Bartolome et al. present ProteasomeID, a novel method to identify components, interactors, and (potentially) substrates of the proteasome in cell lines and mouse models. As a major protein degradation machine that is highly conserved across eukaryotes, the proteasome has historically been assumed to be relatively homogeneous across biological scales (with few notable exceptions, e.g., immunoproteasomes and thymoproteasomes). However, a growing body of evidence suggests that there is some degree of heterogeneity in the composition of proteasomes across cell tissues, and can be highly dynamic in response to physiologic and pathologic stimuli. This work provides a methodological framework for investigating such sources of variation. The authors start by adapting the increasingly popular biotin ligation strategy for labelling proteins coming into close proximity with one of three different subunits of the proteasome, before proceeding with PSMA4 for further development and analysis based on their preliminary labelling data. In a series of well-constructed and convincing validation experiments, the authors go on to show that the tagged PSMA4 construct can be incorporated into functional proteasomes, and is able to label a broad set of known proteasome components and interacting proteins in HEK293T cells. They also attempt to identify novel proteasomal degradation substrates with ProteasomeID; while this was convincing for known substrates with particularly short half-lives, the results for substrates with longer half-lives were less clear. One of the most compelling results was from a similar experiment to confirm proteasomal degradation induced by a BRD-targeting PROTAC, which I think is likely to be of keen interest to the targeted degradation community. Finally, the authors establish a ProteasomeID mouse model, and demonstrate its utility across several tissues.

Strengths:

(1) ProteasomeID itself is an important step forward for researchers with an interest in protein turnover across biological scales (e.g., in sub-cellular compartments, in cells, in tissues, and whole organisms). I especially see interest from two communities: those studying fundamental proteostasis in physiological and pathologic processes (e.g., ageing; tissue-specific protein aggregation diseases), and those developing targeted protein degradation modalities (e.g., PROTACs; molecular glues). All the datasets generated and deposited here are likely to provide a rich resource to both. The HEK293T cell line data are a valuable proof-of-concept to allow expansion into more biologically-relevant cell culture settings; however, I envision the greatest innovation here to be the mouse model. For example, in the targeted protein degradation space, two major hurdles in early-stage pre-clinical development are (i) evaluation of degradation efficacy across disease-relevant tissues, and (ii) toxicity and safety implications caused by off-target degradation, e.g., of newly-identified molecular glues and/or in particularly-sensitive tissues. The ProteasomeID mouse allows early in vivo assessment of both these questions. The results of the BRD PROTAC experiment in 293T cells provides an excellent in vitro proof-of-concept for this approach.

(2) The mass-spectrometry-based proteomics workflows used and presented throughout the manuscript are robust, rigorous, and convincing. For example, the algorithm the authors use for defining enrichment score cut-offs are logical and based on rational models, rather than on arbitrary cut-offs that are common for similar proteomics studies. The construction (and subsequent validation) of both BirA*- and miniTurbo- tagged PSMA4 variants also increases the utility of the method, allowing researchers to choose the variant with the labelling time-scale required for their particular research question.

(3) The optimised BioID and TurboID protocol the authors develop (summarised in Fig. S2A) and validate (Fig. S2B-D) is likely to be of broad interest to cell and molecular biologists beyond the protein degradation field, given that proximity labelling is a current gold-standard in global protein:protein interaction profiling.

Limitations:

I think the authors do an excellent job in highlighting the limitations of ProteasomeID throughout the Results and Discussion. I do have some specific comments that might provide additional context for the reader.

(1) The authors do a good job in showing that a substantial proportion of PSMA4-BirA* is incorporated into functional proteasome particles; however, it is not immediately clear to me how much background (false-positive IDs) might be contributed by the ~40 % of PSMA4-BirA* that is not incorporated into the mature core particle (based on the BirA* SEC-MS traces in Fig. 2b and S3b, i.e., the large peak ~ fraction 20). Are there any bands lower down in the native gel shown in Fig. 2c, i.e., corresponding to lower molecular weight complexes or monomeric PSMA4-BirA*? The enrichment of proteasome assembly factors in all the ProteasomeID experiments might suggest the presence of assembly intermediates, which might themselves become substrates for proteasomal degradation (as has been shown for other incompletely-assembled protein complexes, e.g., the ribosome, TRiC/CCT).

(2) Although the authors attempt to show that BirA* tagging of PSMA4 does not interfere with proteasome activity (Fig. 2e-f), I think the experimental evidence for this is incomplete. They show that the overall chymotrypsin-like activity (attributable to PSMB5) in cells expressing PSMA4-BirA* is not markedly reduced compared with control BirA*-expressing cells. However, they do not show that the activity of the specific proteasome sub-population that contains PSMA4-BirA* is unaffected (e.g., by purifying this sub-population via the Flag tag). The proteasome activity of the sub-population of wild-type proteasome complexes that do not contain the PSMA4-BirA* (~50%, based on the earlier immunoblots) could account for the entire chymotrypsin-like activity-especially in the context of HEK293T cells, where steady-state proteasome levels are unlikely to be limiting. It would also be useful to assess any changes in tryspin- and caspase- like activities, especially as tagging of PSMA4 could conceivably interfere with the activity of some PSMB subunits, but not others.

(3) I was left slightly unsure as to the general utility of ProteasomeID for identifying novel proteasomal substrates in homeostatic conditions--especially for proteins with longer half-lives. The cycloheximide chases in Fig. 4g/S4j are clear for MYC and TIGD5 (which have short half-lives), but are not so clear for ARMC6 and BRAT1: the reduction in the bands are modest, and might have been clearer with longer "chase" time-points. Furthermore, classifying candidates based on enrichment following proteasome inhibition with MG-132 have the potential to lead to a high number of false positives. ProteasomeID's utility in identifying potential substrates in more targeted settings (e.g., molecular glues, off-target PROTAC substrates) is far more apparent.

Reviewer #2 (Public Review):

Summary:

In this paper, the authors wanted to show that capsaicin can disrupt the interaction between Keap1 and Nrf2 by directly binding to Keap1 at an allosteric site. The resulting stabilization of Nrf2 would protect CAP-treated gastric cells from alcohol-induced redox stress and damage as well as inflammation (both in vitro and in vivo).

Strengths:

One major strength of the study is the use of multiple methods (CoIP, SPR, BLI, deuterium exchange MS, CETSA, MS simulations, target gene expression) that consistently show for the first time that capsaicin can disrupt the Nrf2/Keap1 interaction at an allosteric site and lead to stabilization and nuclear translocation of Nrf2.

Weaknesses:

One major weakness of the study is that plausibility is taken as proof for causality. The finding that capsaicin directly binds to Keap1 and releases Nrf2 from its fate of degradation (in vitro) is taken for granted as the sole explanation for the observed improved gastric health upon alcohol exposure (in vivo). There is no consideration or exclusion of any potential unrelated off-target effect of capsaicin, or proteins other than Nrf2 that are also controlled by Keap1.

Another point that hampers full appreciation of the capsaicin effect in cells is that capsaicin is not investigated alone, but mostly in combination with alcohol only.

Bottom Line:

Overall, the authors are convincing that capsaicin (although weakly) binds to Keap1 and releases Nrf2 from degradation. With this, the authors provide a significant finding with marked relevance for the redox/Nrf2 as well as natural products /hit discovery communities. Moreover, the employed toolbox of different complementary methodologies can set the bar for future PPI inhibitor studies. The translation of this novel finding in a biological setting (alcohol-stressed gastric cells) still leaves some open questions and concerns. These concerns mainly arise from lacking control experiments and/or somewhat biased conclusions from the obtained data sets.

Reviewer #2 (Public Review):

Summary:

The paper addresses several factors that influence daily changes in concentration of metabolites in the Drosophila melanogaster gut. The authors describe metabolomes extracted from fly guts at four time-points during a 24-hour period, comparing profiles of primary metabolites, lipids, and biogenic amines. The study elucidates that the percentage of metabolites that exhibit a circadian cycle, peak phases of their increased appearance, and the cycling amplitude depends on the combination of factors (microbiome status, composition or timing of the diet, circadian clock genotype). Multiple general conclusions based on the data obtained with modern metabolomics techniques are provided in each part of the article. Descriptive analysis of the data supports the finding that microbiome increases the number of metabolites for which concentration oscillates during the day period. Results of the experiments show that timed feeding significantly enhanced metabolite cycling and changed its phase regardless of the presence of a microbiome. The authors suggest that the host circadian rhythm modifies both metabolite cycling period and the number of such metabolites.

Strengths:

The obvious strength of the study is the data on circadian cycling of the detected 843, 4510, and 4330 total primary metabolites, lipids, and biogenic amines respectively in iso31 flies and 623, 2245, and 2791 respective metabolites in per01 mutants. The comparison of the abundance of these metabolites, their cycling phase, and the ratio of cycling/non-cycling metabolites is well described and illustrated. The conditions tested represent significant experimental interest for contemporary chronobiology: with/without microbiota, wild-type/mutant period gene, ad libitum/time-restricted feeding, and high-sugar/high-protein diet. The authors conclude that the complex interaction between these factors exists, and some metabolic implications of combinations of these factors can be perceived as reminiscent of metabolic implications of another combination ("...the microbiome and time-restricted feeding paradigms can compensate for each other, suggesting that different strategies can be leveraged to serve organismal health"). Enrichment analysis of cycling metabolites leads to an interesting suggestion that oscillation of metabolites related to amino acids is promoted by the absence of microbiota, alteration of circadian clock, and time-restricted feeding. In contrast, association with microbiota induces oscillation of alpha-linolenic acid-related metabolites. These results provide the initial step for hypothesising about functional explanations of the uncovered observations.

Weaknesses:

Among the weaknesses of the study, one might point out too generalist interpretations of the results, which propose hypothetical conclusions without their mechanistic proof. The quantitative indices analysed are obviously of particular interest, however are not self-explaining and exhaustive. More specific biological examples would add valuable insights into the results of this study, making conclusions clearer. More specific comments on the weaknesses are listed below:

(1) The criterion of the percentage of cycling metabolites used for comparisons has its own limitations. It is not clear, whether the cycling metabolites are the same in the guts with/without microbiota, or whether there are totally different groups of metabolites that cycle in each condition. GO enrichment analysis gives only a partial assessment, but is still not quantitative enough.

(2) The period of cycling data is based on only 4 time points during 24 hours in 4 replicates (>200 guts per replicate) on the fifth day of the experiment (10-12-day-old adults). It does not convincingly prove that these metabolites cycle the following days or more finely within the day. Moreover, it is not clear how peaks in polar histogram plots were detected in between the timepoints of ZT0, ZT6, ZT12, and ZT18.

(3) Average expression and amplitude are analysed for groups of many metabolites, whereas the data on distinct metabolites is hidden behind these general comparisons. This kind of loss of information can be misleading, making interpretation of the mentioned parameters quite complicated for authors and their readers. Probably more particular datasets can be extracted to be discussed more thoroughly, rather than those general descriptions.

(4) The metabolites' preservation is crucial for this type of analysis, and both proper sampling plus normalisation require more attention. More details about measures taken to avoid different degradation rates, different sizes of intestines, and different amounts of microbes inside them will be beneficial for data interpretation.

(5) The data in the article describes formal phenomena, not directly connected with organism physiology. The parameters discussed obviously depend on the behaviour of flies. Food consumption, sleep, and locomotor activity could be additionally taken into account.

(6) Division of metabolites into three classes limits functional discussion of found differences. Since the enrichment analysis provided insights into groups of metabolites of particular interest (for example, amino acid metabolism), a comparison of their cycling characteristics can be shown separately and discussed.

Reviewer #2 (Public Review):

Summary:

In this manuscript, Wang and co-workets employ single molecule light microscopy (SMLM) to detect Nipah virus Fusion protein (NiV-F) in the surface of cells. They corroborate that these glycoproteins form microclusters (previously seen and characterized together with the NiV-G and Nipah Matrix protein by Liu and co-workers (2018) also with super-resolution light microscopy). Also seen by Liu and coworkers the authors show that the level of expression of NiV-F does not alter the identity of these microclusters nor endosomal cleavage. Moreover, mutations and the transmembrane domain or the hexamer-of-trimer interface seem to have a mild effect on the size of the clusters that the authors quantified. Importantly, it has also been shown that these particles tend to cluster in Nipah VLPs.

Strengths:

The authors have tried to perform SMLM in single VLPs and have shown partially the importance of NiV-F clustering.

Weaknesses:

The labelling strategy for the NiV-F is not sufficiently explained. The use of a FLAG tag in the extracellular domain should be validated and compared with the unlabelled WT NiV-F when expressed in functional pseudoviruses (for example HIV-1 based particles decorated with NiV-F). This experiment should also be carried out for both infection and fusion (including BlaM-Vpr as a readout for fusion). I would also suggest to run a time-of-addition BlaM experiment to understand how this particular labelling strategy affects single virion fusion as compared to the the WT. It would also be very important to compare the FLAG labelling approach with recent advances in the field (for instance incorporating noncanonical amino acids (ncAAs) into NiV-F by amber stop-codon suppression, followed by click chemistry).

The correlation between the existence of microclusters of a particular size and their functionality is missing. Only cell-cell fusion assays are shown in supplementary figures and clearly, single virus entry and fusion cannot be compared with the biophysics of cell-cell fusion. Not only the environment is completely different, membrane curvature and the number of NiV-F drastically varies also. Therefore, specific fusion assays (either single virus tracking and/or time-of-addition BlaM kinetics with functional pseudoviruses) are needed to substantiate this claim.

The authors also claim they could not characterize the number of NiV-F particles per cluster. Another technique such as number and brightness (Digman et al., 2008) could support current SMLM data and identify the number of single molecules per cluster. Also, this technology does not require complex microscopy apparatus. I suggest they perform either confocal fluorescence fluctuation spectroscopy or TIRF-based nandb to validate the clusters and identify how many molecule are present in these clusters. Also, it is not clear how many cells the authors employ for their statistics (at least 30-50 cells should be employed and not consider the number of events blinking events). I hope the authors are not considering only a single cell to run their stats... The differences between the mutants and the NiV-F is minor even if their statistical analyses give a difference (they should average the number and size of the clusters per cell for a total of 30-50 cells with experiments performed at least in three different cells following the same protocol). They should also compare the level of expression (with the number of molecules per cell provided by number and brightness) with the total number of clusters. Overall, it seems that the authors have only evaluated a very low number of cells.

The same applies to the VLP assay. I assume the authors have only taken VLPs expressing both NiV-M and NiV-F (and NiV-G). But even if this is not clearly stated I would urge the authors to show how many viruses were compared per condition (normally I would expect 300 particles per condition coming from three independent experiments). As a negative control to evaluate the cluster effect I would mix the different conditions. Clearly you have clusters with all conditions and the differences in clustering depending on each condition are minimal. Therefore you need to increase the n for all experiments.

Reviewer #2 (Public Review):

Summary:

In their manuscript, Zhao et al. describe a link between JAK-STAT pathway activation in nephrocytes on a high-fat diet. Nephrocytes are the homologs to mammalian podocytes and it has been previously shown, that metabolic syndrome and obesity are associated with worse outcomes for chronic kidney disease. A study from 2021 (Lubojemska et al.) could already confirm a severe nephrocyte phenotype upon feeding Drosophila a high-fat diet and also linking lipid overflow by expressing adipose triglyceride lipase in the fat body to nephrocyte dysfunction. In this study, the authors identified a second pathway and mechanism, how lipid dysregulation impact on nephrocyte function. In detail, they show activation of JAK-STAT signaling in nephrocytes upon feeding them a high-fat diet, which was induced by Upd2 expression (a leptin-like hormone) in the fat body, and the adipose tissue in Drosophila. Further, they could show genetic and pharmacological interventions can reduce JAK-STAT activation and thereby prevent the nephrocyte phenotype in the high-fat diet model.

Strengths:

The strength of this study is the combination of genetic tools and pharmacological intervention to confirm a mechanistic link between the fat body/adipose tissue and nephrocytes. Inter-organ communication is crucial in the development of several diseases, but the underlying mechanisms are only poorly understood. Using Drosophila, it is possible to investigate several players of one pathway, here JAK-STAT. This was done, by investigating the functional role of Hop, Socs36E, and Stat92E in nephrocytes and has also been combined with feeding a high-fat diet, to assess restoration of nephrocyte function by inhibiting JAK-STAT signaling. Adding a translational approach was done by inhibiting JAK-STAT signaling with methotrexate, which also resulted in attenuated nephrocyte dysfunction. Expression of the leptin-like hormone upd2 in the fat body is a good approach to studying inter-organ communication and the impact of other organs/tissue on nephrocyte function and expands their findings from nephrocyte function towards whole animal physiology.

Weaknesses:

Although the general findings of this study are of great interest, there are some weaknesses in the study, which should be addressed. Overall, the number of flies investigated for the majority of the experiments is very low (6 flies) and it is not clear whether the flies used, are from independent experiments to exclude problems with food/diet. For the analysis, the mean values of flies should be calculated, as one fly can be considered a biological replicate, but not all individual cells. By increasing the number of flies investigated, statistical analysis will become more solid. In addition, the morphological assessment is rather preliminary, by only using a Pyd antibody. Duf or Sns should be visualized as well, also the investigation of the different transgenic fly strains studying the importance of JAK-STAT signaling in nephrocytes needs to include a morphological assessment. Moreover, the expected effect of feeding a high-fat diet on nephrocytes needs to be shown (e.g. by lipid droplet formation) and whether upd2 is actually increased here should also be assessed. The time points of assessment vary between 1, 3, and 7 days and should be consistent throughout the study or the authors should describe why they use different time points.

Reviewer #2 (Public Review):

This work deals with a very difficult physical problem: relating the assembly of building blocks on a molecular scale to the appearance of large, macroscopic assemblies. This problem is particularly difficult to treat, because of the large number of units involved, and of the complex way in which these units-monomers-interact with each other and with the solvent. In order to make the problem treatable, the authors recur to a number of approximations: Among these, there is the assumption that the system is spatially homogeneous, i.e., its features are the same in all regions of space. In particular, the homogeneity assumption may not hold in biologically relevant systems such as cells, where the behavior close to the cell membrane may strongly differ from the one in the bulk. As a result, this hypothesis calls for a cautious consideration and interpretation of the results of this work. Another notable simplification introduced by the authors is the assumption that the system can only follow two possible behaviors: In the first, each monomer interacts equally with the solvent; no matter the size of the cluster of which it is part. In the second case, monomers in the bulk of a cluster and monomers at the assembly boundary interact with the solvent in a different way. These two cases are considered not only because they simplify the problem, but also because they are inspired by biologically relevant proteins.

With these simplifications, the authors trace the phase diagram of the system, characterizing its phases for different fractions of the volume occupied by the monomers and solvent, and for different values of the temperature. The results qualitatively reproduce some features observed in recent experiments, such as an anomalous distribution of cluster sizes below the system saturation threshold, and the gelation of condensed phases above such threshold.

Reviewer #2 (Public Review):

This concise and focused study by Lowry and colleagues identifies a motif in the pores of three families of channel/scramblase proteins that regulate exclusive ion permeation and lipid transport. These three ion channel families, which include the TMEM16s, the plant-expressed and stress-gated cation channel OSCA, and the mammalian homolog and mechanosensitive cation channel, TMEM63 share low sequence similarity between them and have seemingly differing functions, as anion (TMEM16s), or stress-activated cation channels (OSCA/TMEM63). The study finds that in all three families, mutating a single hydrophobic residue in the ion permeation pathway of the channels confers lipid transport through the pores of the channels, indicating that TMEM16 and the related OSCA and TMEM63 channels have a conserved potential for both ion and lipid permeation. The authors interpret the findings as revealing that these channel/scramblase proteins have a relatively low "energetic barrier for scramblase" activity. The experiments themselves seem to be done with a high level of rigor and the paper is well written. A weakness is the limited scope of the experiments which, if fixed, could open up a new line of inquiry.

Reviewer #2 (Public Review):

Summary:

The study by Link et al. advances our understanding of the actomyosin system in T. brucei, focusing on the role of TbMyo1, a class I myosin, within the parasite's endosomal system. Using a combination of biochemical fractionation, in vitro motility assays, and advanced imaging techniques such as correlative light and electron microscopy (CLEM), this paper demonstrates that TbMyo1 is dynamically distributed across early and late endosomes, the cytosol, is associated with the cytoskeleton, and a fraction has an unexpected association with glycosomes. Notably, the study shows that TbMyo1 can translocate actin filaments at velocities suggesting an active role in intracellular trafficking, potentially higher than those observed for similar myosins in other cell types. This work not only elucidates the spatial dynamics of TbMyo1 within T. brucei but also suggests its broader involvement in maintaining the complex architecture of the endosomal network, underscoring the critical role of the actomyosin system in a parasite that relies on high rates of endocytosis for immune evasion.

Strengths:

A key strength of the study is its exceptional rigor and successful integration of a wide array of sophisticated techniques, such as in vitro motility assays, and advanced imaging methods, including correlative light and electron microscopy (CLEM) and immuno-electron microscopy. This combination of approaches underscores the study's comprehensive approach to examining the ultrastructural organization of the trypanosome endomembrane system. The application of functional data using inhibitors, such as latrunculin A for actin depolymerization, further strengthens the study by providing insights into the dynamics and regulatory mechanisms of the endomembrane system. This demonstrates how the actomyosin system contributes to cellular morphology and trafficking processes. Furthermore, the discovery of TbMyo1 localization to glycosomes introduces a novel aspect to the potential roles of myosin I proteins within the cell, particularly in the context of organelles analogous to peroxisomes. This observation not only broadens our understanding of myosin I functionality but also opens up new avenues for research into the cellular biology of trypanosomatids, marking a significant contribution to the field.

Weaknesses:

Certain limitations inherent in the study's design and scope render the narrative incomplete and make it challenging to reach definitive conclusions. One significant limitation is the reliance on spatial association data, such as colocalization of TbMyo1 with various cellular components-or the absence thereof-to infer functional relationships. Although these data suggest potential interactions, the authors do not confirm functional or direct physical interactions.

While TbMyo1's localization is informative, the authors do not directly demonstrate its biochemical or mechanical activities in vivo, leaving its precise role in cellular processes speculative. Direct assays that manipulate TbMyo1 levels, activity, and/or function, coupled with observations of the outcomes on cellular processes, would provide more definitive evidence of the protein's specific roles in T. brucei. A multifaceted approach, including genetic manipulations, uptake assays, kinetic trafficking experiments, and imaging, would offer a more robust framework for understanding TbMyo1's roles. This comprehensive approach would elucidate not just the "what" and "where" of TbMyo1's function but also the "how" and "why," thereby deepening our mechanistic insights into T. brucei's biology.

Reviewer #2 (Public Review):

Summary:

There is significant interest in characterizing the mechanisms by which genetic mutations linked to autoimmunity perturb immune processes. Pahl et al. collect information on dynamic accessible regions, genes, and 3D contacts in primary CD4+ T cell samples that have been stimulated ex vivo. The study includes a variety of analyses characterizing these dynamic changes. With TF footprinting they propose factors linked to active regulatory elements. They compare the performance of their variant mapping pipeline that uses their data versus existing datasets. Most compelling there was a deep dive into additional study of regulatory elements nearby the IL2 gene. Finally, they perform a pharmacological screen targeting several genes they suggest are involved in T cell proliferation.

Strengths:

The work done characterizing elements at the IL2 locus is impressive.

Weaknesses:

- Missing critical context to evaluate claims. There are extensive studies performed on resting and activated immune cell states (CD4+ T cells and other cell types) and some at multiple time points or concentrations of stimuli that collect ATAC-seq and/or RNA-seq that have been ignored by this study. How do conclusions from previous studies compare to what the authors conclude here? It is impossible to evaluate the claims without this additional context. These are a few studies I am familiar with (the authors should perform a more comprehensive search to be sure they're not ignoring existing observations) that would be important to compare/contrast conclusions:<br /> o Alasoo, K. et al. Shared genetic effects on chromatin and gene expression indicate a role for enhancer priming in immune response. Nat. Genet. 50, 424-431 (2018).<br /> o Calderon, D., Nguyen, M.L.T., Mezger, A. et al. Landscape of stimulation-responsive chromatin across diverse human immune cells. Nat Genet 51, 1494-1505 (2019).<br /> o Gate, R.E., Cheng, C.S., Aiden, A.P. et al. Genetic determinants of co-accessible chromatin regions in activated T cells across humans. Nat Genet 50, 1140-1150 (2018).<br /> o Glinos, D.A., Soskic, B., Williams, C. et al. Genomic profiling of T-cell activation suggests increased sensitivity of memory T cells to CD28 costimulation. Genes Immun 21, 390-408 (2020).<br /> o Gutierrez-Arcelus, M., Baglaenko, Y., Arora, J. et al. Allele-specific expression changes dynamically during T cell activation in HLA and other autoimmune loci. Nat Genet 52, 247-253 (2020).<br /> o Kim-Hellmuth, S. et al. Genetic regulatory effects modified by immune activation contribute to autoimmune disease associations. Nat. Commun. 8, 266 (2017).<br /> o Ye, C. J. et al. Intersection of population variation and autoimmunity genetics in human T cell activation. Science 345, 1254665 (2014).

- As a general point, I appreciate it when each claim includes a corresponding effect size and p-value, which helps me evaluate the strength of significance of supporting evidence.

Reviewer #2 (Public Review):

Summary:

This study by Sun et al. identifies a novel role for IBTK in promoting cancer protein translation, through regulation of the translational helicase eIF4A1. Using a multifaceted approach, the authors demonstrate that IBTK interacts with and ubiquitinates eIF4A1 in a non-degradative manner, enhancing its activation downstream of mTORC1/S6K1 signaling. This represents a significant advance in elucidating the complex layers of dysregulated translational control in cancer.

Strengths:

A major strength of this work is the convincing biochemical evidence for a direct regulatory relationship between IBTK and eIF4A1. The authors utilize affinity purification and proximity labeling methods to comprehensively map the IBTK interactome, identifying eIF4A1 as a top hit. Importantly, they validate this interaction and the specificity for eIF4A1 over other eIF4 isoforms by co-immunoprecipitation in multiple cell lines. Building on this, they demonstrate that IBTK catalyzes non-degradative ubiquitination of eIF4A1 both in cells and in vitro through the E3 ligase activity of the CRL3-IBTK complex. Mapping IBTK phosphorylation sites and showing mTORC1/S6K1-dependent regulation provides mechanistic insight. The reduction in global translation and eIF4A1-dependent oncoproteins upon IBTK loss, along with clinical data linking IBTK to poor prognosis, support the functional importance. Finally, the impact of IBTK on eIF4A1 target gene expression in colon and lung cancer cell lines, strengthens these findings.

Weaknesses:

While the effects of IBTK knockout/over-expression on bulk protein synthesis are shown, the expression of several eIF4A1 target oncogenes remains unchanged.

Summary:

Overall, this study significantly advances our understanding of how aberrant mTORC1/S6K1 signaling promotes cancer pathogenic translation via IBTK and eIF4A1. The proteomic, biochemical and phosphorylation mapping approaches established here provide a blueprint for interrogating IBTK function. These data should galvanize future efforts to target the mTORC1/S6K1-IBTK-eIF4A1 axis as an avenue for cancer therapy, particularly in combination with eIF4A inhibitors.

Reviewer #2 (Public Review):

Summary:

The authors aimed to identify which regions of DVL2 contribute to its endogenous/basal clustering, as well as the relevance of such domains to condensate/phase separation and WNT activation.

Strengths:

A strength of the study is the focus on endogenous DVL2 to set up the research questions, as well as the incorporation of various techniques to tackle it. I found also quite interesting that DVL2-CFR addition to DVL1 increased its MW in density gradients.

Weaknesses:

I think that several of the approaches of the manuscript are subpar to achieve the goals and/or support several of the conclusions. For example:

(1) Although endogenous DVL2 indeed seems to form complexes (Figure 1A), neither the number of proteins involved nor whether those are homo-complexes can be determined with a density gradient. Super-resolution imaging or structural analyses are needed to support these claims.

(2) Follow-up analyses of the relevance of the DVL2 domains solely rely on overexpressed proteins. However, there were previous questions arising from o/e studies that prompted the focus on endogenous, physiologically relevant DVL interactions, clustering, and condensate formation. Although the title, conclusions, and relevance all point to the importance of this study for understanding endogenous complexes, only Figures 1A and B deal with endogenous DVL2.

