Reviewer #2 (Public Review):

In this manuscript, the authors conducted a study in which they measured eye movements, pupil diameter, and neural activity in V4 in monkeys engaged in a visual attention task. The task required the monkeys to report changes in the orientation of Gabors' visual stimuli. The authors manipulated the difficulty of the trials by varying the degree of orientation change and focused their analysis on trials of intermediate difficulty where the monkeys' hit rate was approximately 50%. Their key findings include the following: 1) Hit trials were preceded by larger pupil diameter, reflecting higher arousal, and by more stable eye positions; 2) V4 neurons exhibit larger visual responses in hit trials; 3) Superficial and deep layers exhibited greater coherence in hit trials during both the pre-target stimulus period and the non-target stimulus presentation period. These findings have useful implications for the field, and the experiments and analyses presented in this manuscript validly support the authors' claims.

Strengths:<br /> The experiments were well-designed and executed with meticulous control. The analyses of both behavioural and electrophysiological data align with the standards in the field.

Weaknesses:<br /> Many of the findings appear to be incremental compared to previous literature, including the authors' own work. While incremental findings are not necessarily a problem, the manuscript lacks clear statements about the extent to which the dataset, analysis, and findings overlap with the authors' prior research. For example, one of the main findings, which suggests that V4 neurons exhibit larger visual responses in hit trials (as shown in Fig. 3), appears to have been previously reported in their 2017 paper. Additionally, it seems that the entire Fig1-S1 may have been reused from the 2017 paper. These overlaps should have been explicitly acknowledged and correctly referenced.

Previous studies have demonstrated that attention leads to decorrelation in V4 population activity. The authors should have discussed how and why the high coherence across layers observed in the current study can coexist with this decorrelation.

Furthermore, the manuscript does not explore potentially interesting aspects of the dataset. For instance, the authors could have investigated instances where monkeys made 'false' reports, such as executing saccades towards visual stimuli when no orientation change occurred. It would be valuable to provide the fraction of the monkeys' responses in a session, including false reports and correct rejections in catch trials, to allow for a broader analysis that considers the perceptual component of neural activity over pure sensory responses.

Reviewer #1 (Public Review):

Zhu, et al present a genome-wide histone modification analysis comparing patients with schizophrenia (on or off antipsychotics) to non-psychiatric controls. The authors performed analyses across the dorsolateral prefrontal cortex and tested for enrichment of nearby genes and pathways. The authors performed an analysis measuring the effect of age on the epigenomic landscape as well. While this paper provides a unique resource around SCZ and its epigenetic correlates, and some potentially intriguing findings in the antipsychotic response dataset there were some potential missed opportunities - related to the integration of outside datasets and genotypes that could have strengthened the results and novelty of the paper.

Major Comments

1. Is there genotype data available for this cohort of donors or can it be generated? This would open several novel avenues of investigation for the authors. First the authors can test for enrichment of heritability for SCZ or even highly comorbid disorders such as bipolar. Second, it would allow the authors to directly measure the genetic regulation of histone markers by calculating QTLs (in this case histone hQTLs). The authors assert that although interesting, ATAC-seq approach does not provide the same chromatin state information as histone mods mapped by ChiP. Why do the authors not test this? There are several ATAC-seq datasets available for SCZ [https://pubmed.ncbi.nlm.nih.gov/30087329/]and an additional genomic overlap could help tease apart genetic regulation of the changes observed.

2. Can the authors theorize why their analysis found significant effects for H3K27Ac for antipsychotic use when a recent epigenomic study of SCZ using a larger cohort of samples and including the same histone modifications did not [https://pubmed.ncbi.nlm.nih.gov/30038276/]? Given the lower n and lower number of cells in this group, it would be helpful if the authors could speculate on why they see this. Do the authors know if there is any overlap with the Girdhar study donors or if there are other phenotypic differences that could account for this?

3. The reviewer is concerned about the low concordance between bulk nuclei RNA-seq and single-cell RNA-seq for SCZ (236 of 802 DEGs in NeuN+ and 63 of 1043 NEuN-). While it is not surprising for different cohorts to have different sets of DEGs these seem to be vastly different. Was there a particular cell type(s) that enriched for the authors' DEGs in the single-cell dataset? Do the authors know if any donors overlapped between these cohorts?

4. Functional enrichment analyses: details are not provided by the authors and should be added. The authors need to consider a) providing a gene universe, ie only considering the sets of genes with nearby H3K4me3/ H3K27ac levels, to such pathway tools, and b) should take into account the fact that some genes have many more peaks with data. There are known biases in seemingly just using the best p-value per gene in other epigenetic analysis (ie. DNA methylation data) and software is available to run correct analyses: https://pubmed.ncbi.nlm.nih.gov/23732277.

Reviewer #2 (Public Review):

The manuscript by Zhu has generated ChIP-seq and RNA-seq data from sizeable cohorts of SCZ patient samples and controls. The samples include 15 AF-SCZ samples and 15 controls, as well as 14 AT-SCZ samples and 14 controls. The genomics data was generated using techniques optimized for low-input samples: MOWChIP-seq and SMART-seq2 for histone profiles and transcriptome, respectively. The study has generated a significant data resource for the investigation of epigenomic alterations in SCZ. I am not convinced that the hierarchical pairwise design - first comparing AF-SCZ and AT-SCZ with their corresponding controls and secondarily contrasting the two comparisons is fully justified. The authors should repeat the statistical analysis by modeling all three groups simultaneously with an interaction effect for treatment or directly compare AF-SCZ to AT-SCZ groups and evaluate if the main conclusions remain supported.

Major comments

1. The manuscript did not discuss (mention) the quality control of RNA-seq data shown in Fig. 1B. The color scheme choice for the heatmap visualization did not provide a quantitative presentation of the specificity of the RNA-seq data. I would recommend using bar plots to present the results more quantitatively.

2. How does the specificity of this RNA-seq dataset compare to previous studies using a similar NeuN sorting strategy?

3. I appreciate the effort to assess the ChIP-seq data quality using phantompeakqualtools. However, prior knowledge/experience with this tool is required to fully understand the QC results. The authors should additionally provide browser shots at different scales for key neuronal/glial genes, so readers can have a more direct assessment of data quality, such as the enrichment of H3K4me3 at promoters (but not elsewhere), and H3K27ac at promoters and enhancers. Existing browser views, such as Fig. 2B are too zoomed out for assessing the data quality.

4. The pairwise regression model should be explicitly reported in methods.

5. The statistical strategy to compare AF-SCZ and AT-SCZ to their corresponding control groups was unjustified. Why not model all three groups simultaneously with an interaction effect for treatment or directly compare AF-SCZ to AT-SCZ groups? If the manuscript argues that the antipsychotic effect is the main novelty, why not directly compare AF-SCZ and AT-SCZ?

6. The method of pairwise comparison to corresponding control groups, then further comparing the pairwise results opens the study to a number of statistical vulnerabilities. For example, on page 12, the studies identified 166 DEGs between AF and control, and 1273 DEGs between AT and control. Instead of implicating a greater amount of difference between AT and control, such a result can often be driven by differences in between-group variance, rather than between-group means, that is, are the SCZ-AF and SCZ-treated effect size magnitudes and directionalities similar (but the treated group has lower variance) or are the two groups truly different in terms of means? The result in Fig. 5A suggests effect sizes for the two comparisons (AF-Ctrl and AT-Ctrl) are similar but have lower variability in the treated group.

7. The pairwise comparison further raised the possibility the results were driven by the difference in the two control cohorts rather than the two SCZ cohorts.

Reviewer #1 (Public Review):

Summary:<br /> The circuit mechanism underlying the formation of grid cell activity and the organization of grid cells in the medial entorhinal cortex (MEC) is still unclear. To understand the mechanism, the current study investigated synaptic interactions between stellate cells (SC) and PV+ interneurons (IN) in layer 2 of the MEC by combing optogenetic activations and paired patch-clamp recordings. The results convincingly demonstrated highly structured interactions between these neurons: specific and direct excitatory-inhibitory interactions existed at the scale of grid cell phase clusters, and indirect interactions occurred at the scale of grid modules.

Strengths:<br /> Overall, the manuscript is very well written, the approaches used are clever, and the data were thoroughly analyzed. The study conveyed important information for understanding the circuit mechanism that shapes grid cell activity. It is important not only for the field of MEC and grid cells, but also for broader fields of continuous attractor networks and neural circuits.

Weaknesses:<br /> (1) The study largely relies on the fact that ramp-like wide-field optogenetic stimulation and focal optogenetic activation both drove asynchronous action potentials in SCs, and therefore, if a pair of PV+ INs exhibited correlated activity, they should receive common inputs. However, it is unclear what criteria/thresholds were used to determine the level of activity asynchronization, and under these criteria, what percentage of cells actually showed synchronized or less asynchronized activity. A notable percentage of synchronized or less asynchronized SCs could complicate the results, i.e., PV+ INs with correlated activity could receive inputs from different SCs (different inputs), which had synchronized activity. More detailed information/statistics about the asynchronization of SC activity is necessary for interpreting the results.