(3) Mutants lacking activity/complex formation, e.g. DVL2_1-418, may need further validation. For instance, DVL2_1-506 (same mutant but with DEP) seems to form condensates and it is functional in WNT signalling (King et al., 20223). These differences could be caused by the lack of DEP domain in this particular construct and/or folding differences.

(4) The key mutants, DeltaCFR and VV/FF only show mild phenotypes. The authors' results suggest that these regions contribute but are not necessary for 1) complex formation (Density gradient Figures 7A and B), condensate formation (Figures 7C and D), and WNT activity (Figure 7E). Of note Figure 7C shows examples for the mutants with no condensates while the qualification indicates that 50% of the cells do have condensates.

(5) Most of the o/e analyses (including all reporter assays) should be performed in DVL1-3 KO cells in order to explore specifically the behaviour of the investigated mutants.

(6) How comparable are condensates found in the cytoplasm (usually for wt DVL) with those located in the nucleus (DEP mutants)?

Several studies in the last two decades have analysed the relevance of DVL homo - and hetero-clustering by relying on overexpressed proteins. Recent studies also explored the possibility of DVL undergoing liquid-liquid phase separation following similar principles. As highlighted by the authors in the introduction, there is a need to understand DVL dynamics under endogenous/physiological conditions. Recent super-resolution studies aimed at that question by characterising endogenously edited DVL2. The authors seemed to aim in the same direction with their initial findings (Figure 1A) but quickly moved to o/e proteins without going back to the initial question. This reviewer thinks that to support their conclusions and advance in this important question, the authors should introduce the relevant mutations in the endogenous locus (e.g. by Cas9+ donor template encoding the required 3' exons, as done by others before for WNT components, including DVL2) and determine their impact in the above-indicated processes.

Reviewer #2 (Public Review):

This manuscript uses biochemistry and X-ray crystallography to further probe the molecular mechanism of Parkin regulation and activation. Using a construct that incorporates cleavage sites between different Parkin domains to increase the local concentration of specific domains (i.e., molecular scissors), the authors suggest that competitive binding between the p-Ubl and RING2 domains for the RING0 domain regulates Parkin activity. Further, they demonstrate that this competition can occur in trans, with a p-Ubl domain of one Parkin molecule binding the RING0 domain of a second monomer, thus activating the catalytic RING1 domain. In addition, they suggest that the ACT domain can similarly bind and activate Parkin in trans, albeit at a lower efficiency than that observed for p-Ubl. The authors also suggest from crystal structure analysis and some biochemical experiments that the linker region between RING2 and repressor elements interacts with the donor ubiquitin to enhance Parkin activity.

Ultimately this manuscript challenges previous work suggesting that the p-Ubl domain does not bind to the Parkin core in the mechanism of Parkin activation. The use of the 'molecular scissors' approach to probe these effects is an interesting approach to probe this type of competitive binding. However, there are issues with the experimental approach manuscript that detract from the overall quality and potential impact of the work.

The competitive binding between p-Ubl and RING2 domains for the Parkin core could have been better defined using biophysical and biochemical approaches that explicitly define the relative affinities that dictate these interactions. A better understanding of these affinities could provide more insight into the relative bindings of these domains, especially as it relates to the in trans interactions.

I also have concerns about the results of using molecular scissors to 'increase local concentrations' and allow for binding to be observed. These experiments are done primarily using proteolytic cleavage of different domains followed by size exclusion chromatography. ITC experiments suggest that the binding constants for these interactions are in the µM range, although these experiments are problematic as the authors indicate in the text that protein precipitation was observed during these experiments. This type of binding could easily be measured in other assays. My issue relates to the ability of a protein complex (comprising the core and cleaved domains) with a Kd of 1 µM to be maintained in an SEC experiment. The off-rates for these complexes must be exceeding slow, which doesn't really correspond to the low µM binding constants discussed in the text. How do the authors explain this? What is driving the Koff to levels sufficiently slow to prevent dissociation by SEC? Considering that the authors are challenging previous work describing the lack of binding between the p-Ubl domain and the core, these issues should be better resolved in this current manuscript. Further, it's important to have a more detailed understanding of relative affinities when considering the functional implications of this competition in the context of full-length Parkin. Similar comments could be made about the ACT experiments described in the text.

Ultimately, this work does suggest additional insights into the mechanism of Parkin activation that could contribute to the field. There is a lot of information included in this manuscript, giving it breadth, albeit at the cost of depth for the study of specific interactions. Further, I felt that the authors oversold some of their data in the text, and I'd recommend being a bit more careful when claiming an experiment 'confirms' a specific model. In many cases, there are other models that could explain similar results. For example, in Figure 1C, the authors state that their crystal structure 'confirms' that "RING2 is transiently displaced from the RING0 domain and returns to its original position after washing off the p-Ubl linker". However, it isn't clear to me that RING2 ever dissociated when prepared this way. While there are issues with the work that I feel should be further addressed with additional experiments, there are interesting mechanistic details suggested by this work that could improve our understanding of Parkin activation. However, the full impact of this work won't be fully appreciated until there is a more thorough understanding of the regulation and competitive binding between p-Ubl and RIGN2 to RORB both in cis and in trans.

Reviewer #2 (Public Review):

Summary:

The authors tried to test the hypothesis that Cdk8 and Cdk19 stabilize the cytoplasmic CcNC protein, the partner protein of the Mediator complex including CDK8/19 and Mediator protein via a kinase-independent function by generating induced double knockout of Cdk8/19. However, the evidence presented suffers from a lack of focus and rigor and does not support their claims.

Strengths:

This is the first comprehensive report on the effect of a double knockout of CDK8 and CDK19 in mice on male fertility, hormones, and single-cell testicular cellular expression. The inducible knockout mice led to male sterility with severe spermatogenic defects, and the authors attempted to use this animal model to test the kinase-independent function of CDK8/19, previously reported for humans. Single-cell RNA-seq of knockout testis presented a high resolution of molecular defects of all the major cell types in the testes of the inducible double knockout mice. The authors also have several interesting findings such as reentry into cell cycles by Sertoli cells, and loss of Testosterone in induced dko that could be investigated further.

Weaknesses:

The claim of reproductive defects in the induced double knockout of CDK8/19 resulted from the loss of CCNC via a kinase-independent mechanism is interesting but was not supported by the data presented. While the construction and analysis of the systemic induced knockout model of Cdk8 in Cdk19KO mice is not trivial, the analysis and data are weakened by the systemic effect of Cdk8 loss, making it difficult to separate the systemic effect from the local testis effect.

The analysis of male sterile phenotype is also inadequate with poor image quality, especially testis HE sections. The male reproductive tract picture is also small and difficult to evaluate. The mice crossing scheme is unusual as you have three mice to cross to produce genotypes, while we could understand that it is possible to produce pups of desired genotypes with different mating schemes, such a vague crossing scheme is not desirable and of poor genetics practice. Also using TAM-treated wild type as control is ok, but a better control will be TAM-treated ERT2-cre; CDK8f/f or TAM-treated ERT2 Cre CDK19/19 KO, so as to minimize the impact from the well-recognized effect of TAM.

While the authors proposed that the inducible loss of CDK8 in the CDK19 knockout background is responsible for spermatogenic defects, it was not clear in which cells CDK8/19 genes are interested and which cell types might have a major role in spermatogenesis. The authors also put forward the evidence that reduction/loss of Testosterone might be the main cause of spermatogenic defects, which is consistent with the expression change in genes involved in steroigenesis pathway in Leydig cells of inducible double knockout. However it is not clear how the loss of Testosterone contributed to the loss of CcnC protein.

The authors should clarify or present the data on where CDK8 and CDK19 as well as CcnC are expressed so as to help the readers understand which tissues both CDK might be functioning in and cause the loss of CcnC. It should be easier to test the hypothesis of CDK8/19 stabilizing CcnC protein using double knock-out primary cells, instead of the whole testis.

Since CDK8KO and CDK19KO both have significantly reduced fertility in comparison with wildtype, it might be important to measure the sperm quantity and motility among CDK8 KO, CDK19KO, and induced DKO to evaluate spermatogenesis based on their sperm production.

Some data for the inducible knockout efficiency of Cdk8 were presented in Supplemental Figure 1, but there is no legend for the supplemental figures, it was not clear which band represented the deletion band, and which tissues were examined. Tail or testis? It seems that two months after the injection of Tam, all the Cdk8 were completely deleted, indicating extremely efficient deletion of Tam induction by two months post administration. Were the complete deletion of Cdk8 happening even earlier? An examination of time points of induced loss would be useful and instructional as to when is the best time to examine phenotypes.

The authors found that Sertoli cells re-entered the cell cycle in the inducible double knockout but stopped short of careful characterization other than increased expression of cell cycle genes.

Overall this work suffered from a lack of focus and rigor in the analysis and lack of sufficient evidence to support their main conclusions.

Minor:

Dko should be appropriately named iDKO (induced dKO).

"suppress spermatogenesis and male fertility" in the title does not fit the evidence presented.

"DKO males, had an understized and dedifferentiated reproductive system?" what is the evidence for "undifferentiated"?

We performed necropsy ? not the right wording here.

Colchicine-lke apoptotic bodies ? what does this mean? Not clear.

Images throughout the manuscript suffer from poor resolution and are often blurry and hard to evaluate.

To pinpoint the meiotic stage defect of iDKO, it is better to use the meiotic chromosome spread approach.

Reviewer #2 (Public Review):

The manuscript by Ma et al. tries to develop a protocol for cell-based meat production using chicken fibroblasts as three-dimensional (3D) muscle tissues with fat accumulation. The authors used genetically modified fibroblasts, which can be forced to differentiate into muscle cells, and formulated 3D tissues with these cells and a biphasic material (hydrogel). The degrees of muscle differentiation and lipid deposition in culture were determined by immunohistochemical, biochemical, and molecular biological evaluations. Notably, the protocol successfully achieved the process of myogenic and lipogenic stimulation in the 3D tissues.

As addressed after the initial review process, the manuscript is clearly written with well-supportive figures. The study design is reasonable with adequate analysis. In the revised manuscript, the authors further discussed the ideas in terms of the approach using genetic modification for cell-based meat production. However, more careful considerations may still be helpful when actually using the technology for cultivated meat production.

Reviewer #2 (Public Review):

Summary:

In the manuscript, the authors have presented new mechanistic details to show how intracellular cAMP levels are maintained and linked to the phosphodiesterase enzyme which in turn is controlled by PhoP. Later, they showed the physiological relevance linked to altered cAMP concentrations.

Strengths:

Well-thought-out experiments. The authors carefully planned the experiments well to uncover the molecular aspects of it diligently.

Weaknesses:

None. The authors have meticulously responded to all my queries and concerns through multiple rounds of review.

Reviewer #2 (Public Review):

Summary:

This paper describes the latest version of the most popular program for CTF estimation for cryo-EM images: CTFFIND5. New features in CTFFIND5 are the estimation of tilt geometry, including for samples, like FIB-milled lamellae, that are pre-tilted along a different axis than the tilt axis of the tomographic experiment, plus the estimation of sample thickness from the expanded CTF model described by McMullan et al (2015). The results convincingly show the added value of the program for thicker and tilted images, such as are common in modern cryo-ET experiments. The program will therefore have a considerable impact on the field.

I have only minor suggestions for improvement below:

Abstract: "[CTF estimation] has been one of the key aspects of the resolution revolution"-> This is a bit over the top. Not much changed in the actual algorithms for CTF estimation during the resolution revolution.<br /> L34: "These parameters" -> Cs is typically given, only defocus (and if relevant phase shift) are estimated.<br /> L110-116: The text is ambiguous: are rotations defined clockwise or counter-clockwise? It would be good to explicitly state what subsequent rotations, in which directions and around which axes this transformation matrix (and the input/output angles in CTFFIND5) correspond to.<br /> L129-130: As a suggestion: it would be relatively easy, and possibly beneficial to the user, to implement a high-resolution limit that varies with the accumulated dose on the sample. One example of this exists in the tomography pipeline of RELION-5.<br /> Substituting Eq (7) into Eq (6) yields ksi=pi, which cannot be true. If t is the sample thickness, then how can this be a function of the frequency g of the first node of the CTF function? The former is a feature of the sample, the latter is a parameter of the optical system. This needs correction.

Reviewer #2 (Public Review):

Summary:

This study by Mendes et al provides novel key insights into the role of chemotaxis and immune cell recruitment into the hypothalamus in the development of diet-induced obesity. Specifically, the authors reveal that although transcriptional changes in hypothalamic resident microglia following exposure to high-fat feeding are minor, there are compelling transcriptomic differences between resident microglia and microglia recruited to the hypothalamus, and these are sexually dimorphic. Using independent loss-of-function studies, the authors also demonstrate an important role of CXCR3 and hypothalamic CXCL10 in the hypothalamic recruitment of CCR2+ positive cells on metabolism following exposure to high-fat diet-feeding in mice. This manuscript puts forth conceptually novel evidence that inhibition of chemotaxis-mediated immune cell recruitment accelerates body weight gain in high-fat diet-feeding, suggesting that a subset of microglia that express CXCR3 may confer protective, anti-obesogenic effects.

Strengths:

The work is exciting and relevant given the prevalence of obesity and the consequences of inflammation in the brain on perturbations of energy metabolism and ensuant metabolic diseases. Hypothalamic inflammation is associated with disrupted energy balance, and activated microglia within the hypothalamus resulting from excessive caloric intake and saturated fatty acids are often thought to be mediators of impairment of hypothalamic regulation of metabolism. The present work reports a novel notion in which immune cells recruited into the hypothalamus that express chemokine receptor CXCR3 may have a protective role against diet-induced obesity. In vivo studies reported herein demonstrate that inhibition of CXCR3 exacerbates high-fat diet-induced body weight gain, increases circulating triglycerides and fasting glucose levels, worsens glucose tolerance, and increases the expression of orexigenic neuropeptides, at least in female mice.

This work provides a highly interesting and needed overview of preclinical and clinical brain inflammation, which is relevant to readers with an interest in metabolism and immunometabolism in the context of obesity.

Using flow cytometry, cell sorting, and transcriptomics including RNA-sequencing, the manuscript provides novel insights into transcriptional landscapes of resident and recruited microglia in the hypothalamus. Importantly, sex differences are investigated.

Overall, the manuscript is perceived to be highly interesting, relevant, and timely. The discussion is thoughtful, well-articulated, and a pleasure to read and felt to be of interest to a broad audience.

Weaknesses:

There were no major weaknesses perceived. Some comments for potential textual additions to the results/discussion are listed in recommendations to authors.

Reviewer #2 (Public Review):

The hard work of the authors is much appreciated. With overexpression of a-arrestin Txnip in RPE, cones and the combined respectively, the authors show a potential gene agnostic treatment that can be applied to retinitis pigmentosa. Furthermore, since Txnip is related to multiple intracellular signaling pathway, this study is of value for research in the mechanism of secondary cone dystrophy as well.

Strengths

- The follow-up study builds on innovative ground by exploring the impact of TxnipC247S and its combination with HSP90AB1 knockdown on cone survival, offering novel therapeutic pathways.<br /> - Testing of different Txnip deletion mutants provides a nuanced understanding of its functional domains, contributing valuable insights into the mechanism of action in RP treatment.<br /> - The findings regarding GLUT1 clearance and the differential effects of Txnip mutants on cone and RPE cells lay the groundwork for targeted gene therapy in RP.

Comments on revised version:

The researchers answered our questions and included additional discussion in the manuscript.

Reviewer #2 (Public Review):

In their manuscript entitled "BEND2 is a crucial player in oogenesis and reproductive aging", the authors present their findings that full-length BEND2 is important for repair of meiotic double strand break repair in spermatocytes, regulation of LINE-1 elements in spermatocytes, and proper oocyte meiosis and folliculogenesis in females. The manuscript utilizes an elegant system to specifically ablate the full-length form of BEND2 which has been historically difficult to study due to its location on the X chromosome and male sterility of global knockout animals.

While the manuscript is an overall excellent addition to the field, it would significantly benefit from a few additional experiments, as well as some additional clarification/elaboration.

The claim that BEND2 is required for ovarian reserve establishment is not supported, as the authors only look at folliculogenesis and oocyte abundance starting at one week of age, after the reserve is formed. Analysis of earlier time points would be much more convincing and would parse the role of BEND2 in the establishment vs. maintenance of this cell population. In spermatocytes, the authors demonstrate a loss of nuclear BEND2 in their mutant but do not comment on the change in localization (which is now cytoplasmic) of the remaining protein in these animals. This may have true biological significance and a discussion of this should be more thoroughly explored.

Reviewer #2 (Public Review):

Summary:

In this manuscript, Shah et al. explore the function of an understudied neural circuitry from the dLS -> LHA -> RVM in mediating stress-induced analgesia. They initially establish this neural circuitry through a series of intersectional tracings. Subsequently, they conduct behavioral tests, coupled with optogenetic or chemogenetic manipulations, to confirm the involvement of this pathway in promoting analgesia. Additionally, fiber photometry experiments are employed to investigate the activity of each brain region in response to stress and pain.

Strengths:

Overall, the study is comprehensive, and the findings are compelling.

Weaknesses:

One noteworthy concern arises regarding the overarching hypothesis that restrained-induced stress promotes analgesia. A more direct interpretation suggests that intense struggling, rather than stress per se, activates the dLS -> LHA -> RVM pathway that may drive analgesic responses.

Reviewer #2 (Public Review):

To enable robust production of hematopoietic progenitors in-vitro, Petazzi et al examined the role of transcription factors in the arterial hemogenic endothelium. They use IGFBP2 as a candidate gene to increase the directed differentiation of iPSCs into hematopoietic progenitors. They have established a novel induced-CRISPR mediated activation strategy to drive the expression of multiple endogenous transcription factors and show enhanced production of hematopoietic progenitors through expansion of the arterial endothelial cells. Further, upregulation of IGFBP2 in the arterial cells facilitates the metabolic switch from glycolysis to oxidative phosphorylation, inducing hematopoietic differentiation. While the overall study and resources generated are good, assertions in the manuscript are not entirely supported by the experimental data and some claims need further experimental validation.

Reviewer #2 (Public Review):

Summary:

This paper investigates virus-host interactions in deep-sea bacteriophage systems which employ a seemingly mutualistic approach to viral replication in which the virus aids host cell polysaccharide import and utilization via metabolic reprogramming. The hypothesis being tested is supported with solid and convincing evidence and the findings are potentially generalizable with implications for our understanding of polysaccharide-mediated virus-host interactions and carbon cycles in marine ecosystems more broadly.

Strengths:

This paper synthesizes sequencing and phylogenic analyses of two Lentisphaerae bacteria and three phage genomes; electron microscopy imaging of bacterial/phage particles; differential gene expression analyses; differential growth curve analyses, and differential phage proliferation assays to extract insights into whether laminarin and starch can induce both host growth and phage proliferation. The data presented convincingly demonstrate that both host culture density and phage proliferation increase as a result having host, phage, and polysaccharide carbon source together in culture.

Weaknesses (suggestions for improvement):

The article would be strengthened by the following additional experiment: providing the phage proteins hypothesized to be aiding host cell growth (red genes from Figure 5...TonB system energizer ExbB, glycosidases, etc) individually or in combination on plasmids rather than within the context of the actual phage itself to see if such additional genes are necessary and sufficient to realize the boosts in host cell growth/saturation levels observed in the presence of the phages tested.

The paper would also benefit from additional experiments focused on determining how the polysaccharide processing, transport, and metabolism genes are being used by the phages to either directly increase viral infection/replication or else to indirectly do so by supporting the growth of the host in a more mutualistic manner (i.e. by improving their ability to import, degrade, and metabolize polysaccharides).

The introduction would benefit from a discussion of what is known regarding phage and/or viral entry pathways that utilize carbohydrate anchors during host entry. The discussion could also be improved by linking the work presented to the concept of "selfishness" in bacterial systems (see for instance Giljan, G., Brown, S., Lloyd, C.C. et al. Selfish bacteria are active throughout the water column of the ocean. ISME COMMUN. 3, 11 (2023) https://doi.org/10.1038/s43705-023-00219-7). The bacteria under study are gram negative and it was recently demonstrated (https://www.nature.com/articles/ismej201726) that "selfish" bacteria sequester metabolizable polysaccharides in their periplasm to advantage. It is plausible that the phages may be hijacking this "selfishness" mechanism to improve infectivity and ENTRY rather than helping their hosts to grow and profilerate so they can reap the benefits of simply having more hosts to infect. The current work does not clearly distinguish between these two distinct mechanistic possibilities. The paper would be strengthened by at least a more detailed discussion of this possibility as well as the author's rationale for interpreting their data as they do to favor the "mutualistic" interpretation. In the same light, the paper would benefit from a more careful choice of words which can also help to make such a distinction more clear/evident/intentional. As currently written the authors seem to be actively avoiding giving insights wrt this question.

Finally, I would be interested to know if the author's sequencing datasets might be used to inform the question raised above by using bacterial immunity systems such as CRISPR/Cas9. For example, if the phage systems studied are truly beneficial/mutualistic for the bacteria then it's less likely that there would be evidence of targeted immunity against that particular phage that has the beneficial genes that support polysaccharide metabolism.

Reviewer #2 (Public Review):

Summary:

The preprint by Fawaz et al. presents the findings of a study that aimed to assess the relationship between somatic mutations associated with clonal hematopoiesis (CHIP) and the prevalence of myocardial infarction (MI). The authors conducted targeted DNA sequencing analyses on samples from 149 MI patients and 297 non-MI controls from a separate cohort. Additionally, they investigated the impact of the loss of the Y chromosome (LOY), another somatic mutation frequently observed in clonally expanded blood cells. The results of the study primarily demonstrate no significant associations, as neither CHIP nor LOY were found to be correlated with an increased prevalence of MI. Of note, the null findings regarding CHIP are in conflict with several larger studies in the literature.

Strengths:

Overall, this is a useful research work on an emerging risk factor for cardiovascular disease (CVD). The use of a targeted sequencing approach is a strength, as it offers higher sensitivity than the whole exome sequencing approaches used in many previous studies.

Weaknesses:

Reporting null findings is definitely relevant in an emerging field such as the role of somatic mutations in cardiovascular disease. Nevertheless, the study suffers from severe limitations, which casts doubts on the authors' conclusions, as detailed below:

(1) The small sample size of the study population is a critical limitation, particularly when reporting null findings that conflict (partly) with positive findings in much larger studies, totaling hundreds of thousands of individuals (e.g. Zekavat et al, Nature CVR 2023, Vlasschaert et al, Circulation 2023; Zhao et al, JAMA Cardio 2024). The authors claim that they have 90% power to detect an effect size of CHIP on MI comparable to that in a previous report (Jaiswal et al, NEJM 2017). However, the methodology used to estimate statistical power is not described. Furthermore, the work by Jaiswal et al (NEJM 2017) showed a hazard ratio of approx. 2.0, but more recent work in much larger populations suggests that the overall effect of CHIP on atherosclerotic CVD is smaller, most likely due to the heterogeneity of effects of different mutated genes (e.g. Zekavat et al, Nature CVR 2023, Vlasschaert et al, Circulation 2023; Zhao et al, JAMA Cardio 2024). In addition, several analyses in the current manuscript are conducted separately in MI(+) (n= 149) and MI(-) (N=297) individuals, further limiting statistical power. Power is still lower in the investigation of the effects of LOY and its interaction with CHIP, as only men are included in these analyses. Overall, I believe the study is severely underpowered, which calls into question the validity of the reported null findings.

(2) Related to the above, it is widely accepted that the effects of CHIP on CVD are highly heterogeneous, as some mutated genes appear to have a strong impact on atherosclerosis, whereas the effect of others is negligible (e.g. Zekavat et al, Nature CVR 2023, Vlasschaert et al, Circulation 2023, among others). TET2 mutations are frequently considered a "positive control", given the multiple lines of evidence suggesting that these mutations confer a higher risk of atherosclerotic disease. However, no association with MI or related variables was found for TET2 mutations in the current work. Reporting the statistical power specifically for assessing the effect of TET2 mutations would enhance the interpretation of these results.

(3) One of the most essential features of CHIP is the tight correlation with age. In this study, the effect of age on CHIP (Supplementary Tables S5, S6) seems substantially milder than in previous studies. Given the relatively weak association with age here, it is not surprising that no association with MI or atherosclerotic disease was found, considering that this association would have a much smaller effect size. In addition, there are previous reports of sex-related differences in the prevalence of CHIP, is there an association between CHIP and age after adjusting for sex?

(4) The mutated genes included in the definition of "CHIP" here are markedly different than those in most previous studies, particularly when considering specifically the studies that demonstrated an association between CHIP and atherosclerotic CVD. For instance, the definition of CHIP in this manuscript includes genes such as ANKRD26, CALR, CCND2, and DDX41... that are not prototypical CHIP genes. This is unlikely to have a major impact on the main results, as the vast majority of mutations detected are indeed in bona fide CHIP genes, but it should be at least acknowledged. Furthermore, the strategy used here for the CHIP variant calling and curation seems substantially different than that used in previous studies, which precludes a direct comparison. This is important because such differences in the definition of CHIP and the curation of variants are the basis of most conflicting findings in the literature regarding the effects of this condition. Ideally, the authors should conduct sensitivity analyses restricted to prototypical CHIP genes, using the criteria that have been previously established in the field (e.g. Vlasschaert et al, Blood 2023).

(5) An important limitation of the current study is the cross-sectional design of most of the analyses. For instance, it is not surprising that no association is found between CHIP and prevalent atherosclerosis burden by ultrasound imaging, considering that many individuals may have developed atherosclerosis years or decades before the expansion of the mutant clones, limiting the possible effect of CHIP on atherosclerosis burden. Similarly, the analysis of the relationship between CHIP and a history of MI may be confounded by the potential effects of MI on the expansion of mutant clones. In this context, it is noteworthy that the only positive results here are found in the analysis of the relationship between CHIP at baseline and incident MI development over follow-up. Increasing the sample size for these longitudinal analyses would provide deeper insights into the relationship between CHIP and MI.

(6) The description of some analyses lacks detail, but it seems that statistical analyses were exclusively adjusted for age or age and sex. The lack of adjustment for conventional cardiovascular risk factors in statistical analyses may confound results, particularly given the marked differences in several variables observed between groups.

(7) The variant allele fraction (VAF) threshold for identifying clinically relevant clonal hematopoiesis is still a subject of debate. The authors state that subjects without any detectable mutation or with mutations with a VAF below 2% were considered non-CHIP carriers. While this approach is frequent in the field, it likely misses many impactful mutations with lower VAFs. Such false negatives could contribute to the null findings reported here. Ideally, the authors should determine the lower detection limit of their sequencing approach (either computationally or through serial dilution experiments) and identify the threshold of VAF that can be detected reliably with their sequencing assay. The association between CHIP and MI should then be evaluated considering all mutations above this VAF threshold, in addition to sensitivity analyses with other thresholds frequent in the literature, such as 1% VAF, 2% VAF, and 10% VAF.

(8) The authors should justify the use of 3D vascular ultrasound imaging exclusively in the supra-aortic trunk. I am not familiar with this technique, but it seems to be most typically used to evaluate atherosclerosis burden in superficial vascular beds such as carotids or femorals. I am concerned about the potential impact of tissue depth on the accurate quantification of atherosclerosis burden in the current study (e.g. https://doi.org/10.1016/j.atherosclerosis.2016.03.002). It is unclear whether the carotids or femorals were imaged in the study population.

(9) The specific criteria used to define LOY need to be justified. LOY is stated to be defined based on a "A cut off of 9% of cells with mLOY defined the detection of a mLOY based on the study of 30 men of less than 40 years who had a normal karyotype as assessed by conventional cytogenetic study." As acknowledged by the authors, this definition of LOY is substantially different than that used in recent studies employing the same technique to detect LOY (Mas-Peiro et al, EHJ 2023). In addition, it seems essential to provide more detailed information on the ddPCR assay used to determine LOY, including the operating range and, more importantly, the lower limit of detection (%LOY) of the assay. A dilution series of a control DNA with no LOY would be helpful in this context.

(10) Our understanding of the relationship between CHIP and CVD is evolving fast, and the manuscript should be considered in the context of recent literature in the field. For instance, the recent work by Zhao et al (JAMA Cardio 2024, doi:10.1001/jamacardio.2023.5095) should be considered, as it used a similar targeted DNA sequencing approach as the one used here, but found a clear association between CHIP and coronary heart disease (in a population of 6181 individuals).

(11) The use of subjective terms like "comprehensive" or "thorough" in the title of the manuscript does not align with the objective nature of scientific reporting.

Reviewer #2 (Public Review):

Interesting work with an original and appealing hypothesis. The authors performed an open-label trial comparing nebulized dornase alfa to best available care in COVID-19, reaching the primary outcome of CRP reduction over the first week of intervention. The main weaknesses of the study are the small sample size, the lack of randomization for the majority of the participants, and the lack of blinding. The authors have sufficiently addressed the issues raised, provided that these weaknesses are highlighted in the limitations section.

Reviewer #2 (Public Review):

Zhang et al. established chronic unpredictable mild stress (CUMS) mouse model, which displayed osteoporosis phenotype, suggesting a potential correlation between psychological stress and bone metabolism. They found that miRNA candidate miR-335-3p is downregulated in the long bone of CUMS mice through microRNA sequencing and qRT-PCR experiments. They further demonstrated that miR-335-3p attenuates osteoclast activity via inhibiting Fos signaling, which can induce NFATC1 expression and regulate osteoclast activity.

Strengths:

The authors established CUMS mouse model and confirmed the osteoporosis phenotype through careful characterization of bone and analysis of osteoclast activity. They performed microRNA sequencing to identify the miRNA candidate regulating the bone loss in the CUMS mouse model. They also validated the expression of miR-335-3p and interfered with the function of miR-335-3p through an in vitro assay. Overall, the findings from this study provide important hints for the correlation between psychological stress and bone metabolism.

Weakness:

The data provided by the authors are preliminary, especially the mechanistic insight, which needs to be enhanced. The authors have shown that miR-335-3p expression was altered in the CUMS mouse model and the change of its expression regulated osteoclast activity. The validation should be conducted in vivo, and the mechanism behind this should be investigated further.

Reviewer #2 (Public Review):

Summary:

This is an interesting and impressive study that provides a rare opportunity to learn about brain-behaviour links of learning systems at a relatively early stage of development.

The main strengths are that the authors followed a relatively large group of children over 2 years and used a reinforcement learning task aimed at assessing learning that depends on both the striatum and the hippocampus. The authors also included a thorough overview of the computational models and the choices they made. I think this paper would be of considerable interest and contributes to knowledge about how learning and memory systems change with development.

Reviewer #2 (Public Review):

Summary

Faress et al. address how synaptic plasticity (i.e. potentiation induced by high frequency stimulation, HFS) induced at different time points and pathways relative to those active during initial learning can transform memories. They adopt an experimental design developed by Nabavi et al, 2014 to optogenetically induce a weak fear memory by pairing an optical conditioned stimulus (CS) at thalamo-LA synapses with a footshock unconditioned stimulus (US) in male mice. Homosynaptic HFS delivered in the same pathway before or after conditioning transforms the weak memory into a stronger one. Leveraging a new dual wavelength optogenetic approach in vivo, they also show that heterosynaptic (cortico-LA) HFS directly following the opto-conditioning can transform the thalamo-LA induced fear memory, or create a memory when directly delivered after unpaired conditioning. Lastly, they demonstrate that heterosynaptic potentiation of the thalamo-LA pathway accompanies the strengthening of fear memory in freely moving mice. The authors conclude that a transient experience (i.e. weak memory) can be transformed into a stable one by non-Hebbian forms of plasticity.

Strengths

This study uses well-defined and elegant optogenetic manipulations of distinct neural pathways in awake behaving mice combined with in vivo recordings, which allows to directly manipulate and monitor synaptic strength and memory. It addresses an interesting, timely, and important question.

Weaknesses

A key experiment with in vivo monitoring of LFPs and behavior (Fig. 5a-c) seems a bit underpowered and input-output curves (extended data 5c) not entirely convincing.<br /> Ex vivo slice experiments (Fig. 5d-f) are not well aligned with in vivo experimental conditions. While they provide proof of principle, this is not entirely novel (see Fonseca et al, 2013).

Significance and impact

The conclusions are well supported by the data. The significance of the study lies in showing in vivo, that plasticity induced at different times or synaptic pathways than those engaged during learning can modify a memory and the synaptic strength in the neural pathway related to that memory. While heterosynaptic and timing-dependent effects in synaptic plasticity have been described largely ex vivo on shorter time scales, the discovery of lasting behavioral effects on memory is novel. The study was enabled by a combination of clever approaches: creation of a "synthetic" pathway-specific association and a novel dual opsin approach in vivo to probe the role of plasticity in a converging second pathway at the same time.<br /> This work broadens our understanding of how Hebbian and non-Hebbian forms of plasticity shape neural activity and associative memory and is of broad interest to the neuroscience community.

Reviewer #2 (Public Review):

Summary:

The authors investigated how predicted stimuli are represented in posterior regions of the brain by recording electroencephalography during a visual sequence learning task. After learning the spatial order in which four stimuli were presented within a fixed sequence, participants were shown partial sequences - i.e., sequences in which only one element of the sequence was presented. By examining the decoding accuracy of the omitted stimuli, the authors aimed to investigate whether anticipated stimuli are (pro)actively represented in the expected spatial location at the expected time.

Strengths and Weaknesses:

The study successfully replicated previous findings on omitted stimuli within a predicted sequence (Ekman et al., 2023), while providing novel information regarding the temporal dynamics of predictive representation. Nevertheless, this outcome is not entirely surprising, as similar temporal dynamics were observed in a previous study employing a different task (Kok et al., 2017). The high level of scientific rigor is evident, as demonstrated by the numerous control analyses. Additionally, the results are particularly intriguing in terms of discerning the nature of the prepared representation, spanning from early perceptual to late attentional representations. Unfortunately, this distinction is not investigated in detail, thus allowing for alternative interpretations of the results.

The connection between the findings and the literature on priority maps could benefit from further clarification. There is room for a clearer delineation of how much of the representation can be ascribed to a perceptual prediction mechanism versus an attentional (post-perceptual) spatial cueing process. Although the latter can be readily connected to the concept of a priority map guiding spatial attention, the relationship between the priority map and perceptual prediction remains somewhat ambiguous. Noteworthy, an explanation of the results in terms of spatial cueing does not necessarily require a perceptual predictive mechanism. The significant decoding of the location of the omitted stimulus might be attributed to the preceding stimulus orienting attention towards the following location. While this potential explanation was not explicitly addressed in the study, it presents an intriguing avenue for further investigation.

The study provides valuable insight into how omitted, yet predicted stimuli are represented in the brain and its dynamics. While the research is commendable, addressing the outlined limitations would enhance its impact in the field. Specifically, the spatial location decoding results do not disentangle between perceptual prediction (i.e., the features of the expected stimulus) and attentional processes (i.e., the cueing of the to-be-attended location),

Reviewer #2 (Public Review):

Summary:

The authors investigate axonal and synapse development in two distinct visual feature-encoding neurons (VPN), LC4 and LPLC2. They first show that they occupy distinct regions on the GF dendrites, and likely arrive sequentially. Analysis of the VPNs' morphology throughout development, and synaptic gene and protein expression data reveals the temporal order of maturation. Functional analysis then shows that LPLC2 occupancy of the GF dendrites is constrained by LC4 presence.

Strengths:

The authors investigate an interesting and very timely topic, which will help to understand how neurons coordinate their development. The manuscript is very well written, and data are of high quality, that generally support the conclusions drawn (but see some comments for Fig. 2 below). A thorough descriptive analysis of the LC4/LPLC2 to GF connectivity is followed by some functional assessment showing that one neuron's occupancy of the GF dendrite depend on another.<br /> The manuscripts uses versatile methods to look at membrane contact, gene and protein expression (using scRNAseq data and state-of-the art genetic tools) and functional neuronal properties. I find it especially interesting and elegant how the authors combine their findings to highlight the temporal trajectory of development in this system.

Weaknesses:

After reading the summary, I was expecting a more comprehensive analysis of many VPNs, and their developmental relationships. For a better reflection of the data, the summary could state that the authors investigate *two* visual projection neurons (VPNs) and that ablation *of one cell type of VPNs* results in the expansion of the remaining VPN territory.

The manuscript is falling a bit short of putting the results into the context of what is known about synaptic partner choice/competition between different neurons during neuronal or even visual system development. Lots of work has been done in the peripheral the visual system, from the Hiesinger lab and others. Both the introduction and the discussion section should elaborate on this.

The one thing that the manuscript does not unambiguously show is when the connections between LC4 and LPLC2 become functional.

Figure 2:<br /> Figure 2A-C: I found the text related to that figure hard to follow, especially when talking about filopodia. Overall, life imaging would probably clarify at which time point there really are dynamic filopodia. For this study, high magnification images of what the authors define as filopodia would certainly help.<br /> L137ff: This section talks about filopodia between 24-48 hAPF, but only 36h APF is shown in A, where one could see filopodia. The other time points are shown in B and C, but number of filopodia is not quantified.<br /> L143: "filopodia were still present, but visibly shorter": This is hard to see, and again, not quantified.<br /> L144f: "from 72h APF to eclosion, the volume of GF dendrites significantly decreased": this is not actually quantified, comparisons are only done to 24, 36 and 48 h APF.<br /> Furthermore, 72h APF is not shown here, but in Figure 2D, so either show here, or call this figure panel already?

Figure 2D/E: to strengthen the point that LC4 and LPLC2 arrive sequentially, it would help to show all time points analyzed in Figure D/E.

L208: "significant increase ... from 60h APF to 72h APF": according to the figure caption, this comparison is marked by "+" but there is no + in the figure itself.

Figure 3:<br /> A key point of the manuscript is the sequential arrival of different VPN classes. So then why is the scRNAseq analysis in Figure 3 shown pooled across VPNs? Certainly, the reader at this point is interested in temporal differences in gene expression. The class-specific data are somewhat hidden in Supp. Fig. 9, and actually do not show temporal differences. This finding should be presented in the main data.

L438: "silencing LC4 by expressing Kir2.1... reduced the GF response": Is this claim backed by some quantification?

Figure 4K: Do the control data have error bars, which are just too small to see? And what is tested against what? Is blue vs. black quantified as well? What do red, blue, and black asterisks indicate? Please clarify in figure caption.

Optogenetics is mentioned in methods (in "fly rearing", in the genotypes, and there is an extra "Optogenetics" section in methods), but no such data are shown in the manuscripts. (If the authors have those data, it would be great to know when the VPN>GF connections become functional!)

Methods:

Antibody concentrations are not given anywhere and will be useful information for the reader

Could the authors please give more details on the re-analysis of the scRNAseq dataset? How did you identify cell type clusters in there, for example?

L785 and L794: I am curious. Why is it informative to mention what was *not* done?

Custom-written analysis code is mentioned in a few places. Is this code publicly available?

Reviewer #2 (Public Review):

Summary:

This manuscript by Poltavski and colleagues explores the relative contributions of Pax2- and Wnt1- lineage-derived cells in the enteric nervous system (ENS) and how they are each affected by disruptions in Ret and Endrb signaling. The current understanding of ENS development in mice is that vagal neural crest progenitors derived from a Wnt1+ lineage migrate into and colonize the developing gut. The sacral neural crest was thought to make a small contribution to the hindgut in addition but recent work has questioned that contribution and shown that the ENS is entirely populated by the vagal crest (PMID: 38452824). GDNF-Ret and Endothelin3-Ednrb signaling are both known to be essential for normal ENS development and loss of function mutations are associated with a congenital disorder called Hirschsprung's disease. The transcription factor Pax2 has been studied in CNS and cranial placode development but has not been previously implicated in ENS development. In this work, the authors begin with the unexpected observation that conditional knockout of Ednrb in Pax2-expressing cells causes a similar aganglionosis, growth retardation, and obstructed defecation as conditional knockout of Ednrb in Wnt1-expressing cells. The investigators then use the Pax2 and Wnt1 Cre transgenic lines to lineage-trace ENS derivatives and assess the effects of loss of Ret or Ednrb during embryonic development in these lineages. Finally, they use explants from the corresponding embryos to examine the effects of GDNF on progenitor outgrowth and differentiation.

Strengths:

- The manuscript is overall very well illustrated with high-resolution images and figures. Extensive data are presented.

- The identification of Pax2 expression as a lineage marker that distinguishes a subset of cells in the ENS that may be distinct from cells derived from Wnt1+ progenitors is an interesting new observation that challenges the current understanding of ENS development.

- Pax2 has not been previously implicated in ENS development - this manuscript does not directly test that role but hints at the possibility.

- Interrogation of two distinct signaling pathways involved in ENS development and their relative effects on the two purported lineages.

Weaknesses:

- The major challenge with interpreting this work is the use of two transgenic lines, rather than knock-ins, Wnt1-Cre and Pax2-Cre, which are not well characterized in terms of fidelity to native gene expression and recombination efficiency in the ENS. If 100% of cells that express Wnt1 do not express this transgene or if the Pax2 transgene is expressed in cells that do not normally express Pax2, then these observations would have very different interpretations and not support the conclusions made. The two lineages are never compared in the same embryo, which also makes it difficult to assess relative contributions and renders the evidence more circumstantial than definitive.

- Visualization of the Pax2-Cre and Wnt-1Cre induced recombination in cross-sections at postnatal ages would help with data interpretation. If there is recombination induced in the mesenchyme, this would particularly alter the interpretation of Ednrb mutant experiments, since that pathway has been shown to alter gut mesenchyme and ECM, which could indirectly alter ENS colonization.

- No consideration of glia - are these derived from both lineages?

- No discussion of how these observations may fit in with recent work that suggests a mesenchymal contribution of enteric neurons (PMID: 38108810).

Reviewer #2 (Public Review):

Summary:

Developing neuronal models that are shareable, reproducible, and interoperable allows the neuroscience community to make better use of published models and to collaborate more effectively. In this manuscript, the authors present a consolidated overview of the NeuroML model description system along with its associated tools and workflows. They describe where different components of this ecosystem lay along the model development pathway and highlight resources, including documentation and tutorials, to help users employ this system.

Strengths:

The manuscript is well-organized and clearly written. It effectively uses the delineated model development life cycle steps, presented in Figure 1, to organize its descriptions of the different components and tools relating to NeuroML. It uses this framework to cover the breadth of the software ecosystem and categorize its various elements. The NeuroML format is clearly described, and the authors outline the different benefits of its particular construction. As primarily a means of describing models, NeuroML also depends on many other software components to be of high utility to computational neuroscientists; these include simulators (ones that both pre-date NeuroML and those developed afterwards), visualization tools, and model databases.

Overall, the rationale for the approach NeuroML has taken is convincing and well-described. The pointers to existing documentation, guides, and the example usages presented within the manuscript are useful starting points for potential new users. This manuscript can also serve to inform potential users of features or aspects of the ecosystem that they may have been unaware of, which could lower obstacles to adoption. While much of what is presented is not new to this manuscript, it still serves as a useful resource for the community looking for information about an established, but perhaps daunting, set of computational tools.

Weaknesses:

The manuscript in large part catalogs the different tools and functionalities that have been produced through the long development cycle of NeuroML. As discussed above, this is quite useful, but it can still be somewhat overwhelming for a potential new user of these tools. There are new user guides (e.g., Table 1) and example code (e.g. Box 1), but it is not clear if those resources employ elements of the ecosystem chosen primarily for their didactic advantages, rather than general-purpose utility. I feel like the manuscript would be strengthened by the addition of clearer recommendations for users (or a range of recommendations for users in different scenarios).

For example, is the intention that most users should primarily use the core NeuroML tools and expand into the wider ecosystem only under particular circumstances? What are the criteria to keep in mind when making that decision to use alternative tools (scale/complexity of model, prior familiarity with other tools, etc.)? The place where it seems most ambiguous is in the choice of simulator (in part because there seem to be the most options there) - are there particular scenarios where the authors may recommend using simulators other than the core jNeuroML software?

The interoperability of NeuroML is a major strength, but it does increase the complexity of choices facing users entering into the ecosystem. Some clearer guidance in this manuscript could enable computational neuroscientists with particular goals in mind to make better strategic decisions about which tools to employ at the outset of their work.

Reviewer #2 (Public Review):

Summary:

This study employed voltage imaging in the CA1 region of the mouse hippocampus during the exploration of a novel environment. The authors report synchronous activity, involving almost half of the imaged neurons, occurred during periods of immobility. These events did not correlate with SWRs, but instead, occurred during theta oscillations and were phased-locked to the trough of theta. Moreover, pairs of neurons with high synchronization tended to display non-overlapping place fields, leading the authors to suggest these events may play a role in binding a distributed representation of the context.

Strengths:

Technically this is an impressive study, using an emerging approach that allows single-cell resolution voltage imaging in animals, that while head-fixed, can move through a real environment. The paper is written clearly and suggests novel observations about population-level activity in CA1.

Weaknesses:

The evidence provided is weak, with the authors making surprising population-level claims based on a very sparse data set (5 data sets, each with less than 20 neurons simultaneously recorded) acquired with exciting, but less tested technology. Further, while the authors link these observations to the novelty of the context, both in the title and text, they do not include data from subsequent visits to support this. Detailed comments are below:

(1) My first question for the authors, which is not addressed in the discussion, is why these events have not been observed in the countless extracellular recording experiments conducted in rodent CA1 during the exploration of novel environments. Those data sets often have 10x the neurons simultaneously recording compared to these present data, thus the highly synchronous firing should be very hard to miss. Ideally, the authors could confirm their claims via the analysis of publicly available electrophysiology data sets. Further, the claim of high extra-SWR synchrony is complicated by the observation that their recorded neurons fail to spike during the limited number of SWRs recorded during behavior- again, not agreeing with much of the previous electrophysiological recordings.

(2) The authors posit that these events are linked to the novelty of the context, both in the text, as well as in the title and abstract. However, they do not include any imaging data from subsequent days to demonstrate the failure to see this synchrony in a familiar environment. If these data are available it would strengthen the proposed link to novelty if they were included.

(3) In the discussion the authors begin by speculating the theta present during these synchronous events may be slower type II or attentional theta. This can be supported by demonstrating a frequency shift in the theta recording during these events/immobility versus the theta recording during movement.

(4) The authors mention in the discussion that they image deep-layer PCs in CA1, however, this is not mentioned in the text or methods. They should include data, such as imaging of a slice of a brain post-recording with immunohistochemistry for a layer-specific gene to support this.

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 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.

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.

Comments on revised version:

The authors have addressed my comments.

Reviewer #2 (Public Review):

Summary:

This study proposed a new mechanism by which TGF-beta signaling pathway promotes contacts between oocyte and the surrounding somatic cells in mouse, by regulating the numbers of transzonal projections (TZPs).

Strengths:

The conditional Smad4 knockout and three-dimensional observation of transzonal projections are solid and sufficiently support the major conclusions.

Comments on revised version:

The authors have adequately addressed the reviewers' questions and comments.

Reviewer #2 (Public Review):

Summary:

In this paper, Chamness and colleagues make a pioneering effort to map epistatic interactions among mutations in a membrane protein. They introduce thousands of mutations to the mouse GnRH Receptor (GnRHR), either under wild-type background or two mutant backgrounds, representing mutations that destabilize GnRHR by distinct mechanisms. The first mutant background is W107A, destabilizing the tertiary fold, and the second, V276T, perturbing the efficiency of cotranslational insertion of TM6 to the membrane, which is essential for proper folding. They then measure surface expression of these three mutant libraries, using it as a proxy for protein stability, since misfolded proteins do not typically make it to the plasma membrane. The resulting dataset is then used to shed light on how diverse mutations interact epistatically with the two genetic background mutations. Their main conclusion is that epistatic interactions vary depending on the degree of destabilization and the mechanism through which they perturb the protein. The mutation V276T forms primarily negative (aggravating) epistatic interactions with many mutations, as is common to destabilizing mutations in soluble proteins. Surprisingly, W107A forms many positive (alleviating) epistatic interactions with other mutations. They further show that the locations of secondary mutations correlate with the types of epistatic interactions they form with the above two mutants.

Strengths:

Such a high throughput study for epistasis in membrane proteins is pioneering, and the results are indeed illuminating. Examples of interesting findings are that: (1) No single mutation can dramatically rescue the destabilization introduced by W107A. (2) Epistasis with a secondary mutation is strongly influenced by the degree of destabilization introduced by the primary mutation. (3) Misfolding caused by mis-insertion tends to be aggravated by further mutations. The discussion of how protein folding energetics affects epistasis (Fig. 7) makes a lot of sense and lays out an interesting biophysical framework for the findings.

Weaknesses:

The major weakness comes from the potential limitations in the measurements of surface expression of severely misfolded mutants. It seems that only about 5% of the W107A makes it to the plasma membrane compared to wild-type. This point is discussed quite fairly in the paper. (Figures 2 and 3). This might be a low starting point from which to accurately measure the effects of secondary mutations. I am concerned about the extent to which surface expression can report on protein stability, especially when it comes to double mutants where each mutation alone severely decreases surface expression. It is possible that in these cases, both the single and double mutants are completely misfolded, beyond repair. The surface-expressed proteins in such mutants may not be stable, folded or active at all, and the authors do not provide any indication that the combined effects of the mutations are derived from effects on folding stability or misfolding. Therefore, the reason for the epistatic effects of these mutations is hard to interpret, leaving a notable gap in our understanding. However, I find that this point is discussed much more fairly in the current manuscript.

With that said, I believe that the results regarding the epistasis of V276T with other mutations are strong and very interesting on their own.

Another concern relates to the measurements of the epistatic effects of mutations in the background of the V107A mutation. I am concerned about their measurement accuracy. Firstly, the authors note that the surface immunostaining measurements of these mutants are on average only 2-fold above background, which is quite a low signal-to-noise regimen. Secondly, I believe that the authors still haven't demonstrated the reproducibility of their surface expression measurements. To showcase the reproducibility, the authors show the correlation of two biological replicates in Figure S3. However, these are shown only for the 251 mutations that passed a reproducibility filter, after the authors "discarded variant scores for which the difference in percentile rank across the two replicates was greater than 25%. " . this means that all mutations that showed irreproducible results were filtered out before the analysis in Figure S3. It is, therefore, no surprise that the remaining mutations are highly reproducible, and such an analysis cannot serve as an indication of the reproducibility. It remains possible that a large fraction of the surface immunostaining scores of the V107A variants are dominated by noise and that their correlation in these two replicates might be random and may not necessarily be reproduced in a third replicate, for example.

Reviewer #2 (Public Review):

Summary:

This is an interesting work where Wen et al. aimed to shed light on the mechanisms driving the protective role of soluble uric acid (sUA) toward avoiding excessive inflammation. They present biochemical data to support that sUA inhibits the enzymatic activity of CD38 (Figures 1 and 2). In a mouse model of acute response to sUA and using mice deficient in CD38, they find evidence that sUA increases the plasma levels of nicotinamide nucleotides (NAD+ and NMN) (Figure 3) and that sUA reduces the plasma levels of inflammasome-driven cytokines IL-1b and IL-18 in response to endotoxin, both dependent on CD38 (Figure 4). Their work is an important advance in the understanding of the physiological role of sUA, with mechanistic insight that can have important clinical implications.

Strengths:

The authors present evidence from different approaches to support that sUA inhibits CD38, impacts NAD+ levels, and regulates inflammatory responses through CD38.

Weaknesses:

The authors investigate macrophages as the cells impacted by sUA to promote immunoregulation, proposing that inflammasome inhibition occurs through NAD+ accumulation and sirtuin activity due to sUA inhibition of CD38. Unfortunately, the study still lacks data to support this model, as they could not replicate their in vivo findings using murine bone marrow-derived macrophages, a standard model to assess inflammasome activation. Without an alternative approach, the study lacks data to establish in vitro that sUA inhibition of CD38 reduces inflammasome activation in macrophages - consequently, they cannot determine yet if both NAD+ accumulation and sirtuin activity in macrophages is a mechanism leading to sUA role in vivo.

Reviewer #2 (Public Review):

In the manuscript, the authors combine SARS-CoV-2 sequence data from a state in Germany and mobility data to help in understanding the movement of the virus and the potential to help decide where to focus sequencing. The global expansion in sequencing capability is a key outcome of the public health response. However, there remains uncertainty about how to maximise the insights the sequence data can give. Improved ability to predict the movement of emergent variants would be a useful public health outcome. Also knowing where to focus sequencing to maximising insights is also key. The presented case study from one State in Germany is therefore a useful addition to the literature. Nevertheless, I have a few comments.

One of the key goals of the paper is to explore whether mobile phone data can help predict the spread of lineages. However, it appears unclear whether this was actually addressed in the analyses. To do this, the authors could hold out data from a period of time, and see whether they can predict where the variants end up being found.

The abstract presents the mobility-guided sampling as a success, however, the results provide a much more mixed result. Ultimately, it's unclear what having this strategy really achieved. In a quickly moving pandemic, it is unclear what hunting for extra sequences of a specific, already identified, variant really does. I'm not sure what public health action would result, especially given the variant has already been identified.

Relatedly, it is unclear to me whether simply relying on spatial distance would not be an alternative simpler approach than mobile phone data. From Figure 2, it seems clear that a simple proximity matrix would work well at reconstructing viral flow. The authors could compare the correlation of spatial, spatial proximity, and CDR data.

Reviewer #2 (Public Review):

Summary:

This research involves conducting experiments to determine the role of Fmnl2 during oocyte meiosis I.

Strengths:

Identifying the role of Fmnl2 during oocyte meiosis I is significant.

Weaknesses:

The quantitative analysis and the used approach to perturb FMNL2 function would benefit from more confirmatory approaches and rigorous analysis.

Comments on revised version:

The authors addressed most of my comments. However, some comments were not addressed convincingly.

My concern is still valid. The authors used only one approach to knockdown FMNL2 which is "siRNA-mediated knockdown". Using an additional approach to inhibit FMNL2 (Trim-Away or morpholino,..) would be beneficial to confirm that the effect of siRNA-mediated knockdown of FMNL2 is specific.

Response 1: In the author's response, they mentioned that successful migration was quantified based on the contact between the spindle pole and the oocyte cortex.<br /> After spindle migration, it is very common for the spindle to be close to (but not in contact with) the cortex for a considerable time. The spindle pole comes in contact with the cortex later (just before anaphase onset and polar body extrusion). Fig. 3A shows an example where at 9 h, the spindle is already migrated but did not come in contact with the cortex until 9:30 h. Based on Fig. 3B,C, the authors assessed spindle migration in fixed oocytes, making it impossible to fix all oocytes at the time of spindle contact with the cortex. Also,<br /> the representative images in Fig. 3C do not show spindle staining to assess the contact between the spindle and the cortex.<br /> Overall, I still believe that the distance between the spindle and the cortex is more accurate for quantifying spindle migration.

Response 2: The authors mentioned, "we made appropriate modifications to the relevant descriptions of immunoprecipitation experiments". I can't find these modifications in the manuscript. The authors need to state clearly that the immunoprecipitation results do not necessarily reflect meiotic oocytes specifically because these experiments were done using the whole ovary which contains both somatic cells and oocytes.

Response 5: The authors mentioned that "Based on our observations, during the extrusion of the first polar body in oocytes, there is a temporary occurrence of cellular morphological fragmentation due to cortical reorganization". Unfortunately, this means that the live imaging system in the authors' laboratory is not ideal for oocyte maturation. Several publications show normal oocyte morphology during cytokinesis. Please delete or replace Fig. 2E.

Reviewer #2 (Public Review):

Summary:

Numerous studies by the authors and other groups have demonstrated an important role for HIV gene expression kidney cells in promoting progressive chronic kidney disease, especially HIV associated nephropathy. The authors had previously demonstrated a role for protein kinase R (PKR) in a non-HIV transgenic model of kidney disease (Okamoto, Commun Bio, 2021). In this study, the authors used innovative techniques including bulk and single nuclear RNAseq to demonstrate that mice expressing a replication-incompetent HIV transgene have prominent dysregulation of mitochondrial gene expression and activation of PKR and that treatment of these mice with a small molecule PKR inhibitor ameliorated the kidney disease phenotype in HIV-transgenic mice. They also identified STAT3 as a key upstream regulator of kidney injury in this model, which is consistent with previously published studies. Other important advances include identifying the kidney cell types that express the HIV transgene and have dysregulation of cellular pathways.