(2) The hypothesis about the "direct excitatory-inhibitory" synaptic interactions is made based on the GABAzine experiments in Figure 4. In the Figure 8 diagram, the direct interaction is illustrated between PV+ INs and SCs. However, the evidence supporting this "direct interaction" between these two cell types is missing. Is it possible that pyramidal cells are also involved in this interaction? Some pieces of evidence or discussions are necessary to further support the "direction interaction".

Reviewer #1 (Public Review):

The authors used mathematical models to explore the mechanism(s) underlying the process of polar tube extrusion and the transport of the sporoplasm and nucleus through this structure. They combined this with experimental observations of the structure of the tube during extrusion using serial block face EM providing 3 dimensional data on this process. They also examined the effect of hyperosmolar media on this process to evaluate which model fit the predicted observed behavior of the polar tube in these various media solutions. Overall, this work resulted in the authors arriving at a model of this process that fit the data (model 5, E-OE-PTPV-ExP). This model is consistent with other data in the literature and provides support for the concept that the polar tube functions by eversion (unfolding like a finger of a glove) and that the expanding polar vacuole is part of this process. Finally, the authors provide important new insights into the bucking of the spore wall (and possible cavitation) as providing force for the nucleus to be transported via the polar tube. This is an important observation that has not been in previous models of this process.

Reviewer #2 (Public Review):

The paper follows a recent study by the same team (Jaroenlak et al Plos Pathogens 2020), which documented the dramatic ejection dynamics of the polar tube (PT) in microsporidia using live-imaging and scanning electron microscopy. Although several key observations were reported in this paper (the 3D architecture of the PT within the spore, the speed and extent of the ejection process, the translocation dynamics of the nucleus during germination), the precise geometry of the PT during ejection remain inaccessible to imaging, making it difficult to physically understand the phenomenon.

This paper aims to fill this gap with an indirect "data-driven" approach. By modeling the hydrodynamic dissipation for different unfolding mechanisms identified in the literature and by comparing the predictions with experiments of ejection in media of various viscosities, authors shows that data are compatible with an eversion (caterpillar-like) mechanism but not compatible with a "jack-in-the-box" scenario. In addition, the authors observe that most germinated spores exhibit an inward bulge, which they attribute to buckling due to negative pressure difference. They suggest that this buckling may be a mean of pushing the nucleus out of the PT during the final stage of ejection.

Major strengths:

The most compelling aspect of the study is the experimental analysis of the ejection dynamics (velocity, ejection length) in medium of various viscosities over 3 orders of magnitudes, which, combined with a modeling of the viscous drag of the PT tube, provides very convincing evidence that the unfolding geometry is not a global displacement of the tube but rather an apical extension, where the motion is localized at the end of the tube.

The systematic classification of the different unfolding scenarios, consistent with the previous literature, and their confrontation with data in terms of energy, pressure and velocity also constitute an original approach in microbiology, where in-situ and real time geometry is often difficult to access.

Major weaknesses:

The revised version has clarified some details of the model, adding a paragraph and a figure in the Sup Mat. However, in my opinion, it remains difficult to understand the precise topology and ejection mechanism from the various sketches presented in the article.

The article does not address the mechanical driver (force) of ejection, and the role of pressure is unclear. The revised version replaced the term "negative pressure" with "negative pressure difference", arguing that a positive or negative pressure difference could not be differentiated. However, it is not clear how a lower pressure in the spore than in the bath could eject the tube outside.

Reviewer #1 (Public Review):

In this study, the authors investigated the role of MAM and the Notch signalling pathway in the onset of the atrophic phenotype in both in vivo and in vitro models. The rationale used to obtain the data is one of the main strengths of the study. Already from the reading, the reasoning scheme used by the authors in setting up the study and evaluating the data obtained is clear. Using both cellular and mouse models in vivo consolidates the data obtained. The authors also methodologically described all the choices made in the supplementary section.

Reviewer #2 (Public Review):

In this study, the authors examined how maintenance of mitochondrial-associated endoplasmic reticulum membranes (MAM) are critical for the prevention of muscle atrophy under microgravity conditions. They observed, a reduction in MAM in myotubes placed in a microgravity condition; in addition, MFN2-deficient human iPS cells showed a decrease in the number of MAM, similar to in myotubes differentiated under microgravity conditions, in addition to the activation of the Notch signaling pathway. The authors, morover, obsreved that by treatment with the gamma-secretase inhibitor with DAPT preserved from the atrophic phenotype of differentiated myotubes in microgravity and improve the regenerative capacity of Mfn2-deficient muscle stem cells in dystrophic mice.

The entire study was well conducted, bringing an interesting analysis in vitro and in vivo of aging condition. In my opinion it is necessary to implement the analysis of both genes and proteins for better supporting the conclusions

The study can contribute to better understand one of the major problems of aging, such as muscle atrophy and inhibition of muscle regeneration, emphasizing the importance of NOTCH patway in these pathological situations. The work will be of interest to all scientist working on aging.

Joint Public Review:

The biogenesis of outer membrane proteins (OMPs) into the outer membranes of Gram-negative bacteria is not fully understood, particularly client recognition and insertion by the conserved beta-assembly machinery (BAM), which is itself integrated in the outer membranes. So far, the last strand of an OMP, referred to as the beta-signal, has been known as a primary recognition motif by BAM. Here, authors have identified additional sequence motifs that are located in the upstream of the last strand.

Here, authors carried out rigorous biochemical, biophysical, and genetic approaches to prove that the newly identified internal motifs are critical to the assembly of outer membrane proteins as well as to the interaction with the BAM complex. The identification of important regions on the substrates and Bam proteins during biogenesis is an important contribution that gives clues to the path substrates take en route to the membrane. Assessing the effect of the internal motifs in the assembly of model OMPs in the absence (in vitro) and presence (in vitro and in vivo) of BAM machinery aids a precise definition of the role of the motifs, solidifying the conclusions.

The initial reviews raised several concerns:

1. Strengthening the claim that the recognition of the internal signal by BAM is mediated by BamA and BamD via specific interactions.

2. Justification of the rationale of the peptide inhibition assays as a primary tool to identify significant recognition motifs.

3. More careful interpretation of the mutational effects on OMP assembly - that is, discerning the impairment of BAM-nascent polypeptide chain interaction from the impairment of intrinsic folding.

4. Providing further clarification of the discrepancy between in vitro assay and in vivo assay regarding the effect of the mutation Y286A on OMP assembly.

5. More elaboration on the rationale, interpretation, and representation of neutron refractory data.

6. An explanation is lacking why the strain with BamD R197A does not display VCN sensitivity in contrast to the strain with BamD Y62A.

Those concerns were well addressed in the revised manuscript in a rigorous manner.

Overall, this study comprehensively addresses an important question in the field. The notion that additional signals assist in biogenesis is a novel concept that has been tested and verified at least for a subset of model OMPs in this study. The generalization of the conclusion awaits a further proof of the concept.

Reviewer #1 (Public Review):

Summary:<br /> This manuscript examined the impact of prenatal alcohol exposure on genome-wide DNA methylation in the brain and liver, comparing ethanol-exposed mice to unexposed controls. They also investigated whether a high-methyl diet (HMD) could prevent the DNA methylation alterations caused by alcohol. Using bisulfite sequencing (n=4 per group), they identified 78 alcohol-associated differentially methylated regions (DMRs) in the brain and 759 DMRs in the liver, of which 85% and 84% were mitigated by the HMD group, respectively. The authors further validated 7 DMRs in humans using previously published data from a Canadian cohort of children with FASD.

Overall, the findings from this study provide new insight into the impact of prenatal alcohol exposure, while also showing evidence for methyl-rich diets as an intervention to prevent the effects of alcohol on the epigenome. However, several methodological concerns limit the robustness of these results and should be addressed to further strengthen the conclusions of this study and its applicability to broader settings.

Strengths:<br /> - The use of whole genome bisulfite sequencing allowed for the interrogation of the entire DNA methylome and DMR analysis, rather than a subset of CpGs.<br /> - The combination of data from animal models and humans allowed the authors to make stronger inferences regarding their findings.<br /> - The authors investigated a potential mechanism (high methyl diet) to buffer against the effects of prenatal alcohol exposure, which increases the relevance and applicability of this research.

Weaknesses:<br /> - Mistakes and discontinuities in the reporting of results and methods made the manuscript difficult to follow. There was also some overuse of causal language and overinterpretation of differences.<br /> - The authors provide insufficient details to replicate their analyses, particularly for data quality control steps and statistical analyses.<br /> - The sample size was very small for the epigenetic analyses, which limits the robustness of the findings. This limitation is further emphasized by the cutoffs used to identify DMRs, which did not include multiple test corrections and used a delta cutoff that was not supported by the sequencing depth.<br /> - The authors do not account for potential confounders in their analyses, including birthweight, alcohol levels, and sex. This is a particular problem for the high-methyl diet analyses, in which the alcohol-exposed mice seemed to consume less alcohol than their non-diet counterparts.