Strengths:

Major strengths of the study include the use of a wide variety of state-of-the-art molecular techniques to generate important new data on the pathogenesis of kidney injury in this commonly used model of kidney disease and the identification of PKR as a potential druggable target for the treatment of HIV-induced kidney disease. The authors also identify a potential novel cell type within the kidney characterized by high expression of mitochondrial genes.

Weaknesses:

Though the HIV-transgenic model used in these studies results in a phenotype that is very similar to HIV-associated nephropathy in humans, the model has several limitations that may prevent direct translation to human disease, including the fact that mice lack several genetic factors that are important contributors to HIV and kidney pathogenesis in humans. Additional studies are therefore needed to confirm these findings in human kidney disease.

Reviewer #2 (Public Review):

Summary:

In this manuscript "Immunogenicity and safety of a live-attenuated SARS-CoV-2 vaccine candidate based on multiple attenuation mechanisms" by Suzuki-Okutani et al., the authors evaluate the attenuation, immunogenicity, and protection efficacy of a live-attenuated SARS-CoV-2 vaccine candidate (BK2102) against SARS-CoV-2.

Strengths:

The authors demonstrate that intranasal inoculation of BK2102 is safe and able to induce humoral and cellular immune responses in hamsters, without apparent signs of damage in the lungs, that protects against homologous SARS-CoV-2 and Omicron BA.5 challenge. Safety of BK2102 was further confirmed in a new hACE2 transgenic mouse model generated by the authors.

Weaknesses:

No major weaknesses were identified, however, this reviewer notes the following:

The authors missed the opportunity to include a mRNA vaccine to demonstrate that the immunity and protection efficacy of their live attenuated vaccine BK2102 is better than a mRNA vaccine.

One of the potential advantages of live-attenuated vaccines is their ability to induce mucosal immunity. It would be great if the authors included experiments to assess the mucosal immunity of their live-attenuated vaccine BK2102.

Reviewer #2 (Public Review):

Summary:

Drawing from tools of synthetic biology, Mihajlovic et al. use a cleverly designed experimental system to dissect Ohno's hypothesis, which describes the evolution of functional novelty on the gene-level through the process of duplication & divergence.

Ohno's original idea posits that the redundancy gained from having two copies of the same gene allows one of them to freely evolve a new function. To directly test this, the authors make use of a fluorescent protein with two emission maxima, which allows them to apply different selection regimes (e.g. selection for green AND blue, or, for green NOT blue). To achieve this feat without being distracted by more complex evolutionary dynamics caused by the frequent recombination between duplicates, the authors employ a well-controlled synthetic system to prevent recombination: Duplicates are placed on a plasmid as indirect repeats in a recombination-deficient strain of E.coli. The authors implement their directed evolution approach through in vitro mutagenesis and selection using fluorescent-activated cell sorting. Their in-depth analysis of evolved mutants in single-copy versus double-copy genotypes provides clear evidence for Ohno's postulate that redundant copies experience relaxed purifying selection. In contrast to Ohno's original postulate, however, the authors go on to show that this does not in fact lead to more rapid phenotypic evolution, but rather, the rapid inactivation of one of the copies.

Strengths:

This paper contributes with great experimental detail to an area where the literature predominantly leans on genomics data. Through the use of a carefully designed, well-controlled synthetic system the authors are able to directly determine the phenotype & genotype of all individuals in their evolving populations and compare differences between genotypes with a single or double copy of coGFP. With it they find clear evidence for what critics of Ohno's original model have termed "Ohno's dilemma", the rapid non-functionalization by predominantly deleterious mutations.

Including an expressed but non-functional coGFP in (phenotypically) single copy genotypes provides an especially thoughtful control that allows determining a baseline dN/dS ratio in the absence of selection. All in all the study is an exciting example of how the clever use of synthetic biology can lead to new insights.

Weaknesses:

The major weakness of the study is tied to its biggest strength (as often in experimental biology there is a trade-off between 'resolution' and 'realism').

The paper ignores an important component of the evolutionary process in favour of an in-depth characterization of how two vs one copy evolve. Specifically, by employing a recombination-deficient strain and constructing their duplicates as inverted repeats their experimental design completely abolishes recombination between the two copies.

This is problematic for two reasons:

i) In nature, new duplicates do not arise as inverted, but rather as direct (tandem) repeats and - as the authors correctly point out - these are very unstable, due to the fact that repeated DNA is prone to recA-dependent homologous recombination (which arise orders of magnitude more frequently than point mutations).

ii) This instability often leads to further amplification of the duplicates under dosage selection both in the lab and in the wild (e.g. Andersson & Hughes, Annu. Rev. Genet. 2009), and would presumably also be an outcome under the current experimental set-up if it was not prevented from happening?

So in sum, recombination between duplicate genes is not merely a nuisance in experiments, but occurring at extremely high frequencies in nature (such that the authors needed to devise a clever engineering solution to abolish it), and is often observed in evolving populations, be it in the laboratory or the wild.

The manuscript sells controlling of copy number as a strength. And clearly, without it, the same insights could not be gained. However, if the basis for the very process of what Ohno's model describes is prevented from happening for the process to be studied, then, for reasons of clarity and context this needs pointing out, especially, to readers less familiar with the principles of molecular evolution.

Connected to this, there are several places in the introduction and the discussion where I feel that the existing literature, in particular models put forward since Ohno that invoke dosage selection (such as IAD) end up being slightly misrepresented.

My point is best exemplified in line 1 of Discussion: "To test Ohno's hypothesis and to distinguish its predictions from those of competing hypotheses, it is necessary to maintain a constant and stable copy number of duplicated genes during experimental evolution."

I think this statement is simply not true and might be misleading. To take the exaggerated position of a devil's advocate, the goal of evolutionary biology should be to find out how evolution actually proceeds in nature most of the time, rather than creating laboratory systems that manage to recapitulate influential ideas.

While fixing copy number may be a necessary step to understand how one copy evolves if a second one is present, it seems that if Ohno's hypothesis only works out in recA-deficient bacterial strains and on engineered inverted repeats, that Ohno might have missed one crucial aspect of how paralogs evolve. The mentioned competing hypotheses have been put forward to (a) address Ohno's dilemma (which the present study beautifully demonstrates exists under their experimental conditions) and (b) to reflect a commonly observed evolutionary process in bacteria (dosage gain in response to selection, e.g. a classic way of gaining antibiotic resistance). Fixing the copy number allowed the authors to show which predictions of Ohno's model hold up and which don't (under these specific conditions). But they do so without even preventing the processes described by alternative models from happening, so the experimental system is hardly appropriate to distinguish between Ohno & alternatives. Therefore, I think it could be made clearer that the experimental system is great to look at certain aspects Ohno's hypothesis in detail, but it can only inform us about a universe without recombination.

(1) Citing the works by ref 8, 26, 27 to merely state that "in some copies were gained and some were lost (ref 6, ref 25)" makes it seem as if fixing at 2 copies is some sort of sensible average. Yet ref 6 (Dhar et al.) specifically states that dosage is the most important response. Moreover, in this study gene copies are lost, but plasmid copies are gained instead. In Holloway et al. 2007 (ref 25), the 2 copies resided on different plasmids, so entirely different underlying molecular genetics might be at work (high cost of plasmid maintenance, and competitive binding on both proteins onto the respective (off)-target, where either way selection favored a single copy, so a different situation altogether). In both cited studies, fixing the copy would have prohibited learning something about the process of duplication & divergence.

Hence this statement seems to distract the readers from the main message, which seems that preventing recombination experimentally allows to follow the divergence of each copy and studying a response that does not involve dosage-increase.

(2) "These studies highlighted the importance of gene duplication in providing fast adaptation under changing environmental conditions but they focused on the importance of gene dosage." I think this constructs a false dichotomy. Instead, these studies pointed out that dosage (and with it, selection for dosage) is an important part of the equation that might have been missed by Ohno.

(3) "Such models are also easier to test experimentally, because they do not require precise control of gene copy number. The necessary tests can even benefit from massive gene amplifications8. Although Ohno's hypothesis is more difficult to test experimentally (...)" - again, I feel the wording is slightly misleading. The point is not that IAD is easier to test and Ohno's model is harder to test in laboratory experiments, rather, experiments (and some more limited observations of naturally evolving populations) seem to suggest that in reality evolution proceeds (more often?) according to IAD rather than Ohno's neofunctionalization hypothesis. However, as the authors point out, it will be exciting to see their clever experimental system used to test other genes and conditions to get a more comprehensive understanding of what gene- and selection- parameter values would overcome Ohno's dilemma.

Reviewer #2 (Public Review):

Centrosomes are an integral part of cell division in most animal cells. There are notable exceptions, however, such as oocytes and plants. In addition, some animal cells can be engineered to lack centrosomes yet they can still manage to complete mitosis. This paper uses a couple of methods (PLK4 inhibition and deletion of SASS6) to remove centrosomes from an immortalized cell line. Indeed, a strength of the paper is that similar results are obtained using both protocols to generate acentrosomal cells. The authors find acentrosomal cells take longer to divide, mostly due to a longer metaphase. The paper is based on the finding that inhibition of MPS1 results in a failure to divide, and the hypothesis that a SAC - dependent delay is required for these acentrosomal cells to divide.

The finding that MPS1 inhibition results in a failure to division is interesting. This is investigated by analyzing cells where AurB, APC or Eg5 (to generate monastral spindles) have been inhibited. My concerns are that the results are not conclusive that the effect of MPS1 is on cell cycle regulation. There is not enough data to make a conclusion as to why inhibition of MPS1 results in cell division failure.

1) An example is how to interpret the effect of Aurora B inhibition, which does not block acentrosomal cell division. If Aurora B is required for SAC activity, it suggests this effect of MPS1 may be a function other than SAC. Given the complexity of the SAC, it would be informative to test other SAC components. Instead, the authors conclude that the mitotic delay caused by MPS is required for acentrosomal cell division. I don't think they have ruled out, or even addressed other functions of MPS1.

2) The authors find that when both the APC and MPS1 are inhibited, the cells eventually divide. These results are intriguing, but hard to interpret. The authors suggest that the failure to divide in MPS1-inhibited cells is because they enter anaphase, and then must back out. This is hard to understand and there is not data supporting some kind of aborted anaphase. Is the division observed with double inhibition some sort of bypass of the block caused by MPS1 inhibition alone? It is not clear why inhibition of APC causes increased cell division when MPS1 is inhibited.

3) The authors characterize MTOC formation in these cells, which is also interesting. MTOCs are established after NEB in acentrosomal cells. Indeed, forming these MTOCs is probably a key mechanism for how these cells complete a division, like mouse oocytes.

Following this, the results with inhibiting Eg5 are interesting. The double inhibition of MPS1 and Eg5 results in division failure, like MPS1 inhibition in acentrosomal cells. Thus, there is a cell division block when the centrioles fail to divide. This result raises the possibility that failure to make a bipolar spindle, or the presence of a monopolar spindle, is the problem. In the absence of a bipolar spindle, a SAC induced delay is required for spindle assembly. This is a possibility but there are multiple interpretations of these results. Primarily, these results do not show the MPS1 effect on acentrosomal cells is SAC related. That a SAC mediated delay is required for acentrosmomal spindle assembly is not the only conclusion.

Comments on revised version:

It appears that very few changes have been made. These are all suggestions in the writing and interpretation.

It's disappointing the most of the readouts are cell division success. There is a lack of data about what happens in the MPS1 knockdowns, such as microtubule attachment to KTs and localization/ activity of checkpoint proteins or downstream factors. More mechanistic insights may be found by testing other checkpoint proteins or assaying more metrics for spindle assembly and cell cycle progression. Or if inducing cell cycle delay suppresses the MPS1 effect. These experiments would implicate cell cycle factors as being required for acentrosomal spindle assembly while ruling out a requirement for MPS1 in spindle assembly.

The paper is well written. But some of the terminology could be improved and some descriptions of the cytology are confusing. Some clear definitions of terms may help. The authors refer to an "extended mitosis" (line 73) and then "exit in the absence of cell division" (line 96) when MPS1 is inhibited. Both are misleading and don't tell the full story. These cells attempt to divide and then fail, resulting in one cell. Use of terms like "spread back out", "rounding up", and "sitting down" seems like jargon and should at least be defined. The term "timely two-ness" (line 23-24) is also not helpful. A brief discussion of data on MPS1 function in mouse and fly acentrosomal meiosis might be appropriate. A comparison would be interesting since loss of MPS1 in acentrosomal oocytes does not have such a drastic block in cell division.

Reviewer #2 (Public Review):

Summary:

This study reveals that short-term social isolation increases social behavior at a reunion, and a population of hypothalamic preoptic area neurons become active after social interaction following short-term isolation (POAiso neurons). Effectively utilizing a TRAP activity-dependent labeling method, the authors inhibit or activate the POAiso neurons and find that these neurons are involved in controlling various social behaviors, including ultrasonic vocalization, investigation, and mounting in both male and female mice. This work suggests a complex role for the POA in regulating multiple aspects of social behavior, beyond solely controlling male sexual behaviors.

Strengths:

A few studies have shown that optogenetic activation of the POA in females promotes vocalization and mounting behavior, similar to the effects observed in males. However, those were the results of artificially stimulating POA neurons, and it was unknown whether POA neurons play a role in naturally occurring female social behaviors. This paper clearly demonstrates that there exists a population of POA neurons that are necessary for naturally evoked female social vocalizations and mounting behaviors.

Weaknesses:

The authors conclude that "In the current study, we identify and characterize a population of preoptic hypothalamic neurons that contribute to the effects of short-term social isolation on the social behaviors of mice." This is an interesting hypothesis, but in my opinion, critical control experiments are missing to support this claim.

All the activity-dependent labeling experiments with TRAP mice, including the subsequent neural activity manipulation experiments (Figures 2, 3, 4, 5E-F), were conducted by labeling neurons only in socially isolated animals, not group-housed animals. The authors labeled neurons after 30-minute social interactions, raising the possibility that the labeled neurons simply represent a "social interaction/behavior population" (mediating mounting and USVs in females and males) rather than a set of neurons specific to social isolation.

I strongly recommend including experimental groups that involve labeling neurons after 30-minute social interactions in group-housed female or male mice and inhibit TRAPed neurons after social isolation or activate TRAPed neurons after group housing. If manipulating the group-housed TRAP neurons has similar effects to manipulating the isolated TRAP neurons, it would suggest the current labeling paradigm is not isolating neurons specific to the effect of social isolation per se. Rather, the neurons may mediate more general social interaction or motivation-related activities. Given the known role of POA in male mating behavior, a group-housed TRAP experiment in males with a female visitor is especially important for understanding the selectivity of the labeled cells.

Without proper controls, referring to the labeled neurons as "POAiso" neurons is potentially misleading. The data thus far suggests these neurons may predominantly reflect a "POA social behavior" population rather than a set of cells distinctly responsive to isolated housing.

Overall, this paper is well-written and provides valuable new data on the neural circuit for female social behaviors and the potentially complex role of POA in social behavior control.

Reviewer #2 (Public Review):

The paper has two main merits. Firstly, it documents a new and important characteristic of the re-organization of the brains of the deaf, namely its variability. The search for a well-defined set of functions for the deprived auditory cortex of the deaf has been largely unsuccessful, with several task-based approaches failing to deliver unanimous results. Now, one can understand why this was the case: most likely there isn't a fixed one well-defined set of functions supported by an identical set of areas in every subject, but rather a variety of functions supported by various regions. In addition, the paper extends the authors' previous findings from blind subjects to the deaf population. It demonstrates that the heightened variability of connectivity in the deprived brain is not exclusive to blindness, but rather a general principle that applies to other forms of deprivation. On a more general level, this paper shows how sensory input is a driver of the brain's reproducible organization.

The method and the statistics are sound, the figures are clear, and the paper is well-written. The sample size is impressively large for this kind of study.

The main weakness of the paper is not a weakness, but rather a suggestion on how to provide a stronger basis for the authors' claims and conclusions. I believe this paper could be strengthened by including in the analysis at least one of the already published deaf/hearing resting-state fMRI datasets (e.g. Andin and Holmer, Bonna et al., Ding et al.) to see if the effects hold across different deaf populations. The addition of a second dataset could strengthen the evidence and convincingly resolve the issue of whether delayed sign language acquisition causes an increase in individual differences in functional connectivity to/from Broca's area. Currently, the authors may not have enough statistical power to support their findings.

Secondly, the authors could more explicitly discuss the broad implications of what their results mean for our understanding of how the architecture of the brain is determined by the genetic blueprint vs. how it is determined by learning (page 9). There is currently a wave of strong evidence favoring a more "nativist" view of brain architecture, for example, face- and object- sensitive regions seem to be in place practically from birth (see e.g. Kosakowski et al., Current Biology, 2022). The current results show what is the role played by experience.

Reviewer #2 (Public Review):

Summary:

In the present work, the authors present an engineering solution to sample preparation in 96-well plates for high-throughput super-resolution microscopy via Expansion Microscopy. This is not a trivial problem, as the well cannot be filled with the gel, which would prohibit the expansion of the gel. A device was engineered that can spot a small droplet of hydrogel solution and keep it in place as it polymerizes. It occupies only a small portion of space at the center of each well, the gel can expand into all directions, and imaging and staining can proceed by liquid handling robots and an automated microscope.

Strengths:

In contrast to Reference 8, the authors' system is compatible with standard 96 well imaging plates for high-throughput automated microscopy and automated liquid handling for most parts of the protocol. They thus provide a clear path towards high-throughput exM and high-throughout super-resolution microscopy, which is a timely and important goal.

Weaknesses:

The assay they chose to demonstrate what high-throughput ExM could be useful for, is not very convincing. But for this reviewer that is not important.

Reviewer #2 (Public Review):

Summary:

This paper evaluates the effect of COVID-19 booster vaccination on reinfection in Shanghai, China among individuals who received primary COVID-19 vaccination followed by initial infection, during an Omicron wave.

Strengths:

A large database is collated from electronic vaccination and infection records. Nearly 200,000 individuals are included in the analysis and 24% became reinfected.

Weaknesses:

The article is difficult to follow in terms of the objectives and individuals included in various analyses. There appear to be important gaps in the analysis. The electronic data are limited in their ability to draw causal conclusions.

More detailed comments:

In multiple places (abstract, introduction), the authors frame the work in terms of understanding the benefit of booster vaccination among individuals with hybrid immunity (vaccination + infection). However, their analysis population does not completely align with this framing. As best as I can tell, only individuals who first received COVID-19 vaccination, and subsequently experienced infection, were included. Why the analysis does not also consider individuals who were infected and then vaccinated is not clear.

In vaccine effectiveness analyses, why was time since initial infection not examined as a modifier of the booster effect? Time since the onset of the Omicron wave is only loosely tied to the immune status of the individual.

The effect of booster vaccination on preventing symptomatic vs. asymptomatic reinfection does not appear to have been evaluated; this is a key gap in the analysis and it would seem the data would support it.

In lines 105-108, the demographic description of the analysis population is incomplete. Is sex or gender identity being described? Are any individuals non-binary? What is the age distribution? (Only the proportions 20-39 and under 6 are stated.)

Figure 1 consort diagram is confusing. In the last row, are the two boxes independent or overlapping sets of individuals? Are all included in secondary analyses?

Reviewer #2 (Public Review):

Summary:

Birnavirus replication factories form alongside early endosomes (EEs) in the host cell cytoplasm. Previous work from the Delgui lab has shown that the VP3 protein of the birnavirus strain infectious bursal disease virus (IBDV) interacts with phosphatidylinositol-3-phosphate (PI3P) within the EE membrane (Gimenez et al., 2018, 2020). Here, Zanetti et al. extend this previous work by biochemically mapping the specific determinants within IBDV VP3 that are required for PI3P binding in vitro, and they employ in silico simulations to propose a biophysical model for VP3-PI3P interactions.

Strengths:

The manuscript is generally well-written, and much of the data is rigorous and solid. The results provide deep knowledge into how birnaviruses might nucleate factories in association with EEs. The combination of approaches (biochemical, imaging, and computational) employed to investigate VP3-PI3P interactions is deemed a strength.

Weaknesses:

(1) Concerns about the sources, sizes, and amounts of recombinant proteins used for co-flotation: Figures 1A, 1B, 1G, and 4A show the results of co-flotation experiments in which recombinant proteins (control His-FYVE v. either full length or mutant His VP3) were either found to be associated with membranes (top) or non-associated (bottom). However, in some experiments, the total amounts of protein in the top + bottom fractions do not appear to be consistent in control v. experimental conditions. For instance, the Figure 4A western blot of His-2xFYVE following co-flotation with PI3P+ membranes shows almost no detectable protein in either top or bottom fractions. Reading the paper, it was difficult to understand which source of protein was used for each experiment (i.e., E. coli or baculovirus-expressed), and this information is contradicted in several places (see lines 358-359 v. 383-384). Also, both the control protein and the His-VP3-FL proteins show up as several bands in the western blots, but they don't appear to be consistent with the sizes of the proteins stated on lines 383-384. For example, line 383 states that His-VP3-FL is ~43 kDa, but the blots show triplet bands that are all below the 35 kDa marker (Figures 1B and 1G). Mass spectrometry information is shown in the supplemental data (describing the different bands for His-VP3-FL) but this is not mentioned in the actual manuscript, causing confusion. Finally, the results appear to differ throughout the paper (see Figures 1B v. 1G and 1A v. 4A).

(2) Possible "other" effects of the R200D mutation on the VP3 protein. The authors performed mutagenesis to identify which residues within patch 2 on VP3 are important for association with PI3P. They found that a VP3 mutant with an engineered R200D change (i) did not associate with PI3P membranes in co-floatation assays, and (ii) did not co-localize with EE markers in transfected cells. Moreover, this mutation resulted in the loss of IBDV viability in reverse genetics studies. The authors interpret these results to indicate that this residue is important for "mediating VP3-PI3P interaction" (line 211) and that this interaction is essential for viral replication. However, it seems possible that this mutation abrogated other aspects of VP3 function (e.g., dimerization or other protein/RNA interactions) aside from or in addition to PI3P binding. Such possibilities are not mentioned by the authors.

(3) Interpretations from computational simulations. The authors performed computational simulations on the VP3 structure to infer how the protein might interact with membranes. Such computational approaches are powerful hypothesis-generating tools. However, additional biochemical evidence beyond what is presented would be required to support the authors' claims that they "unveiled a two-stage modular mechanism" for VP3-PI3P interactions (see lines 55-59). Moreover, given the biochemical data presented for R200D VP3, it was surprising that the authors did not perform computational simulations on this mutant. The inclusion of such an experiment would help tie together the in vitro and in silico data and strengthen the manuscript.

Reviewer #2 (Public Review):

In the manuscript, the authors highlighted the importance of T-cell receptor (TCR) analysis and the lack of amino acid embedding methods specific to this domain. The authors proposed a novel bi-directional context-aware amino acid embedding method, catELMo, adapted from ELMo (Embeddings from Language Models), specifically designed for TCR analysis. The model is trained on TCR sequences from seven projects in the ImmunoSEQ database, instead of the generic protein sequences. They assessed the effectiveness of the proposed method in both TCR-epitope binding affinity prediction, a supervised task, and the unsupervised TCR clustering task. The results demonstrate significant performance improvements compared to existing embedding models. The authors also aimed to provide and discuss their observations on embedding model design for TCR analysis: 1) Models specifically trained on TCR sequences have better performance than models trained on general protein sequences for the TCR-related tasks; and 2) The proposed ELMo-based method outperforms TCR embedding models with BERT-based architecture. The authors also provided a comprehensive introduction and investigation of existing amino acid embedding methods. Overall, the paper is well-written and well-organized.

The work has originality and has potential prospects for immune response analysis and immunotherapy exploration. TCR-epitope pair binding plays a significant role in T cell regulation. Accurate prediction and analysis of TCR sequences are crucial for comprehending the biological foundations of binding mechanisms and advancing immunotherapy approaches. The proposed embedding method presents an efficient context-aware mathematical representation for TCR sequences, enabling the capture and analysis of their structural and functional characteristics. This method serves as a valuable tool for various downstream analyses and is essential for a wide range of applications.

Reviewer #2 (Public Review):

Summary:

Franke et al. characterize the representation of color in the primary visual cortex of mice, highlighting how this changes across the visual field. Using calcium imaging in awake, head-fixed mice, they characterize the properties of V1 neurons (layer 2/3) using a large center-surround stimulation where green and ultra-violet colors were presented in random combinations. Clustering of responses revealed a set of functional cell-types based on their preference to different combinations of green and UV in their center and surround. These functional types were demonstrated to have different spatial distributions across V1, including one neuronal type (Green-ON/UV-OFF) that was much more prominent in the posterior V1 (i.e. upper visual field). Modelling work suggests that these neurons likely support the detection of predator-like objects in the sky.

Strengths:

The large-scale single-cell resolution imaging used in this work allows the authors to map the responses of individual neurons across large regions of the visual cortex. Combining this large dataset with clustering analysis enabled the authors to group V1 neurons into distinct functional cell types and demonstrate their relative distribution in the upper and lower visual fields. Modelling work demonstrated the different capacity of each functional type to detect objects in the sky, providing insight into the ethological relevance of color opponent neurons in V1.

Weaknesses:

While the study presents convincing evidence about the asymmetric distribution of color-opponent neurons in V1, the paper would greatly benefit from a more in-depth discussion of the caveats related to the conclusions drawn about their origin. This is particularly relevant regarding the conclusion drawn about the contribution of color opponent neurons in the retina. The mismatch between retinal color opponency and V1 color opponency could imply that this feature is not solely inherited from the retina, however, there are other plausible explanations that are not discussed here. Direct evidence for this statement remains weak.

In addition, the paper would benefit from adding explicit neuron counts or percentages to the quadrants of each of the density plots in Figures 2-5. The variance explained by the principal components does not capture the percentage of color opponent cells. Additionally, there appear to be some remaining errors in the figure legend and labels that have not been addressed (e.g. '??' in Fig 2 legend).

Overall, this study will be a valuable resource for researchers studying color vision, cortical processing, and the processing of ethologically relevant information. It provides a useful basis for future work on the origin of color opponency in V1 and its ethological relevance.

Reviewer #2 (Public Review):

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

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

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

Comments on revised version:

I want to thank the authors for their thorough and comprehensive work in revising this manuscript. I agree with the authors that learning paradigms might not be a necessity when it comes to study the PE signals, but I don't particularly agree with some of the responses in the rebuttal letter ("Furthermore, conditioning paradigms generally only include one level of aversive outcome: the electrical stimulation is either delivered or omitted."). This is of course correct description for the conditioning paradigm, but the same can be said for an instructed design: the aversive outcome was either delivered or not. That being said, adopting the instructed design itself is legitimate in my opinion.

My main concern, which the authors spent quite some length in the rebuttal letter to address, still remains about the validity for different instructed probabilities. Although subjects were told that the trials were independent, the big difference between 75% and 25% would more than likely confuse the subjects, especially given that most of us would fall prey to the Gambler's fallacy (or the law of small numbers) to some degree. When the instruction and subjective experience collides, some form of inference or learning must have occurred, making the otherwise straightforward analysis more complex. Therefore, I believe that a more rigorous/quantitative learning modeling work can dramatically improve the validity of the results. Of course, I also realize how much extra work is needed to append the computational part but without it there is always a theoretical loophole in the current experimental design.

As the authors mentioned in the rebuttal letter, "selecting participants only if their anticipatory SCR monotonically increased with each increase in instructed probability 0% < 25% < 50% < 75% < 100%, N = 11 participants", only ~1/3 of the subjects actually showed strong evidence for the validity of the instructions. This further raises the question of whether the instructed design, due to the interference of false instruction and the dynamic learning among trials, is solid enough to test the hypothesis.

Reviewer #2 (Public Review):

Summary:

To identify sugar receptors and assess the capacity of these genes the authors first set out to identify behavioral responses in larva and adult as well as physiological response. They used phylogenetics and gene expression (RNAseq) to identify candidates for sugar reception. Using first an in vitro oocyte system they assess the responses to distinct sugars. A subsequent genetic analysis shows that the Gr10 and Gr6 genes provide stage specific functions in sugar perception.

Strengths:

A clear strength of the manuscript is the breadth of techniques employed allowing a comprehensive study in a non-canonical model species.

Weaknesses:

There are no major weaknesses in the study for the current state of knowledge in this species. Since it is much basic work to establish a broader knowledge, context with other modalities remain unknown. It might have been possible to probe certain context known from the fruit fly, which would have strengthened the manuscript.

Reviewer #2 (Public Review):

Summary:

In this manuscript, Shen and collaborators described the generation of conditional double knockout (cDKO) mice lacking LRRK1 and LRRK2 selectively in DAT-positive dopaminergic 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, cDKO mice did not replicate the dramatic increase in autophagic vacuole numbers. The study supports the authors' hypothesis that loss of function rather than gain of function of LRRK2 leads to Parkinson's Disease.

Strengths:

For the first time, the study described a model in which both the Parkinson's disease-associated gene LRRK2 and its homolog LRRK1 are deleted selectively in dopaminergic neurons. This offers a new tool to understand the physiopathological role of LRRK2 and the compensating role of LRRK1 in modulating dopaminergic 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 Parkinson's disease. The evidence of a Parkinsonian phenotype in these conditional knockout mice is limited and should be considered preliminary.

Reviewer #2 (Public Review):

In this manuscript, the authors set out to identify transporters that must exist in Stramenophiles due to the fact that the second half of glycolysis appears to be conducted in the mitochondria. They hypothesize that a Stramenophile-specific clade of transporters related to the dicarboxylate carriers are likely the relevant family and then go on to test two proteins from Blastocystis due to the infectious disease relevance of this organism. They show rather convincingly that these two proteins are expressed and are localized to the mitochondria in the native organism. The purified proteins bind to glycolytic intermediates and one of them, GIC-2, transports several glycolytic intermediates in vitro. This is a very solid and well-executed study that clearly demonstrates that bCIC-2 can transport glycolytic intermediates.

(1) The major weakness is that the authors aren't able to show that this protein actually has this function in the native organism. This could be impossible due to the lack of genetic tools in Blastocystis, but it leaves us without absolute confidence that bGIC-2 is the important glycolytic intermediate mitochondrial transporter (or even that it has this function in vivo).

(2) My impression is that the authors under-emphasize the fact that the hDIC also binds (and is stabilized by) glycolytic intermediates (G3P and 3PG). In the opinion of this reviewer, this might change my interpretation about the uniqueness of the bGIC proteins. They act on additional glycolytic intermediates, but it's not unique.

Reviewer #2 (Public Review):

The authors aim to better understand the neural responses to Shepard tones in auditory cortex. This is an interesting question as Shepard tones can evoke an ambiguous pitch that is manipulated by a proceeding adapting stimulus, therefore it nicely disentangles pitch perception from simple stimulus acoustics.

The authors use a combination of computational modelling, ferret A1 recordings of single neurons, and human EEG measurements.

Their results provide new insights into neural correlates of these stimuli. However, the manuscript submitted is poorly organized, to the point where it is near impossible to review. We have provided Major Concerns below. We will only be able to understand and critique the manuscript fully after these issues have been addressed to improve the readability of the manuscript. Therefore, we have not yet reviewed the Discussion section.

Major concerns

Organization/presentation<br /> The manuscript is disorganized and therefore difficult to follow. The biggest issue is that in many figures, the figure subpanels often do not correspond to the legend, the main body, or both. Subpanels described in the text are missing in several cases. Many figure axes are unlabelled. There is an inconsistent style of in-text citation between figures and the main text. The manuscript contains typos and grammatical errors. My suggestions for edits below therefore should not be taken as an exhaustive list. I ask the authors to consider the following only a "first pass" review, and I will hopefully be able to think more deeply about the science in the second round of revisions after the manuscript is better organized.

Frequency and pitch<br /> The terms "frequency" and "pitch" seem to be used interchangeably at times, which can lead to major misconceptions in a manuscript on Shepard tones. It is possible that the authors confuse these concepts themselves at times (e.g. Fig 5), although this would be surprising given their expertise in this field. Please check through every use of "frequency" and "pitch" in this manuscript and make sure you are using the right term in the right place. In many places, "frequency" should actually be "fundamental frequency" to avoid misunderstanding.

Insufficient detail or lack of clarity in descriptions<br /> There seems to be insufficient information provided to evaluate parts of these analysis, most critically the final pitch-direction decoder (Fig 6), which is a major finding. Please clarify.

Reviewer #2 (Public Review):

Summary:

In this manuscript, Peng et al., reported that 36THz high-frequency terahertz stimulation (HFTS) can suppress the activity of pyramidal neurons by enhancing the conductance of voltage-gated potassium channel. The authors also demonstrated the effectiveness of using 36THz HFTS for treating neuropathic pain.

Strengths:

The manuscript is well written and the conclusions are supported by robust results. This study highlighted the potential of using 36THz HFTS for neuromodulation.

Weaknesses:

More characterization of HFTS is needed, so the readers can have a better assessment of the potential usage of HFTS in their own applications.

(1) It would be very helpful to estimate the volume of tissue that can be influenced by HFTS. It is not clear how 15 mins HFTS was chosen for this functional study. Does a longer time have a stronger effect? A better characterization of the relationship between the stimulus duration of HFTS and its beneficial effects would be very useful.

(2) How long does the behavioral effect last after 15 minutes of HFTS? Figure 5b only presents the behavioral effect for one hour, but the pain level is still effectively reduced at this time point. The behavioral measurement should last until pain sensitization drops back to pre-stim level.

(3) Although the manuscript only tested in ACC, it will also be useful to demonstrate the neural modulation effect on other brain regions. Would 36THz HFTS also robustly modulate activities in other brain regions? Or are different frequencies needed for different brain regions?

Reviewer #2 (Public Review):

Summary:

The manuscript by Hou et al is a short technical report which details the potential use of a recently developed FRET based biosensor for gamma-secretase activity (Houser et al 2020) for in vivo imaging in the mouse brain. Gamma-secretase plays a crucial role in Alzheimer disease pathology and therefore developing methodologies for precise in vivo measurements would be highly valuable to better understand AD pathophysiology in animal models.

The current version of the sensor utilizes a pair of far-red fluorescent proteins fused to a substrate of the enzyme. Using live imaging, it was previously demonstrated it is possible to monitor gamma-secretase activity in cultured cells. Notably, this is a variant of a biosensor that was previously described using CFP-YFP variants FRET pair (Maesako et al, iScience. 2020). The main claim and hypothesis for the MS is that IR excitation and emission has considerable advantages in terms of depth of penetration, as well as reduction in autofluorescence. These properties would make this approach potentially suitable to monitor cellular level dynamics of Gama-secretase in vivo.

The authors use confocal microscopy and show it is possible to detect fluorescence from single cortical cells. The paper described in detail technical information regarding imaging and analysis. The data presented in figures 5-8 details analysis of FRET ratio (FR) measurements within populations of cells. The authors claim it is possible to obtain reliable measurements at the level of individual cells. They compare the FR values across cells and mice and find a spatial correlation among neighboring cells. This is compared with data obtained after inhibition of endogenous gamma-secretase activity, which abolishes this correlation.

Strengths:

The authors describe in detail their experimental design and analysis for in vivo imaging of the reporter. The idea of using a far-red FRET sensor for in vivo imaging is novel and potentially useful to circumvent many of the pitfalls associated with intensity-based FRET imaging in complex biological environments (such as autofluorescence and scattering).

Weaknesses:

There are several critical points regarding validation of this approach and concerns with the data presented that must be addressed:

(1) Regarding the variability and spatial correlation- the dynamic range of the sensor previously reported in vitro is in the range of 20-30% change (Houser et al 2020) whereas the range of FR detected in vivo is between cells is significantly larger (Fig. 3). This raises considerable doubts for specific detection of cellular activity (see point 3).<br /> (2) One direct way to test the dynamic range of the sensor in vivo, is to increase or decrease endogenous gamma-secretase activity and to ensure this experimental design allows to accurately monitor gamma-secretase activity. In the previous characterization of the reporter (Hauser et al 2020), DAPT application and inhibition of gamma-secretase activity results in increased FR (Figures 2 and 3 of Houser et al). This is in agreement with the design of the biosensor, since FR should be inversely correlated with enzymatic activity. Here, while the authors repeat the same manipulation and apply DAPT to block gamma-secretase activity, it seems to induce the opposite effect and reduces FR (comparing figures 8 with figures 5,6,7). First, there is no quantification comparing FR with and without DAPT. Moreover, it is possible to conduct this experiment in the same animals, meaning comparing FR before and after DAPT in the same mouse and cell populations. This point is absolutely critical- if indeed FR is reduced following DAPT application, this needs to be explained since this contradicts the basic design and interpretation of the biosensor.<br /> (3) For further validation, I would suggest including in vivo measurements with a sensor version with no biological activity as a negative control, for example, a mutation that prevents enzymatic cleavage and FRET changes. This should be used to showcase instrumental variability and would help to validate the variability of FR is indeed biological in origin. This would significantly strengthen the claims regarding spatial correlation within population of cells.<br /> (4) In general, confocal microcopy is not ideal for in vivo imaging. Although the authors demonstrate data collected using IR imaging increases penetration depth, out of focus fluorescence is still evident (Figure 4). Many previous papers have primarily used FLIM based analysis in combination with 2p microscopy for in vivo FRET imaging (Some examples: Ma et al, Neuron, 2018; Massengil et al, Nature methods, 2022; DIaz-Garcia et al, Cell Metabolism, 2017; Laviv et al, Neuron, 2020). This technique does not rely on absolute photon number and therefore has several advantage sin terms of quantification of FRET signals in vivo.<br /> It is therefore likely that use of previously developed sensors of gamma-secretase with conventional FRET pairs, might be better suited for in vivo imaging. This point should be at least discussed as an alternative.

Reviewer #2 (Public Review):

Summary:

Naïve CD4 T cells in CD11c-Cre p28-floxed mice express highly elevated levels of proinflammatory IFNg and the transcription factor T-bet. This phenotype turned out to be imposed by thymic dendritic cells (DCs) during CD4SP T cell development in the thymus [PMID: 23175475]. The current study affirms these observations, first, by developmentally mapping the IFNg dysregulation to newly generated thymic CD4SP cells [PMID: 23175475], second, by demonstrating increased STAT1 activation being associated with increased T-bet expression in CD11c-Cre p28-floxed CD4 T cells [PMID: 36109504], and lastly, by confirming IL-27 as the key cytokine in this process [PMID: 27469302]. The authors further demonstrate that such dysregulated cytokine expression is specific to the Th1 cytokine IFNg, without affecting the expression of the Th2 cytokine IL-4, thus proposing a role for thymic DC-derived p28 in shaping the cytokine response of newly generated CD4 helper T cells. Mechanistically, CD4SP cells of CD11c-Cre p28-floxed mice were found to display epigenetic changes in the Ifng and Tbx21 gene loci that were consistent with increased transcriptional activities of IFNg and T-bet mRNA expression. Moreover, in autoimmune Aire-deficiency settings, CD11c-Cre p28-floxed CD4 T cells still expressed significantly increased amounts of IFNg, exacerbating the autoimmune response and disease severity. Based on these results, the investigators propose a model where thymic DC-derived IL-27 is necessary to suppress IFNg expression by CD4SP cells and thus would impose a Th2-skewed predisposition of newly generated CD4 T cells in the thymus, potentially relevant in autoimmunity.

Strengths:

Experiments are well-designed and executed. The conclusions are convincing and supported by the experimental results.

Weaknesses:

The premise of the current study is confusing as it tries to use the CD11c-p28 floxed mouse model to explain the Th2-prone immune profile of newly generated CD4SP thymocytes. Instead, it would be more helpful to (1) give full credit to the original study which already described the proinflammatory IFNg+ phenotype of CD4 T cells in CD11c-p28 floxed mice to be mediated by thymic dendritic cells [PMID: 23175475], and then, (2) build on that to explain that this study is aimed to understand the molecular basis of the original finding.

In its essence, this study mostly rediscovers and reaffirms previously reported findings, but with different tools. While the mapping of epigenetic changes in the IFNg and T-bet gene loci and the STAT1 gene signature in CD4SP cells are interesting, these are expected results, and they only reaffirm what would be assumed from the literature. Thus, there is only incremental gain in new insights and information on the role of DC-derived IL-27 in driving the Th1 phenotype of CD4SP cells in CD11c-p28 floxed mice.

Altogether, the major issues of this study remain unresolved:

(1) It is still unclear why the p28-deficiency in thymic dendritic cells would result in increased STAT1 activation in CD4SP cells. Based on their in vitro experiments with blocking anti-IFNg antibodies, the authors conclude that it is unlikely that the constitutive activation of STAT1 would be a secondary effect due to autocrine IFNg production by CD4SP cells. However, this possibility should be further tested with in vivo models, such as Ifng-deficient CD11c-p28 floxed mice. Alternatively, is this an indirect effect by other IFNg producers in the thymus, such as iNKT cells? It is necessary to explain what drives the STAT1 activation in CD11c-p28 floxed CD4SP cells in the first place.

(2) It is also unclear whether CD4SP cells are the direct targets of IL-27 p28. The cell-intrinsic effects of IL-27 p28 signaling in CD4SP cells should be assessed and demonstrated, ideally by CD4SP-specific deletion of IL-27Ra, or by establishing bone marrow chimeras of IL-27Ra germline KO mice.

Reviewer #2 (Public Review):

Summary:

This valuable study characterizes the requirement for individual let-7 clusters to limit the generation of IL-17 producing CD8 T cells and the severity of emphysema in mouse models. Mature let-7 family miRNAs originate from multiple loci, several of which have been reported and/or are reported here to be downregulated in emphysematous lung tissue and/or lung T cells. The results provided are convincing but incomplete, as the let-7 cluster with the most convincing effects on T cell cytokine production is not tested for effects on disease pathogenesis.

Let-7 family miRNAs are largely redundant in function and originate from multiple genomic loci ("clusters"). Erice et al demonstrate that two individual clusters (let7afd and let7bc2) in mice regulate the generation of IL-17 producing CD8 T cells in vitro and in vivo in a model of emphysema. These cells also express higher levels of the IL-17-inducing transcription factor RORgt, encoded by Rorc, which the authors demonstrate to be a direct target of let-7. Since multiple let-7 family miRNAs are downregulated in T cells and lung tissue in emphysema, these data support a model in which reduced let-7 allows increased IL-17 production by T cells, contributing to disease pathogenesis.

Strengths:

The inclusion of miRNA and pri-miRNA expression data from sorted human lung T cells as well as mouse T cells from an emphysema model is a strength.

The study includes complementary loss of function and gain of function experimental systems to test the effect of altered let-7 function, though it should be noted that these involved different let-7 family members and did not yield simple, complementary results for all experimental outcomes.

The most important finding is that deletion of just one let-7 cluster ("Let7bc2") is sufficient to exacerbate emphysema in the nCB and CS models.

Weaknesses:

The human miRNA expression data that motivate functional analyses used sorted CD4+ T cells. The authors note that prior work on let-7 showed that it regulates Th17 (CD4) responses, yet this study's functional analyses are all focused on Tc17 (CD8) T cells. Data in this paper show that Tc17 cells are far less numerous than Th17 cells in the nCB and CS models of emphysema.

Compared with Let7bc2 deletion, Let7afd deletion had a much larger effect on IL17 production by CD8 T cells in vitro, and it also had a larger effect on RORgt expression in untreated mice in vivo, especially in the lung. In the revised manuscript, the authors show that let7afdLOF mice have normal numbers of CD4 and CD8 T cells in the thymus and peripheral lymphoid organs and do not exhibit lung histopathology or inflammatory changes at baseline at least up to 6 months of age. As such, they are set up perfectly to test the requirement for Let7afd in the nCB and/or CS models. These experiments would add strength to the core novelty of this work - demonstration of the functional importance of individual let-7 clusters.

The authors could do more to explain the complexity of the let7 miRNA family and the genomic clusters examined in this study. In particular, it would help to know the relationship between mouse Let7bc2 and corresponding human Let7 clusters. It would also be very helpful to know the relative expression of each mature let-7 family member in Tc17 cells. Are mature miRNAs derived from the Let7afd cluster more or less abundant?

The provided evidence for the effect of Let7GOF has an important caveat that came to light during review. Let7g overexpression caused a marked reduction in Rorgt expression in T cells at baseline and in the setting of nCB challenge, and it reduced the frequency of IL17+ producing CD8 T cells in the lung to baseline levels. Yet there was no change in the MLI measurement of histopathology. However, the responses in the experiment shown in Fig. 6C-D are quite muted compared to those shown in Figure 2. In the response to reviewers, the authors speculate that an anti-inflammatory of doxycycline, required for induction of Let7g in this model, "could account for the differences in the magnitude of emphysemic response".

Although RORgt is a great candidate to have direct effects on IL-17 expression, the mechanistic understanding of let-7 action on T cell differentiation and cytokine production is limited to this single target. As noted in the discussion, others have identified cytokine receptor targets that may play a role, but it is also likely others among the many targets of let-7 also contribute.

Reviewer #2 (Public Review):

The manuscript investigates the connections between the ubiquitin ligase protein deltex and the wingless pathway. Two different connections are proposed, one is function of deltex to modulate the gradient of wingless diffusion and hence modulate the spatial patter of wingless pathway targets, which regulate at different thresholds of wingless concentration. The second is a direct interaction between deltex and armadillo, a downstream component of the wingless pathway. Deltex is proposed to cause the degradation of armadillo resulting in suppression of wingless pathway activity. The results and conclusions of the manuscript are interesting and for the most part novel, although previously published work linking Notch and deltex to wingless signal regulation, and endocytosis to wingless gradient formation could be more extensively discussed. However neither of the two parts to the manuscript seem, in themselves sufficiently complete, and combining both parts together therefore seems to lack focus.

The main issue with the manuscript is that much of the conclusions are inferred from genetic interactions in vivo between loss of function mutants and overexpression. While providing useful in vivo physiological context, this type of approach struggles to be able to make definitive conclusions on whether an interaction is due to direct or indirect mechanism, as the authors themselves conclude at the end of section 2.3. The problem is confounded by the fact that there is already documented much cross talk between the Notch signaling pathway and wingless at the transcriptional level, and deltex is already a Notch modulator that can alter wingless mRNA expression (See Hori et al 2004). Deltex in addition to promoting a ligand-independent Notch signal can also induce expression of Notch ligand, allowing further non-autonomous Notch activation and subsequent cell autonomous cis-inhibition of the initial deltex-induced signal. The dynamics and outcomes of the Notch signal response to deltex in vivo is therefore already very complicated to interpret before even considering to unravel indirect (via Notch) and direct interactions with wingless, although the two possibilities are not mutually exclusive. Whilst the revised manuscript does not completely overcome these limitations, further data and quantification have improved the support for the conclusions and there is a wider discussion of the relevant literature. The conclusions are interesting and add significantly to our understanding of the intersections between Wingless, Notch and trafficking regulators in an in vivo context.

Reviewer #2 (Public Review):

Summary:

The study by Algranati et al. introduces an exciting and promising therapeutic approach for the treatment of H3-K27M pediatric gliomas, a particularly aggressive brain cancer predominantly affecting children. By exploring the dual targeting of histone deacetylases (HDACs) and MYC activation, the research presents a novel strategy that significantly reduces cell viability and tumor growth in patient-derived glioma cells and xenograft mouse models. This approach, supported by transcriptomic and epigenomic profiling, unveils the potential of combining Sulfopin and Vorinostat to downregulate oncogenic pathways, including the mTOR signaling pathway. While the study offers valuable insights, it would benefit from additional clarification on several points, such as the rationale behind the dosing decisions for the compounds tested, the specific contributions of MYC amplification and H3K27me3 alterations to the observed therapeutic effects, and the details of the treatment protocols employed in both in-vitro and in-vivo experiments.

Clarification is needed on how doses were selected for the compounds in Figure S2A and throughout the study. Understanding the basis for these choices is crucial for interpreting the results and their potential clinical relevance. IC50s are calculated for specific patient derived lines, but it is not clear how these are used for selecting the dose.

The introduction mentions MYC amplification in high-grade gliomas. It would be beneficial if the authors could delineate whether the models used exhibit varying degrees of MYC amplification and how this factor, alongside differences in H3K27me3, contributes to the observed effects of the treatment.

In Figure 2A, the authors outline an optimal treatment timing for their in vitro models, which appears to be used throughout the figure. It would be helpful to know how this treatment timing was selected and also why Sulfopin is dosed first (and twice) before the vorinostat. Was this optimized?

It should be clarified whether the dosing timeline for the combination drug experiments in Figure 3 aligns with that of Figure 2. This information is also important for interpreting the epigenetic and transcriptional profiling and the timing should be discussed if they are administered sequentially (also shown in Figure 2A).I have the same question for the mouse experiments in Figure 4.

The authors mention that the mice all had severe dehydration and deterioration after 18 days. It would be helpful to know if there were differences in the side effects for different treatment groups? I would expect the combination to be the most severe. This is important in considering the combination treatment.

Minor Points:

(1) For Figure 1F, reorganizing the bars to directly compare the K27M and KO cell lines at each dose would improve readability of this figure.

(2) In Figure 4D, it would be helpful to know how many cells were included (or a minimum included) to calculate the percentages.

Reviewer #3 (Public Review):

In this study Gray and coworkers use a transposon mutant library in order to define: (i) essential genes for K. pneumoniae growth in LB medium, (ii) genes required for growth in urine, (iii) genes required for resistance to serum and complement mediated killing. Although there are previous studies, using a similar strategy, to describe essential genes for K. pneumoniae growth and genes required for serum resistance, this is the first work to perform such a study in urine. This is important because these types of pathogens can cause urinary tract infections. Moreover, the authors performed the work using a highly saturated library of mutants, which makes the results more robust, and used a clinically relevant strain from a pathotype for which similar studies have not been performed yet. Besides applying the transposon mutant library coupled with high-throughput sequencing, the authors validate some of the most relevant genes required for each condition using targeted mutagenesis. This is an important step to confirm that the results obtained from the library are reliable. Although this was done for only a small subset of the most significant genes. In addition, in vitro experiments involving complementation of urine with iron provide additional support to the results obtained with the mutants suggesting the importance of genes required for iron acquisition in a limiting-iron environment such as urine. Overall, the study is well-designed and written, and the methodology and analysis performed are adequate. The study would have benefited from in vivo experiments, including a mouse model of bacterial sepsis or urinary tract infections which could have demonstrated the role of some of the identified genes in the infection process. Nevertheless, the results obtained are informative for the scientific community since they pinpoint genes potentially more relevant in infections caused by K. pneumoniae. The identified genes could represent future targets for developing new therapies against a type of pathogen that is acquiring resistance to all available antibiotics. Although, as mentioned above, these potential targets should be confirmed using in vivo models.

One potential weakness of the work is that the TnSeq analysis only included two replicates per condition, thus it is possible that some of the differences detected may not be reproducible in future studies, first of all those that are less significant. In this sense, hundreds of genes were detected to be theoretically relevant for bacterial resistance to complement in serum. It is possible that some of these genes represent false positives. Thus, confirmation of the relevance of these genes in resistance to complement should be performed in future studies.

Reviewer #3 (Public Review):

Summary:

The receptor tyrosine kinase Anaplastic Lymphoma Kinase (ALK) in humans is nervous system expressed and plays an important role as an oncogene. A number of groups have been studying ALK signalling in flies to gain mechanistic insight into its various roles. In flies, ALK plays a critical role in development, particularly embryonic development and axon targeting. In addition, ALK was also shown to regulate adult functions including sleep and memory. In this manuscript, Sukumar et al., used a suite of molecular techniques to identify downstream targets of ALK signalling. They first used targeted DamID, a technique that involves a DNA methylase to RNA polymerase II, so that GATC sites in close proximity to PolII binding sites are marked. They performed these experiments in wild type and ALK loss of function mutants (using an Alk dominant negative ALkDN), to identify Alk responsive loci. Comparing these loci with a larval single cell RNAseq dataset identified neuroendocrine cells as an important site of Alk action. They further combined these TaDa hits with data from RNA seq in Alk Loss and Gain of Function manipulations to identify a single novel target of Alk signalling - a neuropeptide precursor they named Sparkly (Spar) for its expression pattern. They generated a mutant allele of Spar, raised an antibody against Spar, and characterised its expression pattern and mutant behavioural phenotypes including defects in sleep and circadian function.

Strengths:

The molecular biology experiments using TaDa and RNAseq were elegant and very convincing. The authors identified a novel gene they named Spar. They also generated a mutant allele of Spar (using CrisprCas technology) and raised an antibody against Spar. These experiments are lovely, and the reagents will be useful to the community. The paper is also well written, and the figures are very nicely laid out making the manuscript a pleasure to read.

Weaknesses:

The manuscript has improved very substantially in revision. The authors have clearly taken the comments on board in good faith. Yet, some small concerns remain around the behavioural analysis.

In Fig. 8H and H' average sleep/day is ~100. Is this minutes of sleep? 100 min/day is far too low, is it a typo?

The numbers for sleep bouts are also too low to me e.g. in Fig 9 number of sleep bouts avg around 4.

In their response to reviewers the authors say these errors were fixed, yet the figures appear not to have been changed. Perhaps the old figures were left in inadvertently?

The circadian anticipatory activity analyses could also be improved. The standard in the field is to perform eduction analyses and quantify anticipatory activity e.g. using the method of Harrisingh et al. (PMID: 18003827). This typically computed as the ratio of activity in the 3hrs preceding light transition to activity in the 6hrs preceding light transition.

In their response to reviewers, the authors have revised their anticipation analyses by quantifying the mean activity in the 6 hrs preceding light transition. However, in the method of Harrisingh et al., anticipation is the ratio of activity in the 3hrs preceding light transition to activity in the 6hrs preceding light transition. Simply computing the activity in the 6hrs preceding light transition does not give a measure of anticipation, determining the ratio is key.

Reviewer #2 (Public Review):

Summary:

In this study, Gularte-Merida et al investigate the occurrence of transgenerational effects of non-transmitted parental alleles outside of the well-described effect of "genetic nurture." To achieve this they employed consomic male mice to generate an N2 and N3 population, allowing for the observation of effects due to non-transmitted paternal alleles while controlling for maternal care by using isogenic B6 dams. The authors conduct RNAseq, qPCR validation, and anatomical phenotyping measures to investigate the presence of non-genetic nurture TGE. The author's findings challenge the frequency of non-genetic nurture TGE, a meaningful contribution to the field. Overall, this is an ambitious study with important negative data. The authors are to be commended on this. This greatly strengthens the negative findings within the paper.

The paper, however, is written extremely technically, with little detail, and is not currently suitable for the lay audience. The authors need to greatly increase the clarity of the writing and data presentation.

Strengths:

Elegant experimental design using consomic mouse populations.

The use of a second replication cohort using the same genetic founders as the first study.

Weaknesses:

While much of the explanation of the methods is understandable by geneticists, the paper has implications outside of the genetics field. Overall, I suggest expanding the explanation and language for non-geneticists. This will allow the paper to reach a wider audience.

Reviewer #2 (Public Review):

Summary:

The Authors identified miR-199b-5p is a potential OA target gene using serum exosomal small RNA-seq from human healthy and OA patients. Their RNA-seq results were further compared with publicly available datasets to validate their finding of miR-199b-5p. In vitro chondrocyte culture with miR-199b-5p mimic/inhibitor and in vivo animal models were used to evaluate the function of miR-199b-5p in OA. The possible genes that were potentially regulated by miR-199b-5p were also predicted (i.e., Fzd6 and Gcnt2) and then validated by using Luciferase assays.

Strengths:

(1) Strong in vivo animal models including pain tests.<br /> (2) Validate the binding of miR-199b-5p with Fzd6 and binding of miR-199b-5p with Gcnt2

The authors have addressed my concerns.