Reviewer #2 (Public Review):

Summary:<br /> Bestry et al. investigated the effects of prenatal alcohol exposure (PAE) and high methyl donor diet (HMD) on offspring DNA methylation and behavioral outcomes using a mouse model that mimics common patterns of alcohol consumption in pregnancy in humans. The researchers employed whole-genome bisulfite sequencing (WGBS) for unbiased assessment of the epigenome in the newborn brain and liver, two organs affected by ethanol, to explore tissue-specific effects and to determine any "tissue-agnostic" effects that may have arisen prior to the germ-layer commitment during early gastrulation. The authors found that PAE induces measurable changes in offspring DNA methylation. DNA methylation changes induced by PAE coincide with non-coding regions, including enhancers and promoters, with the potential to regulate gene expression. Though the majority of the alcohol-sensitive differentially methylated regions (DMRs) were not conserved in humans, the ones that were conserved were associated with clinically relevant traits such as facial morphology, educational attainment, intelligence, autism, and schizophrenia. Finally, the study provides evidence that maternal dietary support with methyl donors alleviates the effects of PAE on DNA methylation, suggesting a potential prenatal care option.

Strengths:<br /> The strengths of the study include the use of a mouse model where confounding factors such as genetic background and diet can be well controlled. The study performed whole-genome bisulfite sequencing which allows a comprehensive analysis of the effects of PAE on DNA methylation. However, some weaknesses and limitations of the study are detected.

Weaknesses:<br /> 1. The low generalizability between mouse and human data alerts the validity of the mouse model designed in the study. On the same note, the authors failed to detect any significant effect on PAE-induced behavioral outcomes. I recognize that it is difficult to model all possible conditions of PAE in mice because the amount, frequency, and duration of alcohol consumption in humans vary significantly. Therefore, if the authors only focus on moderate PAE, it should be emphasized in the title and throughout the paper to avoid misinterpretation. In addition, is it possible to stratify the human data based on the level of PAE and compare it to the mouse data?<br /> 2. A major finding of the study is that PAE affects non-coding genomic regions in mice including enhancers and promoters. To improve the significance of the study, the authors need to back up this finding with transcriptome analysis and determine if these DMRs indeed affect gene expression.<br /> 3. The low generalizability between mouse and human data suggests that the regions affected by PAE may be species-specific. It is critical to analyze if PAE-induced DMRs in humans are also enriched in non-coding genomic regions. Considering the huge difference between mouse and human development, particularly in the brain, it is not surprising that different genomic loci are affected, but the affected loci may share similar features.<br /> 4. The specific brain regions and the lobes of the liver where the samples were taken should be clearly indicated.<br /> 5. I don't fully agree with the authors' interpretation that the two shared genomic regions affected in the brain and the liver "must have arisen before the germ layers separated". To claim so, the authors need to exclude the possibility that the two regions are just a coincidence due to the stochastic effect of PAE on DNA methylation.

Reviewer #1 (Public Review):

Summary:<br /> In their manuscript, Massa and colleagues provide a map of the epigenetic landscape in podocytes and analyze the role of the transcription factor MafB in podocyte gene expression. They initially map the histone profile in adult podocytes of the mouse by assaying three different histone methylation marks, namely H3K4me3, H3K4me1, and H3K27me3 for active, primed, and repressed states. They then perform Wt1- and MafB-ChIP-Seq analysis to identify respective direct targets of those transcription factors. Subsequently, they employ an inducible MafB knockout model and show that homozygous knockout mice show proteinuria and FSGS, suggesting an important role for MafB in podocyte homeostasis. RNA-Seq analysis in mice two days after tamoxifen application identified direct and indirect MafB target genes. Finally, the authors turn to a constitutive MafB knockout model, carry out anti-H3K4me3 and anti-Wt1 ChIP experiments, and examine selected promoters. One main conclusion from this work is that MafB opens chromatin and thus facilitates the binding of other transcription factors like Wt1 to podocyte-specific genes.

Strengths and weaknesses:<br /> The authors have performed an impressive number of experiments and generated very valuable data. They use state-of the-art technology and the data are presented well and are sound. This being said the manuscript contains significant novel data, but also experiments that are already available in some sort. The histone profile in adult mouse podocytes is novel and provides an interesting map of epigenetic marks in this particular cell type. It is maybe not too surprising that podocyte-differentiation genes have different chromatin accessibility than genes associated with general development. The Wt1-ChIP has been done before by several labs but is certainly an important control in this work. The MafB-ChIP is new. The inducible MafB knockout model including the identification of Tcf21 as a target gene has been published by others in 2020 (and is acknowledged by the authors). The experiments addressing the potential role of MafB in chromatin opening are new. I find that the data are certainly compatible with the model put forward by the authors, but they are not compelling.

Reviewer #2 (Public Review):

Summary:<br /> The authors investigate the role of MafB in regulating podocyte genes. Mafb is required for podocyte differentiation and maintenance. Mutations of this gene cause FSGS in mice and humans. They profiled MafB binding genome-wide in isolated glomeruli and defined overlap with Wt1. They provide evidence that Mafb is required for Wt1 binding and H3K4me3 methylation at the promoters of two essential podocyte genes, Nphs1 and Nphs2. Understanding how the action of different transcription factors is coordinated to control gene expression - the main goal of this paper - is an important line of investigation.

While the main conclusion of the paper is supported by their data, the scope is limited. Additional ChIP-seq experiments and data analysis are needed to solidify and extend their conclusions.

Strengths:<br /> 1) Performing ChIP-seq for histone modifications on isolated podocytes provides valuable cell-type-specific information. Similarly, profiling Mafb and Wt1 in isolated glomeruli provides podocyte-specific binding patterns because these transcription factors (TFs) are not expressed in other cell types in glomeruli. The significant overlap of their Wt1 binding genome-wide with that of prior published work is reassuring. RNA-seq on isolated podocytes provides the appropriate cell-type specific gene expression data to integrate with ChIP-seq data. Together, the RNA-seq and ChIP-seq data are valuable resources for other investigators examining gene regulation in mouse podocytes.

2) The phenotype analysis of their FSGS model is convincing and well done.

3) Testing how Wt1 binding is affected by loss of Mafb provides insight into how these key podocyte TFs may cooperate to regulate genes.

Weaknesses:<br /> 1) The conclusion that Mafb is required for Wt1 binding and H3K4me3 methylation is based solely on ChIP-PCR at two gene promoters (Nphs1, Nphs2). This result should be validated and extended by ChIP-seq. Mafb and Wt1 binding overlap at more than 200 sites. If their model is correct, it is likely that Wt1 binding would be affected at other genomic sites. This result would add strong support to their model of how Wt1 and Mafb cooperate to regulate genes in podocytes. Moreover, ChIP-seq would define whether the dependence of Wt1 on Mafb is also evident at distal regulatory regions (defined H3K4me1, which is typically found at predicted enhancers).

2) The FSGS model generated by the authors involved conditional deletion of Mafb in podocytes at 8 weeks of age. They found that this resulted in reduced expression of Nphs1 and Nphs2 within 48 hours post-deletion. However, they investigated Wt1 binding and H3K4me3 genomic binding in Mafb homozygous null embryos. While this result provides information about podocyte differentiation, it does not address the maintenance of expression of these essential podocyte genes in the adult kidney. Because post-natal deletion of Mafb led to FSGS and reduced expression of Nphs1/2, ChIP-seq should be performed on the adult conditional mutants in order to provide mechanistic information about the disease.

3) H3K4me1 binds enhancer regions. The authors performed ChIP-seq to profile H3K4me1 in isolated podocytes. However, there was no analysis reported of these results. It would be valuable to determine if Wt1 and Mafb co-localize at predicted enhancers in podocytes and if Wt1 binding is lost at these regions in Mafb mutant glomeruli.

Reviewer #1 (Public Review):

Summary:<br /> The manuscript titled "Coevolution due to physical interactions is not a major driving force behind evolutionary rate covariation" by Little et al., explores the potential contribution of physical interaction between correlated evolutionary rates among gene pairs. The authors find that physical interaction is not the main driving of evolutionary rate covariation (ECR). This finding is similar to a previous report by Clark et al. (2012), Genome Research, wherein the authors stated that "direct physical interaction is not required to produce ERC." The previous study used 18 Saccharomycotina yeast species, whereas the present study used 332 Saccharomycotina yeast species and 11 outgroup taxa. As a result, the present study is better positioned to evaluate the interplay between physical interaction and ECR more robustly.

Strengths & Weaknesses:<br /> Various analyses nicely support the authors' claims. Accordingly, I have only one significant comment and several minor comments that focus on wordsmithing - e.g., clarifying the interpretation of statistical results and requesting additional citations to support claims in the introduction.

Reviewer #2 (Public Review):

Summary:<br /> The authors address an important outstanding question: what forces are the primary drivers of evolutionary rate covariation? Exploration of this topic is important because it is currently difficult to interpret the functional/mechanistic implications of evolutionary covariation. These analyses also speak to the predictive power (and limits) of evolutionary rate covariation. This study reinforces the existing paradigm that covariation is driven by a varied/mixed set of interaction types that all fall under the umbrella explanation of 'co-functional interactions'.

Strengths:<br /> Very smart experimental design that leverages individual protein domains for increased resolution.

Weaknesses:<br /> Nuanced and sometimes inconclusive results that are difficult to capture in a short title/abstract statement.

Reviewer #3 (Public Review):

Summary:<br /> The paper makes a convincing argument that physical interactions of proteins do not cause substantial evolutionary co-variation.

Strengths:<br /> The presented analyses are reasonable and look correct and the conclusions make sense.

Weaknesses:<br /> The overall problem of the analysis is that nobody who has followed the literature on evolutionary rate variation over the last 20 years would think that physical interactions are a major cause of evolutionary rate variation. First, there have been probably hundreds of studies showing that gene expression level is the primary driver of evolutionary rate variation (see, for example, [1]). The present study doesn't mention this once. People can argue the causes or the strength of the effect, but entirely ignoring this body of literature is a serious lack of scholarship. Second, interacting proteins will likely be co-expressed, so the obvious null hypothesis would be to ask whether their observed rates are higher or lower than expected given their respective gene expression levels. Third, protein-protein interfaces exert a relatively weak selection pressure so I wouldn't expect them to play much role in the overall evolutionary rate of a protein.

On point 3, the authors seem confused though, as they claim a co-evolving interface would evolve *faster* than the rest of the protein (Figure 1, caption). Instead, the observation is they evolve slower (see, for example, [2]). This makes sense: A binding interface adds additional constraint that reduces the rate at which mutations accumulate. However, the effect is rather weak.

All in all, I'm fine with the analysis the authors perform, and I think the conclusions make sense, but the authors have to put some serious effort into reading the relevant literature and then reassess whether they are actually asking a meaningful question and, if so, whether they're doing the best analysis they could do or whether alternative hypotheses or analyses would make more sense.

[1] https://www.ncbi.nlm.nih.gov/pmc/articles/PMC4523088/<br /> [2] https://www.ncbi.nlm.nih.gov/pmc/articles/PMC4854464/

Reviewer #1 (Public Review):

The study provides a complete comparative interactome analysis of α-arrestin in both humans and drosophila. The authors have presented interactomes of six humans and twelve Drosophila α-arrestins using affinity purification/mass spectrometry (AP/MS). The constructed interactomes helped to find α-arrestins binding partners through common protein motifs. The authors have used bioinformatic tools and experimental data in human cells to identify the roles of TXNIP and ARRDC5: TXNIP-HADC2 interaction and ARRDC5-V-type ATPase interaction. The study reveals the PPI network for α-arrestins and examines the functions of α-arrestins in both humans and Drosophila. The authors have carried out the necessary changes that were suggested.

I would like to congratulate the authors and the corresponding authors of this manuscript for bringing together such an elaborate study on α-arrestin and conducting a comparative study in drosophila and humans.

Reviewer #2 (Public Review):

In this manuscript, the authors present a novel interactome focused on human and fly alpha-arrestin family proteins and demonstrate its application in understanding the functions of these proteins. Initially, the authors employed AP/MS analysis, a popular method for mapping protein-protein interactions (PPIs) by isolating protein complexes. Through rigorous statistical and manual quality control procedures, they established two robust interactomes, consisting of 6 baits and 307 prey proteins for humans, and 12 baits and 467 prey proteins for flies. To gain insights into the gene function, the authors investigated the interactors of alpha-arrestin proteins through various functional analyses, such as gene set enrichment. Furthermore, by comparing the interactors between humans and flies, the authors described both conserved and species-specific functions of the alpha-arrestin proteins. To validate their findings, the authors performed several experimental validations for TXNIP and ARRDC5 using ATAC-seq, siRNA knockdown, and tissue staining assays. The experimental results strongly support the predicted functions of the alpha-arrestin proteins and underscore their importance.

Reviewer #1 (Public Review):

Zhou et al. have slightly expanded and improved their web tool from the previous submission, fixing some small issues and adding in additional sets of data from HMDP mice. Essentially, the authors have created a tool that facilitates the integrated analysis of omics datasets (particularly transcriptomics, but could be easily adapted to include proteomics) across tissues.

The strength is that this is new; as far as I know, any other multi-tissue analysis software is relatively ad hoc and it is not easily supported by e.g. SRA/GEO, but rather you'd need to download the multiple datasets and DIY. The authors have now shown some statistically significant (albeit expected from literature) results created using their pipeline. Whether the method will be generally useful for the community depends on its further development and support, but of course whether a project is supported also depends on whether its first publication is accepted - somewhat of a Catch-22 for a reviewer. Right now, the results shown are a convincing proof-of-concept that would likely be of utility mostly to the hosting laboratory and their direct collaborators, but which, with continued development at a similar level of effort, could be more generally useful for the growing number of groups interested in cross-tissue analysis.

Reviewer #2 (Public Review):

Summary:<br /> Zhou et al. have revised their previous manuscript, which has greatly improved the quality of the work. Zhou et al. use publicly available GTEx data of 18 metabolic tissues from 310 individuals to explore gene expression correlation patterns within-tissue and across-tissues. Furthermore, they have added an analysis of data from a diverse panel of inbred mouse strains, which allows them to also incorporate data on physiological phenotypes relevant to metabolic signaling between tissues. They now focus on validating their approach to exploring signal in gene co-expression rather than emphasizing unvalidated discoveries. They provide a webtool (GD-CAT) to allow users to explore these data. Focusing more on known biology does result in the study making stronger conclusions from its data. The webtool is also improved, expanded with the mouse data, and of value to the scientific community. Their revision has also corrected key misconceptions from the initial submission and provides greater clarification of the methodologies used.

Strengths:<br /> GTEx as well as the hybrid diversity mouse panel are powerful resource for many areas of biomedicine, and this study represents a valid use of gene co-expression network methodology. They have greatly improved its description and contextualization within the gene co-expression studies. The authors previously did a good job of providing examples confirming known signaling biology and have further improved these. They have largely removed the sections on discovery of novel biology, which is potentially for the better given a lack of follow-up validation, which could be beyond the scope of this manuscript anyway. The webtool, GD-CAT, is easy to use and allows researchers with genes and tissues of interest to perform the same analyses in the GTEx and HMDP data.

Weaknesses:<br /> With the previous version, the primary weaknesses for me were key misconceptions and lack of detail in the methods, which have all been greatly improved. The manuscript could be considered more of a "Resource" than "Research", though there is value in showing how the known biology is reflected in the correlation data and could presumably be paired with validation to discover new biology. Finally, there are sentences here and there that could be rephrased to improve clarity, but overall it is greatly improved.

Reviewer #1 (Public Review):

Summary:<br /> The CPC plays multiple essential roles in mitosis such as kinetochore-microtubule attachment regulation, kinetochore assembly, spindle assembly checkpoint activation, anaphase spindle stabilization, cytokinesis, and nuclear envelope formation, as it dynamically changes its mitotic localization: it is enriched at inner centromeres from prophase to metaphase but it is relocalized at the spindle midzone in anaphase. The business end of the CPC is Aurora B and its allosteric activation module IN-box, which is located at the C-terminal part of INCENP. In most well-studied eukaryotic species, Aurora B activity is locally controlled by the localization module of the CPC, Survivin, Borealin, and the N-terminal portion of INCENP. Survivin and Borealin, which bind the N terminus of INCENP, recognize histone residues that are specifically phosphorylated in mitosis, while anaphase spindle midzone localization is supported by the direct microtubule-binding capacity of the SAH (single alpha helix) domain of INCENP and other microtubule-binding proteins that specifically interact with INCENP during anaphase, which are under the regulation of CDK activity. One of these examples includes the kinesin-like protein MKLP2 in vertebrates.

Trypanosoma is an evolutionarily interesting species to study mitosis since its kinetochore and centromere proteins do not show any similarity to other major branches of eukaryotes, while orthologs of Aurora B and INCENP have been identified. Combining molecular genetics, imaging, biochemistry, cross-linking IP-MS (IP-CLMS), and structural modeling, this manuscript reveals that two orphan kinesin-like proteins KIN-A and KIN-B act as localization modules of the CPC in Trypanosoma brucei. The IP-CLMS, AlphaFold2 structural predictions, and domain deletion analysis support the idea that (1) KIN-A and KIN-B form a heterodimer via their coiled-coil domain, (2) Two alpha helices of INCENP interact with the coiled-coil of the KIN-A-KIN-B heterodimer, (3) the conserved KIN-A C-terminal CD1 interacts with the heterodimeric KKT9-KKT11 complex, which is a submodule of the KKT7-KKT8 kinetochore complex unique to Trypanosoma, (4) KIN-A and KIN-B coiled-coil domains and the KKT7-KKT8 complex are required for CPC localization at the centromere, (5) CD1 and CD2 domains of KIN-A support its centromere localization. The authors further show that the ATPase activity of KIN-A is critical for spindle midzone enrichment of the CPC. The imaging data of the KIN-A rigor mutant suggest that dynamic KIN-A-microtubule interaction is required for metaphase alignment of the kinetochores and proliferation. Overall, the study reveals novel pathways of CPC localization regulation via KIN-A and KIN-B by multiple complementary approaches.