Reviewer #2 (Public review):

Summary:

This manuscript aimed to investigate the non-genetic impact of KHDC3 mutation on the liver metabolism. To do that they analyzed the female liver transcriptome of genetically wild type mice descended from female ancestors with a mutation in the Khdc3 gene. They found that genetically wild type females descended from Khdc3 mutants have hepatic transcriptional dysregulation which persist over multiple generations in the progenies descended from female ancestors with a mutation in the Khdc3 gene. This transcriptomic deregulation was associated with dysregulation of hepatically-metabolized molecules in the blood of these wild type mice with female mutational ancestry. Furthermore, to determine whether small non-coding RNA could be involved in the maternal non-genetic transmission of the hepatic transcriptomic deregulation, they performed small RNA-seq of oocytes from Khdc3-/- mice and genetically wild type female mice descended from female ancestors with a Khdc3 mutation and claimed that oocytes of wild type female offspring from Khdc3-null females has dysregulation of multiple small RNAs.

Finally, they claimed that their data demonstrates that ancestral mutation in Khdc3 can produce transgenerational inherited phenotypes.

However, at this stage and considering the information provided in the paper, I think that these conclusions are too preliminary. Indeed, several controls/experiments need to be added to reach those conclusions.

Additional context you think would help readers interpret or understand the significance of the work<br /> • Line 25: this first sentence is very strong and needs to be documented in the introduction.<br /> • Line 48: Reference 5 is not appropriate since the paper shows the remodeling of small RNA during post-testicular maturation of mammalian sperm and their sensibility to environment. Please, change it<br /> • Line 51: "implies" is too strong and should be replaced by « suggests »<br /> • Line 67: reference is missing<br /> Database, the accession numbers are lacking.<br /> • References showing the maternal transmission of non-genetically inherited phenotypes in mice via small RNA need to be added<br /> • Line 378: All RNA-Seq and small RNA-Seq data are available in the NCBI GEO

Reviewer #2 (Public Review):

Summary:

The authors have addressed the role of S1086 in the FMNL1beta DAD domain in F-actin dynamics, MVB polarization, and exosome secretion, and investigated the potential implication of PKCdelta, which they had previously shown to regulate these processes, in FMNL1beta S1086 phosphorylation. This is based on:<br /> (1) the documented role of FMNL1 proteins in IS formation;<br /> (2) their ability to regulate F-actin dynamics;<br /> (3) the implication of PKCdelta in MVB polarization to the IS and FMNL1beta phosphorylation;<br /> (4) the homology of the C-terminal DAD domain of FMNL1beta with FMNL2, where a phosphorylatable serine residue regulating its auto-inhibitory function had been previously identified.

They demonstrate that FMNL1beta is indeed phosphorylated on S1086 in a PKCdelta-dependent manner and that S1086-phosphorylated FMNL1beta acts downstream of PKCdelta to regulate centrosome and MVB polarization to the IS and exosome release. They provide evidence that FMNL1beta accumulates at the IS where it promotes F-actin clearance from the IS center, thus allowing for MVB secretion.

Strengths

The work is based on a solid rationale, which includes previous findings by the authors establishing a link between PKCdelta, FMNL1beta phosphorylation, synaptic F-actin clearance, and MVB polarization to the IS. The authors have thoroughly addressed the working hypotheses using robust tools. Among these, of particular value is an expression vector that allows for simultaneous RNAi-based knockdown of the endogenous protein of interest (here all FMNL1 isoforms) and expression of wild-type or mutated versions of the protein as YFP-tagged proteins to facilitate imaging studies. The imaging analyses, which are the core of the manuscript, have been complemented by immunoblot and immunoprecipitation studies, as well as by the measurement of exosome release (using a transfected MVB/exosome reporter to discriminate exosomes secreted by T cells).

Weaknesses

The data on F-actin clearance in Jurkat T cells knocked down for FMNL1 and expressing wild-type FMNL1 or the non-phosphorylatable or phosphomimetic mutants thereof would need to be further strengthened, as this is a key message of the manuscript. Also, the entire work has been carried out on Jurkat cells. Although this is an excellent model easily amenable to genetic manipulation and biochemical studies, the key finding should be validated on primary T cells.

Reviewer #2 (Public Review):

The first portion of the manuscript centered on identifying and confirming the ATHB2 microprotein (ATHB2miP), which constitutes the core message of this study. Overall, I find no issue with the selection criteria employed for identifying alternative microprotein mRNA transcripts. However, I do have some queries that I hope the authors can address for clarity.

(1) Upon reviewing the supplemental dataset where the authors listed the 377 unique novel miPs, along with those specifically in WL or shade treatments, I sought to comprehend the rationale behind focusing on ATHB2. Have the authors examined the shade response of all 377 potential microprotein candidates? Readers may be intrigued to learn how many of these candidates exhibit induction or repression under shade conditions, and whether such changes correlate positively or negatively with alterations in the full-length TSSs in response to shade. Essentially, I aim to discern the prevalence of microprotein production during shade responses and any shared characteristics among these microprotein transcripts. This inquiry also aims to uncover the existence of a common mechanism regulating microprotein transcription.

(2) To confirm that ATHB2miP stems from an independent transcription event, the authors sequenced full-length cDNAs using PacBio isoseq. However, I find the information regarding isoseq missing from the manuscript. My assumption is that the full-length cDNAs were reverse transcribed from mRNAs isolated from whole seedlings, where mature mRNAs in the cytoplasm predominate, making it challenging to evaluate whether a specific mRNA undergoes post-transcriptional processing. One approach to confirming ATHB2miP as a product of independent transcription involves examining nascent mRNA produced in the nucleus. The authors may need to isolate nascent mRNAs associated with RNA Polymerase II in the nucleus from seedlings treated with shade for 45 min, and then perform reverse transcription and PacBio isoseq.

(3) The authors noted the identification of two potential start codons, TTG and CTG, in the alternative TSS of ATHB2 using TISpredictor. Yet, it's imperative to identify the actual translation initiation site and the full-length sequence of ATHB2miP. I suggest the authors fuse an epitope tag (e.g., 3xFLAG) to the C-terminus of ATHB2 (utilizing the genomic sequence of ATHB2) and generate transgenic lines to be treated with shade to induce ATHB2miP-3xFLAG production. Affinity purification (anti-FLAG beads) and mass spectrometry can then identify the actual start site of ATHB2miP. This step is crucial, as the current ATHB2miP used may not be the exact sequence, and any observed phenotype could be artifacts arising from these lines.

(4) My confusion arose when analyzing the results in Figures 1E - G. The authors didn't specify whether these plants were subjected to shade treatment. What are the sequences within the second intron and third exon excluded from pATHB2control::GUS that promote transcription and translation? Have the authors examined the sequence features? This information is pivotal and related to the above question #1 because it may tell us whether the sequence feature is shared by other miP candidates.

The latter part of the manuscript focused on the functional characterization of ATHB2miP. The approaches adopted by the authors resemble those used in studying antimorphic (dominant negative) alleles. However, I have several concerns regarding the approaches and conclusions.

(5) Firstly, as mentioned in question #3, the authors did not map the actual translation initiation site of ATHB2miP. Therefore, all constructs involving ATHB2miP, such as eGFP-ATHB2miP, BD-ATHB2miP, and mCherry-ATHB2miP in Figure 2, and 35S::miP in Figures 3-5, may contain extra amino acids in the N-terminus, given that epitope tags were all added to the N terminus. These additional amino acids could potentially impact the behavior of ATHB2miP and lead to artifacts. Identifying the translation initiation site in ATHB2miP would facilitate the development of tools to disrupt ATHB2miP expression without affecting full-length ATHB2 expression. For instance, if the "CTG" before the leucine zipper domain is confirmed as the translation initiation site, mutating it to another Leu codon (e.g., TTA) could generate transgenic lines using the genomic sequence of ATHB2, including this mutation, to evaluate the impact of losing ATHB2miP on shade responses.

(6) Another concern pertains to the 35S::miP line utilized in Figures 3-5. The authors only presented results from one 35S::miP line, raising the possibility of T-DNA insertion disrupting an endogenous gene in the transgenic plant genome. It is essential to clarify how many individual T1 plants were generated and how many of them showed the same phenotype as the line used in the manuscript. Additionally, the use of the constitutive CaMV35S promoter could generate artifacts akin to neomorphic mutations. For example, the authors identified Cluster 1 genes that were only induced in 35S::miP, but not in t-athb2 or WT plants (Figure 3B); moreover, they found an overrepresentation of genes involved in root development in this cluster. This observation correlated well with the root phenotype of 35S::miP under the proximity shade (Figure 4D), in which the short-root phenotype was only observed in lines expressing 35S::miP. These data could be artifacts due to the constitutive expression of ATHB2miP in roots but didn't necessarily reflect the natural function of ATHB2miP.

(7) Furthermore, I seek clarification regarding the rationale behind employing different shade conditions, including deep shade, canopy shade, and proximity shade, and the significance of treating plants with these conditions. The results were challenging to interpret, and I have reservations about some statements made. The authors claimed that ATHB2 acts as a growth repressor in deep shade but a growth promoter in the canopy and proximity shade (Lines 366-368). However, it appears that regardless of the shade conditions, most mutant and transgenic lines were not significantly different from WT (Figure 4C). Additionally, the definition of proximity shade in this manuscript (R:FR = 0.06) differs from that in Roig-Villanova & Martinez-Garcia (Front. Plant Sci., 2016; R:FR, 0.5-0.3). Clarity on this disparity would be appreciated.

(8) In Figure 5, no statistical analyses were presented in Figure 5C. It remains unclear whether the differences observed are statistically significant. Moreover, the values appear quite similar among all three genotypes. Even if statistically significant, do these minor differences in Fe concentrations significantly impact plant physiology? Additionally, some statements related to Figure 5 do not align with the data presented. For instance, claims about longer hypocotyls in t-athb2, athb2∆, and atbh2∆LZ mutants compared to wild type under shade conditions on high iron media (lines 453-455) were not supported by the data in Figure 5D. Similarly, statements about the differences between mutants (lines 458-460) were not substantiated by the data.

Reviewer #2 (Public Review):

In this study, Kavaklıoğlu et al. investigated and presented evidence for the role of domesticated transposon protein L1TD1 in enabling its ancestral relative, L1 ORF1p, to retrotranspose in HAP1 human tumor cells. The authors provided insight into the molecular function of L1TD1 and shed some clarifying light on previous studies that showed somewhat contradictory outcomes surrounding L1TD1 expression. Here, L1TD1 expression was correlated with L1 activation in a hypomethylation-dependent manner, due to DNMT1 deletion in the HAP1 cell line. The authors then identified L1TD1-associated RNAs using RIP-Seq, which displays a disconnect between transcript and protein abundance (via Tandem Mass Tag multiplex mass spectrometry analysis). The one exception was for L1TD1 itself, which is consistent with a model in which the RNA transcripts associated with L1TD1 are not directly regulated at the translation level. Instead, the authors found the L1TD1 protein associated with L1-RNPs, and this interaction is associated with increased L1 retrotransposition, at least in the contexts of HAP1 cells. Overall, these results support a model in which L1TD1 is restrained by DNA methylation, but in the absence of this repressive mark, L1TD1 is expressed and collaborates with L1 ORF1p (either directly or through interaction with L1 RNA, which remains unclear based on current results), leads to enhances L1 retrotransposition. These results establish the feasibility of this relationship existing in vivo in either development, disease, or both.

Reviewer #2 (Public Review):

Summary:

The authors describe a "beads-on-a-string" (BOAS) immunogen, where they link, using a non-flexible glycine linker, up to eight distinct hemagglutinin (HA) head domains from circulating and non-circulating influenzas and assess their immunogenicity. They also display some of their immunogens on ferritin NP and compare the immunogenicity. They conclude that this new platform can be useful to elicit robust immune responses to multiple influenza subtypes using one immunogen and that it can also be used for other viral proteins.

Strengths:

The paper is clearly written. While the use of flexible linkers has been used many times, this particular approach (linking different HA subtypes in the same construct resembling adding beads on a string, as the authors describe their display platform) is novel and could be of interest.

Weaknesses:

The authors did not compare to individuals HA ionized as cocktails and did not compare to other mosaic NP published earlier. It is thus difficult to assess how their BOAS compare.

Other weaknesses include the rationale as to why these subtypes were chosen and also an explanation of why there are different sizes of the HA1 construct (apart from expression). Have the authors tried other lengths? Have they expressed all of them as FL HA1?

Reviewer #2 (Public Review):

Summary:

The study by Rößling et al. addresses the link between the biochemical constitution of the cell wall, in particular the methylesterification state of pectin with signalling induced by the extracellular RALF peptide. The work suggests that only in the presence of demethylesterifies pectin, RALF is able to trigger activation of its receptor FERONIA (FER).

Remarkably, the application of RALF peptides leads to rather dramatic FER-dependent changes in wall integrity and plasma membrane invaginations not observed before. Interestingly, RALF can be out-titrated from the wall by short pectin fragments. In addition, the study provides further evidence for multiple FER-dependent pathways by showing the presence of LRX proteins is not required for the pectin/RALF mediated signalling.

Strengths:

This work provides fundamental insight into a complex emerging pathway, or perhaps several pathways, linking pectin sensing, pectin structure and RALF/FER signalling. The study provides convincing evidence that pectin methylesterase activity is required for RALF sensing, indicating that the physical interaction of RALFs with the cell wall is important for signalling. Beyond that, the study documents very clearly how profoundly RALF signalling can affect cell wall integrity and membrane topology.

Weaknesses:

The genetic material used by the authors to strengthen the connection of RALF signalling and PME activity might not be as suitable as an acute inhibition of PME activity.

The PMEI3ox line generated by Peaucelle et al., 2008 is alcohol-inducible. Was expression of the PMEI induced during the experiments? As ethanol inducible systems can be rather leaky, it would not be surprising if PME activity would be reduced even without induction, but maybe this would warrant testing whether PMEI3 is actually overexpressed and/or whether PME activity is decreased. On a similar note, the PMEI5ox plants do not appear to show the typical phenotype described for this line. I personally don't think these lines are necessary to support the study. Short-term interference with PME activity (such as with EGCG) might be more meaningful than life-long PMEI overexpression, in light of the numerous feedback pathways and their associated potential secondary effects. This might also explain why EGCG leads to an increase in pH, as one would expect from decreased PME activity, while PMEI expression (caveats from above apply) apparently does not (Fig 3A-D).

At least at first sight, the observation that OGs are able to titrate RALF from pectin binding seems at odds with the idea of cooperative binding with low affinity, leading to high avidity oligomers. Perhaps the can provide a speculative conceptual model of these interactions?

I could not find a description of the OG treatment/titration experiments, but I think it would be important to understand how these were performed with respect to OG concentration, timing of the application, etc.

Reviewer #2 (Public Review):

Summary:

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

However, the overall conclusions of the study are not well supported experimentally. The significance of the findings is low because of their mostly correlational nature, and lack of consistency with earlier reports on the same protein.

Based on the integrity and quality of the data as well as the depth of analysis, it is not yet clear if ATG6 is a specific regulator of NPR1 or if it is affecting NPR1's stability indirectly, through inducing an elevation of SA levels in plants. As such, the current study demonstrates a correlation between overexpression of ATG6, SA accumulation, and NPR1 stability, however, whether and how these components work together is not yet demonstrated.

Based on the provided biochemical data, it is not yet clear if the ATG6 functions specifically through NPR1 or through its paralogs NPR3 and NPR4, which are negative regulators of immunity. It is quite possible that interaction with NPR1 (or any NPR) is not the major regulatory step in the activity of ATG6 in plant immunity. The effect of ATG6 on NPR1 could well be indirect, through a change in the SA level and redox environment of the cell during the immune response. Both SA level and redox state of the cell were reported to induce accumulation of NPR1 in the nucleus and increase in stability.

Another major issue is the poor quality of the subcellular analyses. In contradiction to previous studies, ATG6 in this study is not localized to autophagosome puncta, which suggests that the soluble localization pattern presented here does not reflect the true localization of ATG6. Even if the authors propose a novel, non-canonical nuclear localization for ATG6, they still should have detected the canonical autophagy-like localization of this protein.

Reviewer #2 (Public Review):

In this study, the authors report that both mice and human patients carrying function-disrupting mutations in the OFD1 gene exhibited ectopic brown adipose tissue formation in the malformed tongue. The OFD1 gene is located on the X-chromosome and encodes a protein product required for the formation and function of the primary cilium, which is required for cells to properly receive and activate several signaling pathways, particularly the hedgehog signaling pathway. Loss of OFD1 function causes prenatal lethality of male fetuses and mosaic disruption of tissues in females due to random inactivation of the X-chromosome carrying either the mutant or wildtype allele. Using cell type-specific gene inactivation and genetic lineage labeling, the manuscript shows that the ectopic brown adipose tissue in the mutant tongue was not derived from cranial neural crest cells (CNCCs). Additional genetic and embryological studies led to the conclusion that loss of Ofd1 function in the CNCC cells in the embryonic hypoglossal cord, via which the tongue myoblast precursor cells migrate from anterior somites to the tongue primordia, caused disruption of cell-cell interactions between the CNCCs and migrating muscle precursor cells, resulting in altered differentiation of those myoblast precursor cells into brown adipocytes. The authors provided data that disruption of Smo in a subset of CNCCs also resulted in ectopic adipose tissue formation in the tongue, indicating that this phenotype in the Ofd1 mutant mice was likely caused by disruption of hedgehog signaling in CNCCs. However, no experimental evidence is provided to support a major conclusion of the manuscript regarding altered differentiation of the tongue myoblast precursor cells into brown adipocytes in the Ofd1 mutant mice. Since it is well established that hedgehog signaling in the CNCCs is required for them to direct tongue myoblast cell migration as well as for tongue muscle differentiation/organization after the myoblasts arrived in the tongue primordia, the finding of tongue muscle defects in the Ofd1 mutant mice is not surprising. However, if proven true that disruption of Ofd1 function in CNCCs caused tongue myoblast precursor cells to alter their fate and differentiate into brown adipocytes, it would be an interesting new finding. Further identification of the signals produced by the Ofd1 mutant CNCCs for directing the cell fate switch will be a highly significant new advance in understanding the cellular and molecular mechanisms regulating tongue morphogenesis.

Reviewer #2 (Public Review):

Summary<br /> This study by Knop, et al. defines two different developmental roles for the conserved SEL-5/AAK1 protein kinase in Caenorhabditis elegans. In other organisms, AAK1 was known to promote the recycling of the Wntless sorting receptor and endocytosis of Wnt receptors. This study establishes that SEL-5 acts in two roles in C. elegans: in Wnt-producing cells, a role that promotes migration of a neuroblast termed QL.d, and in Wnt-receiving cells, a role that promotes outgrowth of the excretory cell (EXC). Before this study, SEL-5/AAK1 was thought to regulate endocytosis through phosphorylation of AP2M1 and other endocytic adaptor proteins. This study shows convincing data that the SEL-5 makes a partial contribution to AP2M1 phosphorylation, and more surprisingly, that its roles in Wnt-producing and Wnt-receiving cells of C. elegans do not require SEL-5 catalytic activity. Human AAK1 was previously suggested to be a target of drug design efforts due to its roles in neuropathic pain, viral infection, and Alzheimer's disease. The discovery that some roles for SEL-5/AAK1 are independent of catalytic activity will be of broad interest to cell biologists and biochemists.

Strengths<br /> (1) The data establishing the requirement for SEL-5 in QL.d migration and EXC outgrowth (Fig. 1 and Fig. 4) is rigorous and convincing. My assessment of the rigor is based on the following: First, the authors show that two independently derived sel-5 deletion mutations result in defects in QL.d and EXC. Second, the authors show that providing wild-type, GFP-tagged SEL-5 results in significant rescue of both phenotypes. Importantly, they use tissue-specific transgenes to show that the requirement for SEL-5 in QL.d migration is non-cell-autonomous, and the requirement for SEL-5 in EXC outgrowth is cell-autonomous (Fig. 2). For rescue experiments, they show that each tissue-specific transgene is indeed expressed strongly in the tissue of interest. This establishes the roles for SEL-5 in two different roles, in Wnt-producing and Wnt-receiving cells.

(2) The authors present three lines of convincing biochemical and genetic evidence that SEL-5 kinase catalytic activity is not important for its roles in Wnt-producing and Wnt-receiving cells.

Taking a biochemical approach, they use quantitative Westerns to assess the degree of AP2M1 phosphorylation in sel-5 mutants (Fig. 3). Their results show that AP2M1 phosphorylation is diminished, but not absent in mutants. Their results are convincing because they make use of GFP-tagged AP2M1 to probe for total and phospho-AP2M1. I note that they included uncropped Western blots in supplemental data. Furthermore, they make use of a GFP-tagged AP2M1 mutant (T160A) to confirm which residue is phosphorylated. Their results suggest that some mechanism other than AP2M1 phosphorylation may account for the sel-5 mutant phenotypes.

Taking a genetic approach, they make use of a unique allele, dpy-23(mew25), that alters the known AP2M1 phosphorylation site. They show that animals carrying this allele do not display the QL.d and EXC phenotypes (Fig. 3 and Fig. 5). Finally, in a more direct test of whether SEL-5 requires catalytic activity, they make use of GFP-tagged SEL-5 forms mutated at either the active site or the ATP-binding site of the SEL-5 kinase domain. They show that either SEL-5 mutant form successfully rescues the QL.d and EXC defects seen in sel-5 mutants (Fig. 3), suggesting that SEL-5 catalytic activity is unnecessary.

(3) The authors have produced an elegant GFP knock-in allele of the sel-5 gene, allowing analysis of expression and localization in living animals (Fig. 2).

(4) The authors make use of genetic interactions with Wnt signaling mutants to show that SEL-5 acts in a role that promotes Wnt signaling for the QL.d cell (Fig. 1) and counteracts Wnt signaling for the EXC (Fig. 5).

Weaknesses<br /> (1) Some changes to statistical analyses are needed in this study.

Fig. 1B, 1D, 2A, 3E, and 3F report the QL.d phenotype as a percentage of animals scored that were defective in migration. The methods make it clear this data is categorical rather than quantitative. Therefore, a t-test or any test designed for quantitative data is not appropriate. I suggest that the authors should investigate using a chi-squared or Fisher's exact test.

For the reasons mentioned above, the calculation of standard deviation (as shown in error bars) is also not appropriate for Fig. 1B, 1D, 2A, 3E, and 3F. Of course, it is excellent that the authors scored multiple trials. For experiments with mutants, I suggest the authors might combine these trials or show separate results of each trial. For experiments using RNAi (Fig. 1B), each trial should be plotted separately because RNAi effectiveness can vary. If there is not enough space to show multiple trials, then I would ask that a representative trial be shown in the main figure and additional trials in a supplement.

In Fig. 1, 2, 3, and 5, it is not specified whether/how p-values were adjusted for multiple tests.

(2) I felt the author's interpretation of the sel-5 mutant phenotypes in EXC, and the genetic interactions with Wnt signaling mutants, might be improved. The authors show convincing data that the sel-5 mutants display a shortened EXC outgrowth phenotype. Conversely, mutants with reduced Wnt signaling, such as the lin-17 or lin-44 mutants, displayed lengthened EXC outgrowth. The authors show that in double mutants, loss of sel-5 partially suppressed the EXC overgrowth defects of lin-17 or lin-44 mutants (Fig. 5). In my opinion, this data is consistent with a model where SEL-5 acts to inhibit Wnt signaling in EXC. An inhibitory role in a Wnt-receiving cell would be consistent with the known activity for human AAK1 in promoting negative feedback and endocytosis of LPR6. Interestingly, the authors mention in their discussion that a mutant of plr-1, which acts in the internalization of Frizzled receptors, has a shortened EXC phenotype similar to that of sel-5 mutants. These observations all seem consistent with an inhibitory role, yet the authors do not state this as their conclusion. A clarification of their interpretation is needed.

Impact/significance<br /> (1) Among researchers using C. elegans, this study provides a foundation for further investigation of the role of endocytosis, SEL-5, and the retromer, in Wnt trafficking. It is particularly useful that the authors define two different phenotypes that arise from Wnt-producing and Wnt-receiving cells.

(2) Among a broader community of cell biologists and biochemists, this study will be of interest in its finding that SEL-5/AAK1 kinase catalytic activity is unnecessary for the regulation of Wnt signaling.

Reviewer #2 (Public Review):

Urea is widely utilized in agriculture. In this study, the authors the mechanism underlying the adverse impact of urea on seed germination and seedling growth under salt stress conditions. The results show that salt stress induces a pronounced hydrolysis of urea, resulting in an elevation of cytoplasmic pH and subsequent inhibition of seed germination. These findings challenge the previous notion that ammonium accumulation is the primary cause of salt-induced inhibition of germination, thereby offering novel insights into this process.

The authors have provided well-organized genetic or biochemical evidence to support most of their conclusions.

Reviewer #2 (Public Review):

The manuscript entitled " Multimodal HLA-I genotypes regulation by human cytomegalovirus US10 and resulting surface patterning" by Gerke et al describes the biochemical analysis of US10-mediated down regulation of HLA-I molecules. The authors systemically examine the surface expression of different HLA-I alleles in cells expressing US10 and interactions of US10 with HLA-I and antigen presentation machinery. Further, studies examined genotypic and allotypic differences during expression of US10/US11 transcripts suggest a different allelic class I downregulation. In general, the authors have included data supporting the major claims. Yet, the conclusions and findings of the study only marginally advance the overall understanding of HCMV viral evasion and the mechanism of US10 function.

Strengths:<br /> The studies are well characterized and the studies utilize diverse HLA-I and HCMV viral molecules. The biochemistry is excellent and is of high quality. Importantly, the study describes HLA-I allelic specific HCMV down regulation at the cell surface and molecular levels.

Weaknesses:<br /> (1) The authors use over expressive language such as "strong binding" that does not have a quantitative value and it is relative to the specific assay with only small differences among the factors.<br /> (2) The US10 binding to the HLA-I did not correlate with class I surface levels suggesting that binding to the APC machinery (Figure 1); hence, why does the binding of US10 to the APC define its mechanism of action.<br /> (3) The innovative and significant aspects of the study are limited. The study does not delineate the US10 mechanism of action or show data in which US10-mediated MHC class I down regulation impacts adaptive or innate immune function.

Reviewer #2 (Public Review):

Summary:

The interplay between environmental factors and cognitive performance has been a focal point of neuroscientific research, with illuminance emerging as a significant variable of interest. The hypothalamus, a brain region integral to regulating circadian rhythms, sleep, and alertness, has been posited to mediate the effects of light exposure on cognitive functions. Previous studies have illuminated the role of the hypothalamus in orchestrating bodily responses to light, implicating specific neural pathways such as the orexin and histamine systems, which are crucial for maintaining wakefulness and processing environmental cues. Despite advancements in our understanding, the specific mechanisms through which varying levels of light exposure influence hypothalamic activity and, in turn, cognitive performance, remain inadequately explored. This gap in knowledge underscores the need for high-resolution investigations that can dissect the nuanced impacts of illuminance on different hypothalamic regions. Utilizing state-of-the-art 7 Tesla functional magnetic resonance imaging (fMRI), the present study aims to elucidate the differential effects of light on the hypothalamic dynamics and establish a link between regional hypothalamic activity and cognitive outcomes in healthy young adults. By shedding light on these complex interactions, this research endeavors to contribute to the foundational knowledge necessary for developing innovative therapeutic strategies aimed at enhancing cognitive function through environmental modulation.

Strengths:

(1) Considerable Sample Size and Detailed Analysis:<br /> The study leverages a robust sample size and conducts a thorough analysis of hypothalamic dynamics, which enhances the reliability and depth of the findings.

(2) Use of High-Resolution Imaging:<br /> Utilizing 7 Tesla fMRI to analyze brain activity during cognitive tasks offers high-resolution insights into the differential effects of illuminance on hypothalamic activity, showcasing the methodological rigor of the study.

(3) Novel Insights into Illuminance Effects:<br /> The manuscript reveals new understandings of how different regions of the hypothalamus respond to varying illuminance levels, contributing valuable knowledge to the field.

(4) Exploration of Potential Therapeutic Applications:<br /> Discussing the potential therapeutic applications of light modulation based on the findings suggests practical implications and future research directions.

Weaknesses:

(1) Foundation for Claims about Orexin and Histamine Systems:<br /> The manuscript needs to provide a clearer theoretical or empirical foundation for claims regarding the impact of light on the orexin and histamine systems in the abstract.

(2) Inclusion of Cortical Correlates:<br /> While focused on the hypothalamus, the manuscript may benefit from discussing the role of cortical activation in cognitive performance, suggesting an opportunity to expand the scope of the manuscript.