Strengths:<br /> The major conclusion is collectively supported by multiple approaches, combining site-specific genome engineering, epistasis analysis of cellular localization, AlphaFold2 structure prediction of protein complexes, IP-CLMS, and biochemical reconstitution (the complex of KKT8, KKT9, KKT11, and KKT12).

Weaknesses:<br /> - The predictions of direct interactions (e.g. INCENP with KIN-A/KIN-B, or KIN-A with KKT9-KKT11) have not yet been confirmed experimentally, e.g. by domain mutagenesis and interaction studies.

- The criteria used to judge a failure of localization are not clearly explained (e.g., Figure 5F, G).

- It remains to be shown that KIN-A has motor activity.

- The authors imply that KIN-A, but not KIN-B, interacts with microtubules based on microtubule pelleting assay (Fig. S6), but the substantial insoluble fractions of 6HIS-KINA and 6HIS-KIN-B make it difficult to conclusively interpret the data. It is possible that these two proteins are not stable unless they form a heterodimer.

- For broader context, some prior findings should be introduced, e.g. on the importance of the microtubule-binding capacity of the INCENP SAH domain and its regulation by mitotic phosphorylation (PMID 8408220, 26175154, 26166576, 28314740, 28314741, 21727193), since KIN-A and KIN-B may substitute for the function of the SAH domain.

Reviewer #2 (Public Review):

How the chromosomal passenger complex (CPC) and its subunit Aurora B kinase regulate kinetochore-microtubule attachment, and how the CPC relocates from kinetochores to the spindle midzone as a cell transitions from metaphase to anaphase are questions of great interest. In this study, Ballmer and Akiyoshi take a deep dive into the CPC in T. brucei, a kinetoplastid parasite with a kinetochore composition that varies greatly from other organisms.

Using a combination of approaches, most importantly in silico protein predictions using alphafold multimer and light microscopy in dividing T. brucei, the authors convincingly present and analyse the composition of the T. brucei CPC. This includes the identification of KIN-A and KIN-B, proteins of the kinesin family, as targeting subunits of the CPC. This is a clear advancement over earlier work, for example by Li and colleagues in 2008. The involvement of KIN-A and KIN-B is of particular interest, as it provides a clue for the (re)localization of the CPC during the cell cycle. The evolutionary perspective makes the paper potentially interesting for a wide audience of cell biologists, a point that the authors bring across properly in the title, the abstract, and their discussion.

The evolutionary twist of the paper would be strengthened 'experimentally' by predictions of the structure of the CPC beyond T. brucei. Depending on how far the authors can extend their in-silico analysis, it would be of interest to discuss a) available/predicted CPC structures in well-studied organisms and b) structural predictions in other euglenozoa. What are the general structural properties of the CPC (e.g. flexible linkers, overall dimensions, structural differences when subunits are missing etc.)? How common is the involvement of kinesin-like proteins? In line with this, it would be good to display the figure currently shown as S1D (or similar) as a main panel.

Reviewer #3 (Public Review):

Summary:<br /> The protein kinase, Aurora B, is a critical regulator of mitosis and cytokinesis in eukaryotes, exhibiting a dynamic localisation. As part of the Chromosomal Passenger Complex (CPC), along with the Aurora B activator, INCENP, and the CPC localisation module comprised of Borealin and Survivin, Aurora B travels from the kinetochores at metaphase to the spindle midzone at anaphase, which ensures its substrates are phosphorylated in a time- and space-dependent manner. In the kinetoplastid parasite, T. brucei, the Aurora B orthologue (AUK1), along with an INCENP orthologue known as CPC1, and a kinetoplastid-specific protein CPC2, also displays a dynamic localisation, moving from the kinetochores at metaphase to the spindle midzone at anaphase, to the anterior end of the newly synthesised flagellum attachment zone (FAZ) at cytokinesis. However, the trypanosome CPC lacks orthologues of Borealin and Survivin, and T. brucei kinetochores also have a unique composition, being comprised of dozens of kinetoplastid-specific proteins (KKTs). Of particular importance for this study are KKT7 and the KKT8 complex (comprising KKT8, KKT9, KKT11, and KKT12). Here, Ballmer and Akiyoshi seek to understand how the CPC assembles and is targeted to its different locations during the cell cycle in T. brucei.

Strengths & Weaknesses:<br /> Using immunoprecipitation and mass-spectrometry approaches, Ballmer and Akiyoshi show that AUK1, CPC1, and CPC2 associate with two orphan kinesins, KIN-A and KIN-B, and with the use of endogenously expressed fluorescent fusion proteins, demonstrate for the first time that KIN-A and KIN-B display a dynamic localisation pattern similar to other components of the CPC. Most of these data provide convincing evidence for KIN-A and KIN-B being bona fide CPC proteins, although the evidence that KIN-A and KIN-B translocate to the anterior end of the new FAZ at cytokinesis is weak - the KIN-A/B signals are very faint and difficult to see, and cell outlines/brightfield images are not presented to allow the reader to determine the cellular location of these faint signals (Fig S1B).

They then demonstrate, by using RNAi to deplete individual components, that the CPC proteins have hierarchical interdependencies for their localisation to the kinetochores at metaphase. These experiments appear to have been well performed, although only images of cell nuclei were shown (Fig 2A), meaning that the reader cannot properly assess whether CPC components have localised elsewhere in the cell, or if their abundance changes in response to depletion of another CPC protein.

Ballmer and Akiyoshi then go on to determine the kinetochore localisation domains of KIN-A and KIN-B. Using ectopically expressed GFP-tagged truncations, they show that coiled-coil domains within KIN-A and KIN-B, as well as a disordered C-terminal tail present only in KIN-A, but not the N-terminal motor domains of KIN-A or KIN-B, are required for kinetochore localisation. These data are strengthened by immunoprecipitating CPC complexes and crosslinking them prior to mass spectrometry analysis (IP-CLMS), a state-of-the-art approach, to determine the contacts between the CPC components. Structural predictions of the CPC structure are also made using AlphaFold2, suggesting that coiled coils form between KIN-A and KIN-B, and that KIN-A/B interact with the N termini of CPC1 and CPC2. Experimental results show that CPC1 and CPC2 are unable to localise to kinetochores if they lack their N-terminal domains consistent with these predictions. Altogether these data provide convincing evidence of the protein domains required for CPC kinetochore localisation and CPC protein interactions. However, the authors also conclude that KIN-B plays a minor role in localising the CPC to kinetochores compared to KIN-A. This conclusion is not particularly compelling as it stems from the observation that ectopically expressed GFP-NLS-KIN-A (full length or coiled-coil domain + tail) is also present at kinetochores during anaphase unlike endogenously expressed YFP-KIN-A. Not only is this localisation probably an artifact of the ectopic expression, but the KIN-B coiled-coil domain localises to kinetochores from S to metaphase and Fig S2G appears to show a portion of the expressed KIN-B coiled-coil domain colocalising with KKT2 at anaphase. It is unclear why KIN-B has been discounted here.

Next, using a mixture of RNAi depletion and LacI-LacO recruitment experiments, the authors show that kinetochore proteins KKT7 and KKT9 are required for AUK1 to localise to kinetochores (other KKT8 complex components were not tested here) and that all components of the KKT8 complex are required for KIN-A kinetochore localisation. Further, both KKT7 and KKT8 were able to recruit AUK1 to an ectopic locus in the S phase, and KKT7 recruited KKT8 complex proteins, which the authors suggest indicates it is upstream of KKT8. However, while these experiments have been performed well, the reciprocal experiment to show that KKT8 complex proteins cannot recruit KKT7, which could have confirmed this hierarchy, does not appear to have been performed. Further, since the LacI fusion proteins used in these experiments were ectopically expressed, they were retained (artificially) at kinetochores into anaphase; KKT8 and KIN-A were both able to recruit AUK1 to LacO foci in anaphase, while KKT7 was not. The authors conclude that this suggests the KKT8 complex is the main kinetochore receptor of the CPC - while very plausible, this conclusion is based on a likely artifact of ectopic expression, and for that reason, should be interpreted with a degree of caution.

Further IP-CLMS experiments, in combination with recombinant protein pull-down assays and structural predictions, suggested that within the KKT8 complex, there are two subcomplexes of KKT8:KKT12 and KKT9:KKT11, and that KKT7 interacts with KKT9:KKT11 to recruit the remainder of the KKT8 complex. The authors also assess the interdependencies between KKT8 complex components for localisation and expression, showing that all four subunits are required for the assembly of a stable KKT8 complex and present AlphaFold2 structural modelling data to support the two subcomplex models. In general, these data are of high quality and convincing with a few exceptions. The recombinant pulldown assay (Fig. 4H) is not particularly convincing as the 3rd eluate gel appears to show a band at the size of KKT11 (despite the labelling indicating no KKT11 was present in the input) but no pulldown of KKT9, which was present in the input according to the figure legend (although this may be mislabeled since not consistent with the text). The text also states that 6HIS-KKT8 was insoluble in the absence of KKT12, but this is not possible to assess from the data presented. It is also surprising that data showing the effects of KKT8, KKT9, and KKT12 depletion on KKT11 localisation and abundance are not presented alongside the reciprocal experiments in Fig S4G-J.

The authors also convincingly show that AlphaFold2 predictions of interactions between KKT9:KKT11 and a conserved domain (CD1) in the C-terminal tail of KIN-A are likely correct, with CD1 and a second conserved domain, CD2, identified through sequence analysis, acting synergistically to promote KIN-A kinetochore localisation at metaphase, but not being required for KIN-A to move to the central spindle at anaphase. They then hypothesise that the kinesin motor domain of KIN-A (but not KIN-B which is predicted to be inactive based on non-conservation of residues key for activity) determines its central spindle localisation at anaphase through binding to microtubules. In support of this hypothesis, the authors show that KIN-A, but not KIN-B can bind microtubules in vitro and in vivo. However, ectopically expressed GFP-NLS fusions of full-length KIN-A or KIN-A motor domain did not localise to the central spindle at anaphase. The authors suggest this is due to the GPF fusion disrupting the ATPase activity of the motor domain, but they provide no evidence that this is the case. Instead, they replace endogenous KIN-A with a predicted ATPase-defective mutant (G209A), showing that while this still localises to kinetochores, the kinetochores were frequently misaligned at metaphase, and that it no longer concentrates at the central spindle (with concomitant mis-localisation of AUK1), causing cells to accumulate at anaphase. From these data, the authors conclude that KIN-A ATPase activity is required for chromosome congression to the metaphase plate and its central spindle localisation at anaphase. While potentially very interesting, these data are incomplete in the absence of any experimental data to show that KIN-A possesses ATPase activity or that this activity is abrogated by the G209A mutation, and the conclusions of this section are rather speculative.

Impact:<br /> Overall, this work uses a wide range of cutting-edge molecular and structural predictive tools to provide a significant amount of new and detailed molecular data that shed light on the composition of the unusual trypanosome CPC and how it is assembled and targeted to different cellular locations during cell division. Given the fundamental nature of this research, it will be of interest to many parasitology researchers as well as cell biologists more generally, especially those working on aspects of mitosis and cell division, and those interested in the evolution of the CPC.

Reviewer #1 (Public Review):

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

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

Weaknesses:<br /> A few weaknesses exist. Clarification of some aspects of the experimental design would improve the manuscript. However, most concerns relate to the interpretation of this study's findings. The authors state that loss of glucose in urine is sensed as a biological threat based on the HPA axis activation seen in this mouse model. This interpretation is understandable but speculative. Importantly, whether stress hormones mediate the increase in endogenous glucose production in this model and in humans with altered glucose transporter function remains to be demonstrated conclusively. For example, the paper found several other circulating and local factors that could be causal. In addition, the approach used in these studies cannot definitively determine whether renal glucose production or only hepatic glucose production was altered. This model is also unable to shed light on how elevated stress hormones might interact with insulin resistance, which is known to increase endogenous glucose production. That issue is of substantial clinical relevance for patients with T2D and metabolic disease. Finally, while findings from the Glut2 knockout mice are of scientific interest, it should be noted that the Glut2 receptor is critical to the function of pancreatic islets and as such is not a good candidate for pharmacological targeting.

Reviewer #2 (Public Review):

Summary:<br /> The authors previously generated renal Glut2 knockout mice, which have high levels of glycosuria but normal fasting glucose. They use this as an opportunity to investigate how compensatory mechanisms are engaged in response to glycosuria. They show that renal and hepatic glucose production, but not metabolism, is elevated in renal Glut2 male mice. They show that renal Glut2 male mice have elevated Crh mRNA in the hypothalamus and elevated plasma levels of ACTH and corticosterone. They also show that temporary denervation of renal nerves leads to a decrease in fasting and fed blood glucose levels in female renal Glut2 mice, but not control mice. Finally, they perform plasma proteomics in male mice to identify plasma proteins with a greater than 25% (up or down) between the knockouts and controls.

Strengths:<br /> The question that is trying to be addressed is clinically important: enhancing glycosuria is a current treatment for diabetes, but is limited in efficacy because of compensatory increases in glucose production.<br /> Also, the mouse line used is an inducible knockout, thus minimizing the impact of compensatory mechanisms engaged in early development.

Weaknesses:<br /> 1) Though the Methods specify that both male and female mice were used, it appears each experiment was performed only on one sex, rather than each experiment being performed on both sexes. For example, renal denervation was performed only on females, whereas all other experiments were performed exclusively on males. This makes it impossible to examine whether there are sex differences in any measures.

2) This study appears to use an inducible Glut2 knockout with tamoxifen, yet nothing describes when the tamoxifen was delivered relative to the experimental manipulations. Was the knockout performed in young animals? In adult animals? This is important both for the ability of readers to repeat the experiment, but also to interpret the results in light of potential compensatory changes (if the knockout was performed at an early age, for example).

3) In Methods, please clarify whether littermate controls were WT, het, or both. If het mice were used as controls, this is potentially problematic.

4) Conclusions like "the HPA axis may contribute to the compensatory increase in glucose production in renal Glut2 knockout mice" (line 215) are premature. All that is shown is that renal Glut2 male mice have elevated HPA activity. There are no experiments establishing causation. For example, the authors could administer a CRF antagonist or a glucocorticoid receptor antagonist in this mouse line, and examine whether this impacts blood glucose. This was not done.

5) If elevated glycosuria drives HPA activity, one would expect to see elevated HPA activity in humans who take SGLT2 inhibitors. Yet, this does not seem to be the case (Higashikawa et al, 2021; see also Perry et al, 2021 for rodent example). This raises the question of whether the glycosuria observed in the mouse line here is relevant to any human conditions. The relevance of the mechanisms proposed here would be much more convincing if a second model of glycosuria was used here (for example, inducing diabetes in mice and treating with SGLT2 inhibitors). Without these types of experiments, any relevance to human conditions is highly speculative and should be reserved for the Discussion. What the authors are studying here is one mechanism for maintaining blood glucose when glycosuria is induced by a genetic knockout.

6) The experiment examining the impact of renal denervation is nice but incomplete. For example, what is the relevance to the hepatic glucose production that was reported? It is interesting that the renal denervation normalized the elevated HPA activity in Glut2 female mice, but it is not clear how this signaling would alter HPA activity.

7) The Methods need to describe the plasma collection procedure for both ELISA and plasma proteomic experiments. What time of day were samples collected? Were samples collected when animals were euthanized from other experiments after experimental manipulations, or in animals without other experimentation?

8) In general, the links between the disparate mechanisms (signals in the plasma, changes in renal activity, changes in HPA activity) are weak. There are more experiments needed to establish a direct kidney-hypothalamus axis. If renal activity elevates blood glucose in the face of glycosuria, why are there no differences in renal activity between control and Glut2 knockout mice? If the blood glucose levels are regulated by renal activity, it must be the sensitivity to the renal activity that differs between control and knockout mice - perhaps this should be investigated. If one stimulates afferent renal nerves, can one drive HPA activation and elevate blood glucose? How are these measures related to the plasma proteins identified? Without these links, this study is descriptive and correlational.

Reviewer #1 (Public Review):

Summary:<br /> In their study, Petersen et al. investigated the relationship between parameters of metabolic syndrome (MetS) and cortical thickness using partial least-squares correlation analysis (PLS) and performed subsequently a group comparison (sensitivity analysis). To do this, they utilized data from two large-scale population-based cohorts: the UK BioBank (UKB) and the Hamburg City Health Study (HCHS). They identified a latent variable that explained 77% of the shared variance, driven by several measures related to MetS, with obesity-related measures having the strongest contribution. Their results highlighted that higher cortical thickness in the orbitofrontal, lateral prefrontal, insular, anterior cingulate, and temporal areas is associated with lower MetS metric severity. Conversely, the opposite pattern was observed in the superior frontal, parietal, and occipital regions. A similar pattern was then observed in the sensitivity analysis when comparing two groups (MetS vs. matched controls) separately. They then mapped local cellular and network topological attributes to the observed cortical changes associated with MetS. This was achieved using cell-type-specific gene expressions from the Allen Human Brain Atlas and the group consensus functional and structural connectomes of the Human Connectome Project (HCP), respectively. This contextualization analysis allowed them to identify potential cellular contributions in these structures driven by endothelial cells, microglial cells, and excitatory neurons. It also indicated functional and structural interconnectedness of areas experiencing similar MetS effects.