(3) Details of Light Exposure Control:<br /> More detailed information about how light exposure was controlled and standardized is needed to ensure the replicability and validity of the experimental conditions.

(4) Rationale Behind Different Exposure Protocols:<br /> To clarify methodological choices, the manuscript should include more in-depth reasoning behind using different protocols of light exposure for executive and emotional tasks.

Reviewer #2 (Public Review):

Summary:

In this work, using in-depth computational analysis, Bell et al. explore the diverse repertoire of type IV McrBC modification dependent restriction systems. The prototypical two-component McrBC system has been structurally and functionally characterised and is known to act as a defence by restricting phage and foreign DNA containing methylated cytosines. Here, the authors find previously unanticipated complexity and versatility of these systems and focus on detailed analysis and classification of a distinct branch, the so-called CoCoNut, named after its composition of coiled-coil structures and tandem nucleases. These CoCoNut systems are predicted to target RNA as well as DNA and to utilise defence mechanisms with some similarity to type III CRISPR-Cas systems.

Strengths:

This work is enriched with a plethora of ideas and a myriad of compelling hypotheses that now will await experimental verification. The study comes from the group that was amongst the first to describe, characterise, and classify CRISPR-Cas systems. By analogy, the findings described here can similarly promote ingenious experimental and conceptual research that could further drive technological advances. It could also instigate vigorous scientific debates that will ultimately benefit the community.

Weaknesses:

The multi-component systems described here function in the context of large oligomeric complexes similarly to the prototypical McrBC system. While the AlphaFold2 (AF2) multimer predictions are provided in this work, these are not compared with the known McrBC structures. These comparisons could have been helpful not only for providing insights into these multimeric protein systems but also for giving more sound explanations of the differences observed amongst different McrBC types.

Reviewer #2 (Public Review):

Summary:

Key findings of this research include the sequencing of the wasp's genome, identification of venom constituents and teratocytes, and examination of Trichopria drosophilae (Td)'s ecology and parasitic strategies. It was observed that Td doesn't distinguish between hosts based on age but can recognize previously parasitized hosts. The study also explored whether multiple parasitisms by Td improved outcomes, which indeed it did, possibly by increasing venom and teratocyte levels. Utilizing Drosophila ectopic expression tools, the authors functionally characterized venom components, specifically tissue inhibitors of metalloproteinases (Timps), which were found to cause delays in host development. Additionally, experiments revealed that teratocytes produce numerous proteases, aiding in the digestion of host tissues for parasite consumption. The discussion suggests that genes involved in different aspects of parasitism may arise from gene duplication and shifts in tissue expression to venom glands or teratocytes.

Strengths:

This manuscript provides an in-depth and detailed depiction of the parasitic strategies employed by Td wasps, spanning both molecular and behavioral aspects. It consolidates a significant amount of research that, in the past, might have been distributed across multiple papers. By presenting all this data in a single manuscript, it delivers a comprehensive and engaging study that could help future developments in the field of biological control against a major insect pest.

Weaknesses:

While none of the findings are particularly groundbreaking, as similar results have been reported for other parasitoid species in prior research, the integration of these results into one comprehensive overview offers valuable biological insights into an interesting new potential biocontrol species.

Reviewer #2 (Public Review):

Summary:

Pancreatic ductal adenocarcinoma is generally considered a "cold" tumor type with little T cell infiltration. This group demonstrated previously that deletion of the PIK3CA isoform of PI3K in the orthotopic pancreatic ductal adenocarcinoma KPC mouse tumor model led to the elimination of tumors by T cells. Here they performed a genome-wide gene-deletion screen in this tumor using CRISPR to determine what was required for this T cell-mediated infiltration and tumor rejection. Deletion of Pccb in the tumors, which encodes propionyl-CoA carboxylase subunit B, allowed for the outgrowth of the PIK3CA-deleted KPC tumors. This was confirmed with the specific deletion of Pccb in the tumor cells. Demonstrating a likely role in tumor progression in human patients as well, high expression of PCCB in pancreatic ductal adenocarcinoma correlated with lower patient survival. T cells still infiltrated these tumors, but had much higher expression of exhaustion markers. Blockade of PD-1 signaling allowed for the rejection of these tumors. While these are intriguing data demonstrating that loss of PCCB by pancreatic ductal adenocarcinoma is a mechanism to escape T cell immunity, the mechanism by which this occurs is not determined. In addition, there are a few issues that suggest the conclusions of the manuscript should be tempered.

Strengths:

In vivo analysis of tumor CRISPR deletion screen.

The study describes a possible novel mechanism by which a tumor maintains a "cold" microenvironment.

Weaknesses:

(1) A major issue is that it seems these data are based on the use of a single tumor cell clone with PIK3CA deleted. Therefore, there could be other changes in this clone in addition to the deletion of PIK3CA that could contribute to the phenotype.

(2) The conclusion that the change in the PCCB-deficient tumor cell line is unrelated to mitochondrial metabolic changes may be incorrect based on the data provided. While it is true that in the experiments performed, there was no statistically significant change in the oxygen consumption rate or metabolite levels, this could be due to experimental error. There is a trend in the OCR being higher in the PCCB-deficient cells, although due to a high standard deviation, the change is not statistically significant. There is also a trend for there being more aKG in this cell line, but because there were only 3 samples per cell line, there is no statistically significant difference.

(3) More data are required to make the authors' conclusion that there are myeloid changes in the PCCB-deficient tumor cells. There is only flow data from shown from one tumor of each type.

(4) The previous published study demonstrated increased MHC and CD80 expression in the PIK3CA-deficient tumors and these differences were suggested to be the reason the tumors were rejected. However, no data concerning the levels of these proteins were provided in the current manuscript.

Reviewer #2 (Public Review):

Summary:

This study was designed to test the hypothesis that motor neurons play a causal role in circuit assembly of the vestibulo-ocular reflex circuit, which is based on the retrograde model proposed by Hans Straka. This circuit consists of peripheral sensory neurons, central projection neurons, and motor neurons. The authors hypothesize that loss of extraocular motor neurons, through CRISPR/Cas9 mutagenesis of the phox2a gene, will disrupt sensory selectivity in presynaptic projection neurons if the retrograde model is correct.

Account of the major strengths and weaknesses of the methods and results:

The work presented is impressive in both breadth and depth, including the experimental paradigms. Overall, the main results were that the loss of function paradigm to eliminate extraocular motor neurons did not 1) alter the normal functional connections between peripheral sensory neurons and central projection neurons, 2) affect the position of central projection neurons in the sensorimotor circuit, or 3) significantly alter the transcriptional profiles of central projection neurons. Together, these results strongly indicate that retrograde signals from motor neurons are not required for the development of the sensorimotor architecture of the vestibulo-ocular circuit.

Appraisal of whether the authors achieved their aims, and whether the results support their conclusions:

The results of this study showed that extraocular motor neurons were not required for central projection neuron specification in the vestibulo-ocular circuit, which countered the prevailing retrograde hypothesis proposed for circuit assembly. A concern is that the results presented may be limited to this specific circuit and may not be generalizable to other circuit assemblies, even to other sensorimotor circuits.

Discussion of the likely impact of the work on the field, and the utility of the methods and data to the community:

As mentioned above, this study sheds valuable new insights into the developmental organization of the vestibulo-ocular circuit. However, different circuits likely utilize various mechanisms, extrinsic or intrinsic (or both), to establish proper functional connectivity. So, the results shown here, although begin to explain the developmental organization of the vestibulo-ocular circuit, are not likely to be generalizable to other circuits; though this remains to be seen. At a minimum, this study provides a starting point for the examination of patterning of connections in this and other sensorimotor circuits.

Reviewer #2 (Public Review):

This is an interesting study of high quality with important and novel findings. Bruguera et al. report a biochemical and structural analysis of the Tspan12 co-receptor for norrin. Major findings are that Norrin directly binds Tspan12 with high affinity (this is consistent with a report on BioRxiv: Antibody Display of cell surface receptor Tetraspanin12 and SARS-CoV-2 spike protein) and a predicted structure of Tspan12 alone or in complex with Norrin. The Norrin/Tspan12 binding interface is largely verified by mutational analysis. An interaction of the Tspan12 large extracellular loop (LEL) with Fzd4 cannot be detected and interactions of full-length Tspan12 and Fzd4 cannot be tested using nano-disc based BLI, however, Fzd4/Tspan12 heterodimers can be purified and inserted into nanodiscs when aided by split GFP tags. An analysis of a potential composite binding site of a Fzd4/Tspan12 complex is somewhat inconclusive, as no major increase in affinity is detected for the complex compared to the individual components. A caveat to this data is that affinity measurements were performed for complexes with approximately 1 molecule Tspan12 and FZD4 per nanodisc, while the composite binding site could potentially be formed only in higher order complexes, e.g., 2:2 Fzd4/Tspan12 complexes. Interestingly, the authors find that the Norrin/Tspan12 binding site and the Norrin/Lrp6 binding site partially overlap and that the Lrp6 ectodomain competes with Tspan12 for Norrin binding. This result leads the authors to propose a model according to which Tspan12 captures Norrin and then has to "hand it off" to allow for Fzd4/Lrp6 formation. By increasing the local concentration of Norrin, Tspan12 would enhance the formation of the Fzd4/Lrp5 or Fzd4/Lrp6 complex.

The experiments based on membrane proteins inserted into nano-discs and the structure prediction using AlphaFold yield important new insights into a protein complex that has critical roles in normal CNS vascular biology, retinal vascular disease, and is a target for therapeutic intervention. However, it remains unclear how Norrin would be "handed off" from Tspan12 or Tspan12/Fzd4 complexes to Fzd4/Lrp6 complexes, as the relatively high affinity of Norrin to Fzd4/Tspan12 dimers likely does not favor the "handing off" to Fzd4/Lrp6 complexes.

Areas that would benefit from further experiments, or a discussion, include:

- The authors test a potential composite binding site of Fzd4/Tspan12 heterodimers for norrin using nanodiscs that contain on average about 1 molecule Fzd4 and 1 molecule Tspan12. The Fzd4/Tspan12 heterodimer is co-inserted into the nanodiscs supported by split-GFP tags on Fzd4 and Tspan12. The authors find no major increase in affinity, although they find changes to the Hill slope, reflecting better binding of norrin at low norrin concentrations. In 293F cells overexpressing Fzd4 and Tspan12 (which may result in a different stoichiometry) they find more pronounced effects of norrin binding to Fzd4/Tspan12. This raises the possibility that the formation of a composite binding requires Fzd4/Tspan12 complexes of higher order, for example, 2:2 Fzd4/Tspan12 complexes, where the composite binding site may involve residues of each Fzd4 and Tspan12 molecule in the complex. This could be tested in nanodiscs in which Fzd4 and Tspan12 are inserted at higher concentrations or using Fzd4 and Tspan12 that contain additional tags for oligomerization.

- While Tspan12 LEL does not bind to Fzd4, the successful reconstitution of GFP from Tspan12 and Fzd4 tagged with split GFP components provides evidence for Fzd4/Tspan12 complex formation. As a negative control, e.g., Fzd5, or Tspan11 with split GFP tags (Fzd5/Tspan12 or Fzd4/Tspan11) would clarify if FZD4/Tspan12 heterodimers are an artefact of the split GFP system.

- Fzd4/Tspan12 heterodimers stabilized by split GFP may be locked into an unfavorable orientation that does not allow for the formation of a composite binding site of FZD4 and Tspan12, this is another caveat for the interpretation that Fzd4/Tspan12 do not form a composite binding site. This is not discussed.

- Mutations that affect the affinity of norrin/fzd4 are not used to further test if Fzd4 and Tspan12 form a composite binding site. Norrin R41E or Fzd4 M105V were previously reported to reduce norrin/frizzled4 interactions and signaling, and both interaction and signaling were restored by Tspan12 (Lai et al. 2017). Whether a Fzd4/Tspan12 heterodimer has increased affinity for Norrin R41E was not tested. Similarly, affinity of FZD4 M105V vs a Fzd4 M105V/Tspan12 heterodimer were not tested.

- An important conclusion of the study is that Tspan12 or Lrp6 binding to Norrin is mutually exclusive. This could be corroborated by an experiment in which LRP5/6 is inserted into nanodiscs for BLI binding tests with Norrin, or Tspan12 LEL, or a combination of both. Soluble LRP6 may remove norrin from equilibrium binding/unbinding to Tspan12, therefore presenting LRP6 in a non-soluble form may yield different results.

- The authors use LRP6 instead of LRP5 for their experiments. Tspan12 is less effective in increasing the Norrin/Fzd4/Lrp6 signaling amplitude compared to Norrin/Fzd4/Lrp5 signaling, and human genetic evidence (FEVR) implicates LRP5, not LRP6, in Norrin/Frizzled4 signaling. The authors find that Norrin binding to LRP6 and Tspan12 is mutually exclusive, however this may not be the case for Lrp5.

- The biochemical data are largely not correlated with functional data. The authors suggest that the Norrin R115L FEVR mutation could be due to reduced norrin binding to tspan12, but do not test if Tspan12-mediated enhancement of the norrin signaling amplitude is reduced by the R115L mutation. Similarly, the impressive restoration of binding by charge reversal mutations in site 3 is not corroborated in signaling assays.

Reviewer #2 (Public Review):

Summary:

Karim et al investigated the regulation of ACSS2 by SIRT2. The authors identified a previously undescribed acetylation that they then show is important for the regulation and stability of ACSS2 in cells. The authors show that ACSS2 ubiquitination and degradation by the proteasome is regulated by SIRT2-mediated deacetylation of ACSS2 and that stabilizing ACSS2 by blocking SIRT2 can alter lipid accumulation in adipocytes.

Strengths:

Identification of a novel acetylation site on ACSS2 that regulates its protein stability and that has consequences on its activity in adipocytes. Multiple standard approaches were used to manipulate the expression and function of SIRT2 and ACSS2 (i.e., overexpression, knockdown, inhibitors).

Weaknesses:

The authors do not show direct deacetylation of ACSS2 by SIRT2 in an in vitro biochemical assay.

It would have been nice to have included a bona-fide SIRT2 target as a control throughout the study.

Throughout the manuscript, normalizing the data to 1 and then comparing the fold-change using a t-test is not the best statistical approach in that situation since every normalized value for control is 1 with zero standard deviation. The authors should consider an alternative statistical approach.

Though not necessary, using 13C-acetate or D3-acetate tracing would be better for understanding the impact of acetylation on the activity of ACSS2 and its impact on lipogenesis.

Did the authors also consider investigating SIRT1 in their assays? SIRT1 activates ACSS2 while SIRT2 leads to degradation of ACSS2. They should at least discuss these seemingly opposing roles of SIRT1 and SIRT2 in the regulation of ACSS2 and acetate metabolism in more depth, particularly as it concerns situations (i.e., diseases, pathologies) where either SIRT1, SIRT2, or both sirtuins, are active. This would enhance the significance of the findings to the broader research community.

In Figure 3, the authors should consider immunoblotting for endogenous ACSS2 throughout the differentiation and lipogenesis study since the total ACSS2 levels is the crucial aspect to affecting acetate-dependent promotion of lipogenesis in adipocytes, and to confirm TM-dependent stabilization of ACSS2 in that assay.

Do the authors have any data proving the K271 mutants of ACSS2 are still functional? Or that K271 ACSS2 protein is folded correctly?

Reviewer #2 (Public Review):

Summary:

In this study by Bendzunas et al, the authors show that the formation of intra-molecular disulfide bonds involving a pair of Cys residues near the catalytic HRD motif and a highly conserved T-Loop Cys with a BRSK-specific Cys at an unusual CPE motif at the end of the activation segment function as repressive regulatory mechanisms in BSK1 and 2. They observed that mutation of the CPE-Cys only, contrary to the double mutation of the pair, increases catalytic activity in vitro and drives phosphorylation of the BRSK substrate Tau in cells. Molecular modeling and molecular dynamics simulations indicate that oxidation of the CPE-Cys destabilizes a conserved salt bridge network critical for allosteric activation. The occurrence of spatially proximal Cys amino acids in diverse Ser/Thr protein kinase families suggests that disulfide-mediated control of catalytic activity may be a prevalent mechanism for regulation within the broader AMPK family. Understanding the molecular mechanisms underlying kinase regulation by redox-active Cys residues is fundamental as it appears to be widespread in signaling proteins and provides new opportunities to develop specific covalent compounds for the targeted modulation of protein kinases.

The authors demonstrate that intramolecular cysteine disulfide bonding between conserved cysteines can function as a repressing mechanism as indicated by the effect of DTT and the consequent increase in activity by BSK-1 and -2 (WT). The cause-effect relationship of why mutation of the CPE-Cys only increases catalytic activity in vitro and drives phosphorylation of the BRSK substrate Tau in cells is not clear to me. The explanation given by the authors based on molecular modeling and molecular dynamics simulations is that oxidation of the CPE-Cys (that will favor disulfide bonding) destabilizes a conserved salt bridge network critical for allosteric activation. However, no functional evidence of the impact of the salt-bridge network is provided. If you mutated the two main Cys-pairs (aE-CHRD and A-loop T+2-CPE) you lose the effect of DTT, as the disulfide pairs cannot be formed, hence no repression mechanisms take place, however when looking at individual residues I do not understand why mutating the CPE only results in the opposite effect unless it is independent of its connection with the T+2residue on the A-loop.

Strengths:

This is an important and interesting study providing new knowledge in the protein kinase field with important therapeutic implications for the rationale design and development of next-generation inhibitors.

Comments on revised version:

I have one remark related to question number 5 (my question was not clear enough). I meant if the authors did look at the functional relevance of the residues implicated in the identified salt-bridge network/tethers. What happens to the proteins functionally when you mutate those residues? (represented on Fig. 8).

Otherwise, the authors have satisfactorily addressed my concerns.

Reviewer #2 (Public Review):

Summary:

This manuscript describes the analysis of blood transcriptomic data from patients with TB meningitis, with and without HIV infection, with some comparison to those of patients with pulmonary tuberculosis and healthy volunteers. The objectives were to describe the comparative biological differences represented by the blood transcriptome in TBM associated with HIV co-infection or survival/mortality outcomes, and to identify a blood transcriptional signature to predict these outcomes. The authors report an association between mortality and increased levels of acute inflammation and neutrophil activation, but decreased levels of adaptive immunity and T/B cell activation. They propose a 4-gene prognostic signature to predict mortality.

Strengths:

Biological evaluations of blood transcriptomes in TB meningitis and their relationship to outcomes have not been extensively reported previously.<br /> The size of the data set is a major strength and is likely to be used extensively for secondary analyses in this field of research.<br /> The addition of a new validation cohort to evaluate the generalisability of their prognostic model in the revised manuscript is welcome.

Weaknesses:

The bioinformatic analysis is limited to a descriptive narrative of gene-level functional annotations curated in GO and KEGG databases. This analysis cannot be used to make causal inferences. In addition the functional annotations are limited to 'high-level' terms that fail to define the biology very precisely. As a result, the conclusions about the immunopathogenesis of TBM are not adequately substantiated.<br /> The lack of AUROC confidence intervals and direct comparison to the reference prognostic model in the validation cohort undermines confidence in their conclusion that their new prognostic model combing gene expression data and clinical variables performs better than the reference model.

Reviewer #2 (Public Review):

Summary:

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

Strengths:

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

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

In line 386: Role of CNR2 in T cells. The finding that nearly absent CD3+ T cells in the peritoneal cavity of CNR2 ko mice is intriguing.

The interpretation of the results is well-described in the Discussion.

Weaknesses:

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

The authors also mentioned that altered eutopic endometrium contributes to the establishment and progression of endometriosis. This reviewer agrees with lines 324-325. If so, DEGs are likely identified between eutopic endometrium (with/without endometriosis lesion induction) and ectopic lesions. It would be nice to see the data (even though using publicly available data sets).

Figure 7 CDEF. The results of the statistical analyses and analyzed sample numbers should be added. Lines 444-450 cannot be reviewed without them.

This reviewer agrees with lines 498-500. In contrast, retrograded menstrual debris is not decidualized. The section could be modified to avoid misunderstanding.

Reviewer #2 (Public Review):

Liu et al., by focusing on the regulation of G protein-signaling 10 (RGS10), reported that RGS10 expression was significantly lower in patients with breast cancer, compared with normal adjacent tissue. Genetic inhibition of RGS10 caused epithelial-mesenchymal transition, and enhanced cell proliferation, migration, and invasion, respectively. These results suggest an inhibitory role of RGS10 in tumor metastasis. Furthermore, bioinformatic analyses determined signaling cascades for RGS10-mediated breast cancer distant metastasis. More importantly, both in vitro and in vivo studies evidenced that alteration of RGS10 expression by modulating its upstream regulator miR-539-5p affects breast cancer metastasis. Altogether, these findings provide insight into the pathogenesis of breast tumors and hence identify potential therapeutic targets in breast cancer.

The conclusions of this study are mostly well supported by data. However, there is a weakness in the study that needs to be clarified.

In Figure 2A, although some references supported that SKBR3 and MCF-7 possess poorly aggressive and less invasive abilities, examining only RGS10 expression in those cells, it could not be concluded that 'RGS10 acts as a tumor suppressor in breast cancer'. It would be better to introduce a horizontal comparison of the invasive ability of these 3 types of cells using an invasion assay.

Reviewer #2 (Public Review):

Summary:

Weinberg et al. show that spike LCB minibinders can be used as the extracellular domain for SynNotch, SNIPR, and CAR. They evaluated their designs against cells expressing the target proteins and live virus.

Strengths:

This is a good fundamental demonstration of alternative use of the minibinder. The results are unsurprising but robust and solid in most cases.

Weaknesses:

The manuscript would benefit from better descriptions of the study's novelty. Given that LCB previously worked in SynNotch, what unexpected finding was uncovered by this study? It is well known that the extracellular domain of CAR is amendable to different types of binding domains (e.g., scFv, nanobody, DARPin, natural ligands). So, it is not surprising that a minibinder also works with CAR. We don't know if the minibinders are more or less likely to be compatible with CAR or SNIPR.

The demonstrations are all done using just 1 minibinder. It is hard to conclude that minibinders, as a unique class of protein binders, are generalizable in different contexts. All it can conclude is that this specific Spike minibinder can be used in synNotch, SNIPR, and CAR. The LCB3 minibinder seems to be much weaker.

The sensing of live viruses is interesting, but the output is very weak. It is difficult to imagine a utility for such a weak response.

Reviewer #2 (Public Review):

Summary:

In this new paper, the authors used biochemical, structural, and biophysical methods to elucidate the mechanisms by which IP4, the PIP3 headgroup, can induce an autoinhibit form of P-Rex1 and propose a model of how PIP3 can trigger long-range conformational changes of P-Rex1 to relieve this autoinhibition. The main findings of this study are that a new P-Rex1 autoinhibition is driven by an IP4-induced binding of the PH domain to the DH domain active site and that this autoinhibit form stabilized by two key interactions between DEP1 and DH and between PH and IP4P 4-helix bundle (4HB) subdomain. Moreover, they found that the binding of phospholipid PIP3 to the PH domain can disrupt these interactions to relieve P-Rex1 autoinhibition.

Strengths:

The study provides good evidence that binding of IP4 to the P-Rex1 PH domain can make the two long-range interactions between the catalytic DH domain and the first DEP domain, and between the PH domain and the C-terminal IP4P 4HB subdomain that generate a novel P-Rex1 autoinhibition mechanism. This valuable finding adds an extra layer of P-Rex1 regulation (perhaps in the cytoplasm) to the synergistic activation by phospholipid PIP3 and the heterotrimeric Gβγ subunits at the plasma membrane. Overall, this manuscript's goal sounds interesting, the experimental data were carried out carefully and reliably.

Weakness:

The set of experiments with the disulfide bond S235C/M244C caused a bit of confusion for interpretation, it should be moved into the supplement, and the text and Figure 4 were altered accordingly.

Reviewer #2 (Public Review):

This manuscript describes an adaptive laboratory evolution (ALE) study with a previously constructed genome-reduced E. coli. The growth performance of the end-point lineages evolved in M63 medium was comparable to the full-length wild-type level at lower cell densities.

Subsequent mutation profiling and RNA-Seq analysis revealed many changes on the genome and transcriptomes of the evolved lineages. The authors did a great deal on analyzing the patterns of evolutionary changes between independent lineages, such as the chromosomal periodicity of transcriptomes, pathway enrichment analysis, weight gene co-expression analysis, and so on. They observed a striking diversity in the molecular characteristics amongst the evolved lineages, which, as they suggest, reflect divergent evolutionary strategies adopted by the genome-reduced organism.

As for the overall quality of the manuscript, I am rather torn. The manuscript leans towards elaborating observed findings, rather than explaining their biological significance. For this reason, readers are left with more questions than answers. For example, fitness assay on reconstituted (single and combinatorial) mutants was not performed, nor any supporting evidence on the proposed contributions of each mutants provided. This leaves the nature of mutations - be them beneficial, neutral or deleterious, the presence of epistatic interactions, and the magnitude of fitness contribution, largely elusive. Also, it is difficult to tell whether the RNA-Seq analysis in this study managed to draw biologically meaningful conclusions, or instill insight into the nature of genome-reduced bacteria. The analysis primarily highlighted the differences in transcriptome profiles among each lineage based on metrics such as 'DEG counts' and the 'GO enrichment'. However, I could not see any specific implications regarding the biology of the evolved minimal genome drawn. In their concluding remark, 'Multiple evolutionary paths for the reduced genome to improve growth fitness were likely all roads leading to Rome,' the authors observed the first half of the sentence, but the distinctive characteristics of 'all roads' or 'evolutionary paths', which I think should have been the key aspect in this investigation, remains elusive.

Comments on revised version:

I appreciate the author's responses. They responded to most of the comments, but I still think that there is room for improvement. Please refer to the following comments. Quoted below are the author's responses.

"We agree that our study leaned towards elaborating observed findings rather than explaining the detailed biological mechanisms."<br /> - Comment: I doubt if there are scientific merits in merely elaborating observed findings. The conclusion of this study suggests that evolutionary paths in reduced genomes are highly diverse. But if you think about the nature of adaptive evolution, which relies upon the spontaneous mutation event followed by selection, certain degree of divergence is always expected. The problem with current experimental setting is that there are no ways to quantitively assess whether the degree of evolutionary divergence increases as the function of genome reduction, as the authors claimed. In addition, this notion is in direct contradiction to the prediction that genome reduction constraints evolution by reducing the number of solution space. It is more logical to think and predict that genome reduction would, in turn, lead to the loss of evolutionary divergence. We are also interested to know whether solution space to the optimization problem altered in response to the genome reduction. In this regard, a control ALE experiment on non-reduced wild-type seems to be a mandatory experimental control. I highly suggest that authors present a control experiment, as it was done for "JCVI syn3.0B vs non-minimal M. mycoides" (doi: 10.1038/s41586 023 06288 x) and "E. coli eMS57 vs MG1655" (doi: 10.1038/s41467 019 08888 6).<br /> "We focused on the genome wide biological features rather than the specific biological functions."<br /> - Comment: The 'biological features' delivered in current manuscript does not give insight as to which genomic changes translated into strain fitness improvement. Rather than explaining the genotype-phenotype relationships and/or the mechanistic basis of fitness improvement, authors merely elaborated on the observed phenotypes. I question the scientific merits of such 'findings'.<br /> "Although the reduced growth rate caused by genome reduction could be recovered by experimental evolution, it remains unclear whether such an evolutionary improvement in growth fitness was a general feature of the reduced genome and how the genome wide changes occurred to match the growth fitness increase."<br /> - Comment: This response is very confusing to understand. "it remains unclear whether such an evolutionary improvement in growth fitness was a general feature of the reduced genome" - what aspects remain unclear?? What assumption led the authors to believe that reduced genome's fitness cannot be evolutionarily improved?<br /> - Comment: "and how the genome wide changes occurred to match the growth fitness increase" - this is exactly the aspect that authors should deliver, instead of just elaborating the observed findings. Why don't authors select one or two fastest-growing (or the fittest) lineages and specifically analyze underlying adaptive changes (i.e. genotype-phenotype relationships)?