Strengths:<br /> The effects of metabolic syndrome on the brain are still incompletely understood, and such multi-scale analyses are important for the field. Despite the study's sole 'correlation-based' nature, it yields valuable results, including several scales of brain parameters (cortical thickness, cellular, and network-based). The results are robust and benefit from two 'large-scale' datasets, resulting in highly powered statistics.

Weaknesses:<br /> However, some concerns arise regarding certain interpretations and claims made by the authors. In particular, it is not entirely convincing that the authors' results are relevant for studying insulin resistance as a clinical measure of MetS. This is due to the use of non-fasting glycemia as a metric, which the authors claim represents insulin resistance. While non-fasting blood glucose is a potential, albeit poor, indicator of insulin resistance, claiming a direct correlation between insulin resistance and cortical thickness does not seem entirely convincing. By doing so, the authors suggest that insulin resistance might have a weak contribution to cortical thickness abnormalities, with a rather low 'loading' of glycemia compared to the other MetS metrics, although this cannot be conclusively determined from these results.

Reviewer #2 (Public Review):

Summary:<br /> In this manuscript, Petersen et al. aimed for a comprehensive assessment of the relationship between cardiometabolic risk factors and cortical thickness. They found that a latent variable reflecting higher obesity, hypertension, LDL cholesterol, triglyerides, glucose, and lower HDL cholesterol was associated with lower cortical thickness in orbitofrontal, lateral prefrontal, insular, anterior cingulate, and temporal areas. In sensitivity analyses, they showed that this pattern replicated across cohorts and was also consistent with a clinical definition of the metabolic syndrome.

Further, when including cognition in the multivariate analysis, the pattern remained unchanged and indicated that cardiometabolic risk factors were associated with worse cognitive performance across different tests. The authors investigated the cell types implicated in the regions associated with cardiometabolic risk using the Allen brain atlas and found that the density of excitatory neurons type 8, endothelial cells, and microglia reliably co-located with the pattern of cortical thickness. Furthermore, they showed that cortical regions more strongly associated with MetS were more closely structurally & functionally connected than others.

Strengths:<br /> This study performed a comprehensive assessment of the combined association of cardiometabolic risk factors and brain structure and investigated micro- and macroscopic underpinnings. A major strength of the study is the methodological approach of Partial Least Squares which allows the authors to not single out risk factors but to take them into account simultaneously. The large sample size from two cohorts allowed for different sensitivity analyses and convincing evidence for the stability of the first latent variable. The authors demonstrated that the component was also reliably related to cognitive performance, replicating multiple previous studies that evidenced associations of different components of the MetS with worse cognitive performance.

The novel contribution of the study lies in the virtual histology and brain topology investigation of the cortical pattern related to MetS. The virtual histology provided clear evidence of the co-localization of endothelial, glial, and excitatory neuronal cells with the regions of MetS-associated cortical thinning while the brain topology analysis highlighted the disproportionate structural and functional connectivity between associated regions. This analysis provides insights into the role of inflammatory processes and the intricate link between gray matter morphology and microvasculature, both locally and in relation to long-range connectivity. This information is valuable to inform future mechanistic studies.

Weaknesses:<br /> The study is exclusively cross-sectional which does not allow to the authors to disentangle causes from consequences. While studies indicate that most of the differences seen in middle age are probably consequences of the MetS on the vasculature, blood-brain barrier, or inflammatory processes, differences in cortical morphology might also represent a risk factor for weight gain.

Another limitation is the omission of subcortical structures and the cerebellum which might have provided additional information on the pattern of GM differences associated with MetS.

The study is exploratory in nature and for the contextualization analyses it is difficult to judge whether those were selected from a larger pool of analyses. The analysis approach taken to relate the cardiometabolic risk, brain structure, and cognition does not allow the reader to determine whether brain regions most strongly related to the MetS are the ones also most strongly associated with cognitive performance. The cortical pattern arising from the models including cognition is not thoroughly compared to the MetS-only pattern and therefore, it is difficult to estimate to which extent the MetS-related cortical patterns explain variance in cognitive performance.

Reviewer #3 (Public Review):

Summary:<br /> This study investigates the continuous effect of MetS components - namely, obesity, arterial hypertension, dyslipidemia, and insulin resistance - on cortical thickness. It also examines the spatial correlations between MetS effects on cortical thickness with brain cellular and network topological attributes. Additionally, the authors attempt to explore the complex interplay among MetS, cognitive function, and cortical thickness.

The results reveal a latent relationship between MetS and cortical thickness based on a clinical-anatomical dimension. Furthermore, the effect of MetS on cortical thickness is linked to local cell types and network topological attributes. These findings suggest that the authors achieved most, though not all, of their research objectives.

The conclusions are mostly well supported by data and results. However, the use of "was governed by" in the conclusion section suggests a causal relationship. This phrasing is inappropriate given that the study primarily employs correlational analyses.

Strengths<br /> The study presents several strengths:

This study undertakes a comprehensive assessment encompassing the full range of MetS components, such as obesity or arterial hypertension, rather than adopting a case-control study approach (categorizing participants into MetS or non-MetS groups) as seen in some previous research. Utilizing Partial Least Squares (PLS) for correlational analysis effectively addresses issues of multicollinearity (or high covariance among MetS components) and explores the relationship between MetS and brain morphology.

The study leverages two datasets, examining a large sample size of 40,087 individuals. This substantial sample potentially aids in identifying nuanced and underexplored brain anomalies. By incorporating high-quality MRI images, standardized data, and statistical analysis procedures, as well as sensitivity analyses, the results gain robustness, which addresses the limitations of small samples and low reproducibility.

In the context of MetS, this research uniquely employs the concept of imaging transcriptomics, i.e. virtual histology analysis. This approach allows the study to explore intricate relationships between cellular types and cortical thickness anomalies.

Weaknesses<br /> While this work has foundational strengths, the analyses and data seem inadequate to fully support the key claim and analysis. In particular:

After a thorough review of the methods and results sections, I found no direct or strong evidence supporting the authors' claim that the identified latent variables were related to more severe MetS to worse cognitive performance. While a sub-group comparison was conducted, it did not adequately account for confounding factors such as educational level. Additionally, the strength of evidence from such a sub-group comparison is substantially weaker than that from randomized controlled trials or longitudinal cohort studies. Therefore, it is inaccurate for the authors to assert a direct relationship between MetS and cognitive function based on the presented data. A more appropriate research design or data analysis approach, such as mediation analysis, can be employed to address this issue.

The use of the imaging transcriptomics pipeline (virtual histology analysis) to explore the microscale associations with MetS effects on the brain is commendable and has shown promising results. Nevertheless, variations in gene sets may introduce a degree of heterogeneity in the results (Seidlitz, et al., 2020; Martins et al., 2021). Consequently, further validation or exploratory analyses utilizing different gene sets can yield more compelling results and conclusions.

Reviewer #1 (Public Review):

Smirnova et al. present a cryo-EM structure of a nucleosome-SIRT6 complex to understand how the histone deacetylase SIRT6 deacetylates the N-terminal tail of histone H3. The authors obtained the structure at sub-4 Å resolution and can visualize how interactions between the nucleosome and SIRT6 position SIRT6 to allow for H3 tail deacetylation. Through additional conformational analysis of their cryo-EM data, they reveal that SIRT6 positioning is flexible on the nucleosome surface, and this could accommodate the targeting of certain H3 tail residues. This work is significant as it represents the visualization of a histone deacetylase on its native nucleosomal target and reveals how substrate specificity is achieved. Importantly, it should be noted that recently two additional structures of the nucleosome-SIRT6 complex were already published. Therefore, Smirnova et al. confirm and complement these previous findings. Additionally, Smirnova et al. expand our understanding of the structural flexibility of SIRT6 on the nucleosome and clarify that SIRT6 also shows histone deacetylase activity on H3K27Ac.

Reviewer #2 (Public Review):

Smirnova et al. present a cryo-EM structure of human SIRT6 bound to a nucleosome as well as the results from molecular dynamics simulations. The results show that the combined conformational flexibilities of SIRT6 and the N-terminal tail of histone H3 limit the residues with access to the active site, partially explaining the substrate specificity of this sirtuin-class histone deacetylase. Two other groups have recently published cryo-EM structures of SIRT6:nucleosome complexes; this manuscript confirms and complements these previous findings, with the addition of some novel insights into the role of structural flexibility in substrate selection.