Reviewer #2 (Public Review):

Summary:

In this manuscript, the authors provide evidence that posttranslational modification of synuclein by N-acetylation increases clustering of synaptic vesicles in vitro. When using liposomes the authors found that while clustering is enhanced by the presence of either lysophosphatidylcholine (LPC) or phosphatidylcholine in the membrane, N-acetylation enhanced clustering only in the presence of LPC. Enhancement of binding was also observed when LPC micelles were used, which was corroborated by increased intra/intermolecular cross-linking of N-acetylated synuclein in the presence of LPC.

Strengths:

It is known for many years that synuclein binds to synaptic vesicles but the physiological role of this interaction is still debated. The strength of this manuscript is clearly in the structural characterization of the interaction of synuclein and lipids (involving NMR-spectroscopy) showing that the N-terminal 100 residues of synuclein are involved in LPC-interaction, and the demonstration that N-acetylation enhances the interaction between synuclein and LPC.

Weaknesses:

Lysophosphatides form detergent-like micelles that destabilize membranes, with their steady-state concentrations in native membranes being low, questioning the significance of the findings. Oddly, no difference in binding between the N-acetylated and unmodified form was observed when the acidic phospholipid phosphatidylserine was included. It remains unclear to which extent binding to LPC is physiologically relevant, particularly in the light of recent reports from other laboratories showing that synuclein may interact with liquid-liquid phases of synapsin I that were reported to cause vesicle clustering.

Reviewer #2 (Public Review):

In this study, Badugu et al investigate the Rev7 roles in regulating the Mre11-Rad50-Xrs2 complex and in the metabolism of G4 structures. The authors also try to make a conclusion that REV7 can regulate the DSB repair choice between homologous recombination and non-homologous end joining.

The major observations of this study are:

(1) Rev7 interacts with the individual components of the MRX complex in a two-hybrid assay and in a protein-protein interaction assay (microscale thermophoresisi) in vitro.<br /> (2) Modeling using AlphaFold-Multimier also indicated that Rev7 can interact with Mre11 and Rad50.<br /> (3) Using a two-hybrid assay, a 42 C terminal domain in Rev7 responsible for the interaction with MRX was identified.<br /> (4) Rev7 inhibits Mre11 nuclease and Rad50 ATPase activities in vitro.<br /> (5) Rev 7 promotes NHEJ in plasmid cutting/relegation assay.<br /> (6) Rev7 inhibits recombination between chromosomal ura3-1 allele and plasmid ura3 allele containing G4 structure.<br /> (7) Using an assay developed in V. Zakian's lab, it was found that rev7 mutants grow poorly when both G4 is present in the genome and yeast are treated with HU.<br /> (8) In vitro, purified Rev7 binds to G4-containing substrates.

In general, a lot of experiments have been conducted, but the major conclusion about the role of Rev7 in regulating the choice between HR and NHEJ is not justified.

(1) Two stories that do not overlap (regulation of MRX by Rev7 and Rev7's role in G4 metabolism) are brought under one umbrella in this work. There is no connection unless the authors demonstrate that Rev7 inhibits the cleavage of G4 structures by the MRX complex.

(2) The authors cannot conclude based on the recombination assay between G4-containing 2-micron plasmid and chromosomal ura3-1 that Rev7" completely abolishes DSB-induced HR". First of all, there is no evidence that DSBs are formed at G4. Why is there no induction of recombination when cells are treated with HU? Second, as the authors showed, Rev7 binds to G4, therefore it is not clear if the observed effects are the result of Rev7 interaction with G4 or its impact on HR. The established HO-based assays where the speed of resection can be monitored (e.g., Mimitou and Symington, 2010) have to be used to justify the conclusion that Rev7 inhibits MRX nuclease activity in vivo.

Reviewer #2 (Public Review):

Summary:

In their manuscript "Released Bacterial ATP Shapes Local and Systemic Inflammation during Abdominal Sepsis", Daniel Spari et al. explored the dual role of ATP in exacerbating sepsis, revealing that ATP from both host and bacteria significantly impacts immune responses and disease progression.

Strengths:<br /> The study meticulously examines the complex relationship between ATP release and bacterial growth, membrane integrity, and how bacterial ATP potentially dampens inflammatory responses, thereby impairing survival in sepsis models. Additionally, this compelling paper implies a concept that bacterial OMVs act as vehicles for the systemic distribution of ATP, influencing neutrophil activity and exacerbating sepsis severity.

Weaknesses:

(1) The researchers extracted and cultivated abdominal fluid on LB agar plates, then randomly picked 25 colonies for analysis. However, they did not conduct 16S rRNA gene amplicon sequencing on the fluid itself. It is worth noting that the bacterial species present may vary depending on the individual patients. It would be beneficial if the authors could specify whether they've verified the existence of unculturable species capable of secreting high levels of Extracellular ATP.

(2) Do mice lacking commensal bacteria show a lack of extracellular ATP following cecal ligation puncture?

(3) The authors isolated various bacteria from abdominal fluid, encompassing both Gram-negative and Gram-positive types. Nevertheless, their emphasis appeared to be primarily on the Gram-negative E. coli. It would be beneficial to ascertain whether the mechanisms of Extracellular ATP release differ between Gram-positive and Gram-negative bacteria. This is particularly relevant given that the Gram-positive bacterium E. faecalis, also isolated from the abdominal fluid, is recognized for its propensity to release substantial amounts of Extracellular ATP.

(4) The authors observed changes in the levels of LPM, SPM, and neutrophils in vivo. However, it remains uncertain whether the proliferation or migration of these cells is modulated or inhibited by ATP receptors like P2Y receptors. This aspect requires further investigation to establish a convincing connection.

(5) Additionally, is it possible that the observed in vivo changes could be triggered by bacterial components other than Extracellular ATP? In this research field, a comprehensive collection of inhibitors is available, so it is desirable to utilize them to demonstrate clearer results.

(6) Have the authors considered the role of host-derived Extracellular ATP in the context of inflammation?

(7) The authors mention that Extracellular ATP is rapidly hydrolyzed by ectonucleotases in vivo. Are the changes of immune cells within the peritoneal cavity caused by Extracellular ATP released from bacterial death or by OMVs?

(8) In the manuscript, the sample size (n) for the data consistently remains at 2. I would suggest expanding the sample size to enhance the robustness and rigor of the results.

Reviewer #2 (Public Review):

Summary:

This work has an important and ambitious goal: understanding the effects of drugs, in this case antimicrobial molecules, from a holistic perspective. This means that the effect of drugs on a group of genes and whole metabolic pathways is unveiled, rather than its immediate effect on a protein target only. To achieve this goal the authors successfully implement the PISA-Express method (Protein Integral Solubility Alteration), using combined transcriptomics, proteomics, and drug-induced changes in protein stability to retrieve a large number of genes and proteins affected by the used compounds. The compounds used in the study (compound IVa, IVb, IVj, and IVk) were all derived from the precursors compound IV, they are effective against Helicobacter pylori, and their mode of action on clusters of genes and proteins has been compared to the one of the known pylori drug metronidazole (MNZ). Due to this comparison, and confirmed by the diversity of responses induced by these very similar compounds, it can be understood that the approach used is reliable and very informative. Notably, although all compound IV derivatives were designed to target pylori Flavodoxin (Fld), only one showed a statistically significant shift of Fld solubility (compound IVj, FIG S11). For most other compounds, instead, the involvement of other possible targets affecting diverse metabolic pathways was also observed, notably concerning a series of genes with other important functions: CagA (virulence factor), FtsY/FtsA (cell division), AtpD (ATP-synthase complex), the essential GTPase ObgE, Tig (protein export), as well as other proteins involved in ribosomal synthesis, chemotaxis/motility and DNA replication/repairs. Finally, for all tested molecules, in vivo functional data have been collected that parallel the omics predictions, comforting them and showing that compound IV derivatives differently affect cellular generation of reactive oxygen species (ROS), oxygen consumption rates (OCR), DNA damage, and ATP synthesis.

Strengths:

The approach used is very potent in retrieving the effects of chemically active molecules (in this case antimicrobial ones) on whole cells, evidencing protein and gene networks that are involved in cell sensitivity to the studied molecules. The choice of these compounds against H. pylori is perfect, showcasing how different the real biological response is, compared to the hypothetical one. In fact, although all molecules were retrieved based on their activity on Fld, the authors unambiguously show that large unexpected gene clusters may, and in fact are, affected by these compounds, and each of them in different manners.

Impact:

The present work is the first report relying on PISA-Express performed on living bacterial cells. Because of its findings, this work will certainly have a high impact on the way we design research to develop effective drugs, allowing us to understand the fine effects of a drug on gene clusters, drive molecule design towards specific metabolic pathways, and eventually better plan the combination of multiple active molecules for drug formulation. Beyond this, however, we expect this article to impact other related and unrelated fields of research as well. The same holistic approaches might also allow gaining deep, and sometimes unexpected, insight into the cellular targets involved in drug side effects, drug resistance, toxicity, and cellular adaptation, in fields beyond the medicinal one, such as cellular biology and environmental studies on pollutants.

Reviewer #2 (Public Review):

The manuscript by Ma et al. reports the identification of three unrelated people who are heterozygous for de novo missense variants in PLCG1, which encodes phospholipase C-gamma 1, a key signaling protein. These individuals present with partially overlapping phenotypes including hearing loss, ocular pathology, cardiac defects, abnormal brain imaging results, and immune defects. None of the patients present with all of the above phenotypes. PLCG1 has also been implicated as a possible driver for cell proliferation in cancer.

The three missense variants found in the patients result in the following amino acid substitutions: His380Arg, Asp1019Gly, and Asp1165Gly. PLCG1 (and the closely related PLCG2) have a single Drosophila ortholog called small wing (sl). sl-null flies are viable but have small wings with ectopic wing veins and supernumerary photoreceptors in the eye. As all three amino acids affected in the patients are conserved in the fly protein, in this work Ma et al. tested whether they are pathogenic by expressing either reference or patient variant fly or human genes in Drosophila and determining the phenotypes produced by doing so.

Expression in Drosophila of the variant forms of PLCG1 found in these three patients is toxic; highly so for Asp1019Gly and Asp1165Gly, much more modestly for His380Arg. Another variant, Asp1165His which was identified in lymphoma samples and shown by others to be hyperactive, was also found to be toxic in the Drosophila assays. However, a final variant, Ser1021Phe, identified by others in an individual with severe immune dysregulation, produced no phenotype upon expression in flies.

Based on these results, the authors conclude that the PLCG1 variants found in patients are pathogenic, producing gain-of-function phenotypes through hyperactivity. In my view, the data supporting this conclusion are robust, despite the lack of a detectable phenotype with Ser1021Phe, and I have no concerns about the core experiments that comprise the paper.

Figure 6, the last in the paper, provides information about PLCG1 structure and how the different variants would affect it. It shows that the His380, Asp1019, and Asp1165 all lie within catalytic domains or intramolecular interfaces and that variants in the latter two affect residues essential for autoinhibition. It also shows that Ser1021 falls outside the key interface occupied by Asp1019, but more could have been said about the potential effects of Ser1021Phe.

Overall, I believe the authors fully achieved the aims of their study. The work will have a substantial impact because it reports the identification of novel disease-linked genes, and because it further demonstrates the high value of the Drosophila model for finding and understanding gene-disease linkages.

Reviewer #2 (Public Review):

Summary:

Casas-Tinto et al., provide new insight into glial plasticity using a crush injury paradigm in the ventral nerve cord (VNC) of adult Drosophila. The authors find that both astrocyte-like glia (ALG) and ensheating glia (EG) divide under homeostatic conditions in the adult VNC and identify ALG as the glial population that specifically ramps up proliferation in response to injury, whereas the number of EGs decreases following the insult. Using lineage-tracing tools, the authors interestingly observe the interconversion of glial subtypes, especially of EGs into ALGs, which occurs independent of injury and is dependent on the availability of the transcription factor Prospero in EGs, adding to the plasticity observed in the system. Finally, when tracing the progeny of differentiated glia, Casas-Tinto and colleagues detect cells of neuronal identity and provide evidence that such glia-derived neurogenesis is specifically favored following ventral nerve cord injury, which puts forward a remarkable way in which glia can respond to neuronal damage.

Strengths:

This study highlights a new facet of adult nervous system plasticity at the level of the ventral nerve cord, supporting the view that proliferative capacity is maintained in the mature CNS and stimulated upon injury.

The injury paradigm is well chosen, as the organization of the neuromeres allows specific targeting of one segment, compared to the remaining intact, and with the potential to later link observed plasticity to behavior such as locomotion.

Numerous experiments have been carried out in 7-day-old flies, showing that the observed plasticity is not due to residual developmental remodeling or a still immature VNC.

By elegantly combining different genetic tools, the authors show glial divisions with mitotic-dependent tracing and find that the number of generated glia is refined by apoptosis later on.

The work identifies Prospero in glia as an important coordinator of glial cell fate, from development to the adult context, which draws further attention to the upstream regulatory mechanisms.

Weaknesses:

Although the authors do use a variety of methods to show glial proliferation, the EdU data (Figure 1B) could be more informative (Figure 1B) by displaying images of non-injured animals and providing quantifications or the mention of these numbers based on results previously acquired in the system.

The experiments relying on the FUCCI cell cycle reporter suggested considerable baseline proliferation for EGs and ALGs, but when using an independent method (Twin Spot MARCM), mitotic marking was only detected for ALGs. This discrepancy could be addressed by assessing the co-localization of the different glia subsets using the identified driver lines with mitotic markers such as PH3.

The data in Figure 1C would be more convincing in combination with images of the FUCCI Reporter as it can provide further information on the location and proportion of glia that enter the cell cycle versus the fraction that remains quiescent.

The analyses of inter-glia conversion in Figure 3 are complicated by the fact that Prospero RNAi is both used to suppress EG - to ALG conversion and as a marker to establish ALG nature. Clarifications if the GFP+ cells still expressed Pros or were classified as NP-like GFP cells are required here.

The conclusion that ALG and EG glial cells can give rise to cells of neuronal lineage is based on glial lineage information (GFP+ cells from glial G-trace) and staining for the neuronal marker Elav. The use of other neuronal markers apart from Elav or morphological features would provide a more compelling case that GFP+ cells are mature neurons.

Although the text discusses in which contexts, glial plasticity is observed or increased upon injury, the figures are less clear regarding this aspect. A more systematic comparison of injured VNCs versus homeostatic conditions, combined with clear labelling of the injury area would facilitate the understanding of the panels.

Context/Discussion

The study finds that glia in the ventral cord of flies have latent neurogenic potential. Such observations have not been made regarding glia in the fly brain, where injury is reported to drive glial divisions or the proliferation of undifferentiated progenitor cells with neurogenic potential.

Discussing this different strategy for cell replacement adopted by glia in the VNC and pointing out differences to other modes seems fascinating. Highlighting differences in the<br /> the reactiveness of glia in the VNC compared to the brain also seems highly relevant as they may point to different properties to repair damage.

Based on the assays employed, the study points to a significant amount of glial "identity" changes or interconversions, which is surprising under homeostatic conditions. The significance of this "baseline" plasticity remains undiscussed, although glia unarguably show extensive adaptations during nervous system development.

It would be interesting to know if the "interconversion" of glia is determined by the needs in the tissue or would shift in the context of selective ablation/suppression of a glial type.

Reviewer #2 (Public Review):

Summary:

The authors provide strong evidence that bacteria, such as E. coli, compete with tumor cells for iron resources and consequently reduce tumor growth. When sequestration between LCN2 and bacterobactin is blocked by upregulating CDG(DGC-E. coli) or salmochelin(IroA-E.coli), E. coli increase iron uptake from the tumor microenvironment (TME) and restrict iron availability for tumor cells. Long-term remission in IroA-E.coli treated mice is associated with enhanced CD8+ T cell activity. Additionally, systemic delivery of IroA-E.coli shows a synergistic effect with chemotherapy reagent oxaliplatin to reduce tumor growth.

Strengths:

It is important to identify the iron-related crosstalk between E. coli and TME. Blocking lcn2-bacterobactin sequestration by different strategies consistently reduce tumor growth.

Weaknesses:

As engineered E.coli upregulate their function to uptake iron, they may increase the likelihood of escaping from nutritional immunity (LCN2 becomes insensitive to sequester iron from the bacteria). Would this raise the chance of developing sepsis? Do authors think that it is safe to administrate these engineered bacteria in mice or humans?

Reviewer #2 (Public Review):

The goal of the present study is to better understand the 'control objectives' that subjects adopt in a video-game-like virtual-balancing task. In this task, the hand must move in the opposite direction from a cursor. For example, if the cursor is 2 cm to the right, the subject must move their hand 2 cm to the left to 'balance' the cursor. Any imperfection in that opposition causes the cursor to move. E.g., if the subject were to move only 1.8 cm, that would be insufficient, and the cursor would continue to move to the right. If they were to move 2.2 cm, the cursor would move back toward the center of the screen. This return to center might actually be 'good' from the subject's perspective, depending on whether their objective is to keep the cursor still or keep it near the screen's center. Both are reasonable 'objectives' because the trial fails if the cursor moves too far from the screen's center during each six-second trial.

This task was recently developed for use in monkeys (Quick et al., 2018), with the intention of being used for the study of the cortical control of movement, and also as a task that might be used to evaluate BMI control algorithms. The purpose of the present study is to better characterize how this task is performed. What sort of control policies are used. Perhaps more deeply, what kind of errors are those policies trying to minimize? To address these questions, the authors simulate control-theory style models and compare with behavior. They do in both in monkeys and in humans.

These goals make sense as a precursor to future recording or BMI experiments. The primate motor-control field has long been dominated by variants of reaching tasks, so introducing this new task will likely be beneficial. This is not the first non-reaching task, but it is an interesting one and it makes sense to expand the presently limited repertoire of tasks. The present task is very different from any prior task I know of. Thus, it makes sense to quantify behavior as thoroughly as possible in advance of recordings. Understanding how behavior is controlled is, as the authors note, likely to be critical to interpreting neural data.

From this perspective - providing a basis for interpreting future neural results - the present study is fairly successful. Monkeys seem to understand the task properly, and to use control policies that are not dissimilar from humans. Also reassuring is the fact that behavior remains sensible even when task-difficulty become high. By 'sensible' I simply mean that behavior can be understood as seeking to minimize error: position, velocity, or (possibly) both, and that this remains true across a broad range of task difficulties. The authors document why minimizing position and minimizing velocity are both reasonable objectives. Minimizing velocity is reasonable, because a near-stationary cursor can't move far in six seconds. Minimizing position error is reasonable, because the trial won't fail if the cursor doesn't stray far from the center. This is formally demonstrated by simulating control policies: both objectives lead to control policies that can perform the task and produce realistic single-trial behavior. The authors also demonstrate that, via verbal instruction, they can induce human subjects to favor one objective over the other. These all seem like things that are on the 'need to know' list, and it is commendable that this amount of care is being taken before recordings begin, as it will surely aid interpretation.

Yet as a stand-alone study, the contribution to our understanding of motor control is more limited. The task allows two different objectives (minimize velocity, minimize position) to be equally compatible with the overall goal (don't fail the trial). Or more precisely, there exists a range of objectives with those two at the extreme. So it makes sense that different subjects might choose to favor different objectives, and also that they can do so when instructed. But has this taught us something about motor control, or simply that there is a natural ambiguity built into the task? If I ask you to play a game, but don't fully specify the rules, should I be surprised that different people think the rules are slightly different?

The most interesting scientific claim of this study is not the subject-to-subject variability; the task design makes that quite likely and natural. Rather, the central scientific result is the claim that individual subjects are constantly switching objectives (and thus control policies), such that the policy guiding behavior differs dramatically even on a single-trial basis. This scientific claim is supported by a technical claim: that the authors' methods can distinguish which objective is in use, even on single trials. I am uncertain of both claims.

Consider Figure 8B, which reprises a point made in Figure 1&3 and gives the best evidence for trial-to-trial variability in objective/policy. For every subject, there are two example trials. The top row of trials shows oscillations around the center, which could be consistent with position-error minimization. The bottom row shows tolerance of position errors so long as drift is slow, which could be consistent with velocity-error minimization. But is this really evidence that subjects were switching objectives (and thus control policies) from trial to trial? A simpler alternative would be a single control policy that does not switch, but still generates this range of behaviors. The authors don't really consider this possibility, and I'm not sure why. One can think of a variety of ways in which a unified policy could produce this variation, given noise and the natural instability of the system.

Indeed, I found that it was remarkably easy to produce a range of reasonably realistic behaviors, including the patterns that the authors interpret as evidence for switching objectives, based on a simple fixed controller. To run the simulations, I made the simple assumption that subjects simply attempt to match their hand position to oppose the cursor position. Because subjects cannot see their hand, I assumed modest variability in the gain, with a range from -1 to -1.05. I assumed a small amount of motor noise in the outgoing motor command. The resulting (very simple) controller naturally displayed the basic range of behaviors observed across trials (see Image 1)

Image 1.

Some trials had oscillations around the screen center (zero), which is the pattern the authors suggest reflects position control. In other trials the cursor was allowed to drift slowly away from the center, which is the pattern the authors suggest reflects velocity control. This is true even though the controller was the same on every trial. Trial-to-trial differences were driven both by motor noise and by the modest variability in gain. In an unstable system, small differences can lead to (seemingly) qualitatively different behavior on different trials.

This simple controller is also compatible with the ability of subjects to adapt their strategy when instructed. Anyone experienced with this task likely understands (or has learned) that moving the hand slightly more than 'one should' will tend to shepherd the cursor back to center, at the cost of briefly high velocity. Using this strategy more sparingly will tend to minimize velocity even if position errors persist. Thus, any subject using this control policy would be able to adapt their strategy via a modest change in gain (the gain linking visible cursor position to intended hand position).

This model is simple, and there may be reasons to dislike it. But it is presumably a reasonable model. The nature of the task is that you should move your hand opposite where the cursor is. Because you can't see your hand, you will make small mistakes. Due to the instability of the system, those small mistakes have large and variable effects. This feature is likely common to other controllers as well; many may explicitly or implicitly blend position and velocity control, with different trials appearing more dominated by one versus the other. Given this, I think the study presents only weak evidence that individual subjects are switching their objective on individual trials. Indeed, the more parsimonious explanation may be that they aren't. While the study certainly does demonstrate that the control policy can be influenced by verbal instructions, this might be a small adjustment as noted above.

I thus don't feel convinced that the authors can conclusively tell us the true control policy being used by human and monkey subjects, nor whether that policy is mostly fixed or constantly switching. The data are potentially compatible with any of these interpretations, depending on which control-style model one prefers.

I see a few paths that the authors might take if they chose.<br /> --First, my reasoning above might be faulty, or there might be additional analyses that could rule out the possibility of a unified policy underlying variable behavior. If so, the authors may be able to reject the above concerns and retain the present conclusions. The main scientifically novel conclusion of the present study is that subjects are using a highly variable control policy, and switching on individual trials. If this is indeed the case, there may be additional analyses that could reveal that.<br /> --Second, additional trial types (e.g., with various perturbations) might be used as a probe of the control policy. As noted below, there is a long history of doing this in the pursuit system. That additional data might better disambiguate control policies both in general, and across trials.<br /> --Third, the authors might find that a unified controller is actually a good (and more parsimonious) explanation. Which might actually be a good thing from the standpoint of future experiments. Interpretation of neural data is likely to be much easier if the control policy being instantiated isn't in constant flux.

In any case, I would recommend altering the strength of some conclusions, particularly the conclusion that the presented methods can reliably discriminate amongst objectives/policies on individual trials. This is mentioned as a major motivation on multiple occasions, but in most of these instances, the subsequent analysis infers the objective only across trial (e.g., one must observe a scatterplot of many trials). By Figure 7, they do introduce a method for inferring the control policy on individual trials, and while this seems to work considerably better than chance, it hardly appears reliable.

In this same vein I would suggest toning down aspects of the Introduction and Discussion. The Introduction in particular is overly long, and tries to position the present study as unique in ways that seem strained. Other studies have built links between human behavior, monkey behavior, and monkey neural data (for just one example, consider the corpus of work from the Scott lab that includes Pruszynski et al. 2008 and 2011). Other studies have used highly quantitative methods to infer the objective function used by subjects (e.g. Kording and Wolpert 2004). The very issue that is of interest in the present study - velocity-error-minimization versus position-error-minimization - has been extensively addressed in the smooth pursuit system. That field has long combined quantitative analyses of behavior in humans and monkeys, along with neural recordings. Many pursuit experiments used strategies that could be fruitfully employed to address the central questions of the present study. For example, error stabilization was important for dissecting the control policy used by the pursuit system. By artificially stabilizing the error (position or velocity) at zero, or at some other value, one can determine the system's response. The classic Rashbass step (1961) put position and velocity errors in opposition, to see which dominates the response. Step and sinusoidal perturbations were useful in distinguishing between models, as was the imposition of artificially imposed delays. The authors note the 'richness' of the behavior in the present task, and while one could say the same of pursuit, it was still the case that specific and well-thought through experimental manipulations were pretty critical. It would be better if the Introduction considered at least some of the above-mentioned work (or other work in a similar vein). While most would agree with the motivations outlined by the authors - they are logical and make sense - the present Introduction runs the risk of overselling the present conclusions while underselling prior work.

Reviewer #2 (Public Review):

Summary

The paper concerns the phenomenon of continuous flash suppression (CFS), relevant to questions about the extent and nature of subconscious visual processing. Whereas standard CFS studies only measure the breakthrough threshold-the contrast at which an initially suppressed target stimulus with steadily increasing contrast becomes visible-this study also measures the re-suppression threshold, the contrast at which a visible target with decreasing contrast becomes suppressed. Thus, the authors could calculate suppression depth, the ratio between the breakthrough and re-suppression thresholds. To measure both thresholds, the study introduces the tracking-CFS method, a continuous-trial design that results in faster, better controlled, and lower-variance threshold estimates compared to the discrete trials standard in the literature. The study finds that suppression depths are similar for different image categories, providing an interesting contrast to previous results that breakthrough thresholds differ for different image categories. The new finding calls for a reassessment of interpretations based solely on the breakthrough threshold that subconscious visual processing is category-specific.

Strengths

(1) The tCFS method quickly estimates breakthrough and re-suppression thresholds using continuous trials, which also better control for slowly varying factors such as adaptation and attention. Indeed, tCFS produces estimates with lower across-subject variance than the standard discrete-trial method (Fig. 2). The tCFS method is straightforward to adopt in future research on CFS and binocular rivalry.

(2) The CFS literature has lacked re-suppression threshold measurements. By measuring both breakthrough and re-suppression thresholds, this work calculated suppression depth (i.e., the difference between the two thresholds), which warrants different interpretations from the breakthrough threshold alone.

(3) The work found that different image categories show similar suppression depths, suggesting some aspects of CFS are not category-specific. This result enriches previous findings that breakthrough thresholds vary with image categories. Re-suppression thresholds vary symmetrically, such that their differences are constant.

Weakness

I do not follow the authors' reasoning as to why the suppression depth is a better (or fuller, superior, more informative) indication of subconscious visual processing than the breakthrough threshold alone. To my previous round of comments, the authors replied that 'breakthrough provides only half of the needed information.' I do not understand this. One cannot infer the suppression depth from the breakthrough threshold alone, but *one cannot obtain the breakthrough threshold from the suppression depth alone*, either. The two measures are complementary. (To be sure, given *both* the suppression depth and the re-suppression threshold, one can recover the breakthrough threshold. The discussion concerns the suppression depth *alone* and the breakthrough threshold *alone*.) I am fully open to being convinced that there is a good reason why the suppression depth may be more informative than the breakthrough threshold about a specific topic, e.g., inter-ocular suppression or subconscious visual processing. I only request that the authors make such an argument explicit. For example, in the significance statement, the authors write, 'all images show equal suppression when both thresholds are measured. We *thus* find no evidence of differential unconscious processing and *conclude* reliance on breakthrough thresholds is misleading' (emphasis added). Just what supports the 'thus' and the 'conclude'? Similarly, at the end of the introduction, the authors write, '[...] suppression depth was constant for faces, objects, gratings and visual noise. *In other words*, we find no evidence to support differential unconscious processing among these particular, diverse categories of suppressed images' (emphasis added). I am not sure the statements in the two sentences are equivalent.

The authors' reply included a discussion of neural CRFs, which may explain why the bCFS thresholds differ across image categories. A further step seems necessary to explain why CRFs do not qualify as a form of subconscious processing.