Reviewer #3 (Public Review):

Summary: The present study sought to investigate the role ERα expressed in Gabaergic neurons of the rostral periventricular aspect of the third ventricle (RP3V) and medial preoptic nucleus (MPN) in the positive feedback using genetically driven Crispr-Cas9 mediated knockdown of ESR1 in VGAT expressing neurons. ESR1 Knockdown in preoptic gabaergic neurons led to an absence of LH surge and acyclicity when associated with severely reduced kisspeptin (Kp) expression suggesting that a subpopulation of neurons co-expressing Kp and VGAT are key for LH surge since total absence of Kp is associated with an absence of GnRH neuron activation and reduced LH surge. Although the implication of kisspeptin neurons was highly suspected already, the novelty of these results lies in the fact that estrogen signaling is necessary in only a selected fraction of them to maintain both regular cycles and LH surge capacity.

Strengths:<br /> Remarkable aspects of this study are, its dataset which allowed them to segregate animals based on distinct neuronal phenotype matching specific physiological outcomes, the transparency in reporting the results (e.g. all statistical values being reported, all grouping variables being clearly defined, clarity about animals that were excluded and why) and the clarity of the writing. Another remarkable feature of this work lies in the analysis of the dataset. As opposed to the cre-lox approach which theoretically allows for the complete ablation of specific neuronal populations, but may lack specificity regarding timing of action and location, genetically driven in vivo Crispr-Cas9 editing offers both temporal and neuroanatomic selectivity but cannot achieve a complete knock down. This approach based on stereotaxic delivery of the AAV encoded guide RNAs comes with inevitable variability in the location where gene knockdown is achieved. By adjusting their original grouping of the animals based on the evaluation of the extent of kisspeptin expression in the target region, the authors obtained a much clearer and interpretable picture. Although only few animals (n=4) displayed absent kisspeptin expression, the convergence of observations suggesting a central impairment of the reproductive axis is convincing. Finally, the observation that the pulsatile secretion of LH is maintained in the absence of Kp expression in the RP3V lends support to the notion that LH surge and pulsatility are regulated independently by distinct neuronal populations, a model put forward by corresponding author a few years ago.

Reviewer #1 (Public Review):

Summary: The current study examines the necessity of estrogen receptor alpha (ESR1) in GABA neurons located in the anteroventral and preoptic periventricular nuclei and the medial preoptic nucleus of hypothalamus. This brain area is implicated in regulating the pre-ovulatory LH surge in females, but the identity of the estrogen-sensitive neurons that are required remains unknown. The data indicate that approximately 70% knockdown of ESR1 in GABA neurons resulted in variable reproductive phenotypes. However, when the ESR1 knockdown also results in a decrease in kisspeptin expression by these cells, the females had disrupted LH surges, but no alterations in pulsatile LH release. These data support the hypothesis that kisspeptin cells in this region are critical for the pre-ovulatory LH surge in females.

Strengths: The current study examined the efficacy of two guide RNAs to knockdown ESR1 in GABA neurons, resulting in an approximate 70% reduction in ESR1 in GABA neurons. The efficacy of this knockdown was confirmed in the brain via immunohistochemistry and the reproductive outcomes were analyzed several ways to account for differences in guide RNAs or the precise brain region with the ESR1 knockdown. The analysis was taken one step further by grouping mice based on kisspeptin expression following ESR1 knockdown and examining the reproductive phenotypes. Overall, the aims of the study were achieved, the methods were appropriate, and the data were analyzed extensively. This data supports the hypothesis that kisspeptin neurons in the anterior hypothalamus are critical for the preovulatory LH surge.

Weaknesses: One minor weakness in this study is the conclusion that the two different guide RNAs didn't seem to have unique effects on GnRH cFos expression or the reproductive phenotypes. Though the data indicate a 60-70% knockdown for both gRNA2 and gRNA3, 3 of the 4 gRNA2 mice had no cFos expression in GnRH neurons during the time of the LH surge, whereas all mice receiving gRNA3 had at least some cFos/GnRH co-expression. In addition, when mice were re-categorized based on reduction (>75%) in kisspeptin expression, most of the mice in the unilateral or bilateral groups received gRNA2, whereas many of the mice that received gRNA3 were in the "normal" group with no disruption in kisspeptin expression. Whether these results occurred by chance or due to differences in the gRNAs remains unknown. Thus, additional experiments with increased sample sizes would be needed, even if the efficacy of the ESR1 knockdown was comparable, before concluding these 2 gRNAs don't have unique actions.

Reviewer #2 (Public Review):

Clarkson et al investigated the impact of in vivo ESR1 gene disruption selectively in preoptic area GABA neurons on the estrogen regulation of LH secretion. The hypothalamic pathways by which estradiol controls the secretion of gonadotrophins are incompletely understood and relevant to a better understanding of the mechanisms driving fertility and reproduction. Using CRISPR-Cas9 methodology, the authors were able to effectively reduce the expression of estrogen receptor (ER)-alpha in GABA neurons located in the preoptic area of adult female mice. The results obtained were rather variable except in the animals with concomitant suppression of kisspeptin in the rostral periventricular region of the third ventricle (RP3V), which displayed interruption of ovarian cyclicity and an altered estradiol-induced LH surge. The experimental approach used allowed for a cell-selective, temporally-controlled suppression of ER-alpha expression, providing further evidence of the critical role of RP3V kisspeptin neurons in the estrogen positive-feedback effect. The preovulatory LH surge is a variable phenomenon and is better evaluated using serial blood sampling. Although the assessment of the estradiol-induced LH surge was performed in one terminal blood collection, c-Fos expression in GnRH neurons was used as a reliable proxy of the LH surge occurrence. The present findings also suggest that GABA neurotransmission in the preoptic area itself is not involved in the positive-feedback effect of estradiol on LH secretion.

Reviewer #1 (Public Review):

Summary:<br /> This manuscript explores the impact of serotonin on olfactory coding in the antennal lobe of locusts and odor-evoked behavior. The authors use serotonin injections paired with an odor-evoked palp-opening response assay and bath application of serotonin with intracellular recordings of odor-evoked responses from projection neurons (PNs).

Strengths:<br /> The authors make several interesting observations, including that serotonin enhances behavioral responses to appetitive odors in starved and fed animals, induces spontaneous bursting in PNs, and uniformly enhances PN responses to odors. Overall, I had no technical concerns.

Weaknesses:<br /> While there are several interesting observations, the conclusions that serotonin enhanced sensitivity specifically and that serotonin had feeding-state-specific effects, were not supported by the evidence provided. Furthermore, there were other instances in which much more clarification was needed for me to follow the assumptions being made and inadequate statistical testing was reported.

Major concerns.<br /> -To enhance olfactory sensitivity, the expected results would be that serotonin causes locusts to perceive each odor as being at a relatively higher concentration. The authors recapitulate a classic olfactory behavioral phenomenon where higher odor concentrations evoke weaker responses which is indicative of the odors becoming aversive. If serotonin enhanced the sensitivity to odors, then the dose-response curve should have shifted to the left, resulting in a more pronounced aversion to high odor concentrations. However, the authors show an increase in response magnitude across all odor concentrations. I don't think the authors can claim that serotonin enhances the behavioral sensitivity to odors because the locusts no longer show concentration-dependent aversion. Instead, I think the authors can claim that serotonin induces increased olfactory arousal.

-The authors report that 5-HT causes PNs to change from tonic to bursting and conclude that this stems from a change in excitability. However, excitability tests (such as I/V plots) were not included, so it's difficult to disambiguate excitability changes from changes in synaptic input from other network components.

-There is another explanation for the theoretical discrepancy between physiology and behavior, which is that odor coding is further processing in higher brain regions (ie. Other than the antennal lobe) not studied in the physiological component of this study. This should at least be discussed.

-The authors cannot claim that serotonin underlies a hunger state-dependent modulation, only that serotonin impacts responses to appetitive odors. Serotonin enhanced PORs for starved and fed locusts, so the conclusion would be that serotonin enhances responses regardless of the hunger state. If the authors had antagonized 5-HT receptors and shown that feeding no longer impacts POR, then they could make the claim that serotonin underlies this effect. As it stands, these appear to be two independent phenomena.

Reviewer #2 (Public Review):

Summary:<br /> The authors investigate the influence of serotonin on feeding behavior and electrophysiological responses in the antennal lobe of locusts. They find that serotonin injection changes behavior in an odor-specific way. In physiology experiments, they can show that antennal lobe neurons generally increase their baseline firing and odor responses upon serotonin injection. Using a modeling approach the authors propose a framework on how a general increase in antennal lobe output can lead to odor-specific changes in behavior. The authors finally suggest that serotonin injection can mimic a change in a hunger state.

Strengths:<br /> This study shows that serotonin affects feeding behavior and odor processing in the antennal lobe of locusts, as serotonin injection increases activity levels of antennal lobe neurons. This study provides another piece of evidence that serotonin is a general neuromodulator within the early olfactory processing system across insects and even phyla.

Weaknesses:<br /> I have several concerns regarding missing control experiments, unclear data analysis, and interpretation of results.

A detailed description of the behavioral experiments is lacking. Did the authors also provide a mineral oil control and did they analyze the baseline POR response? Is there an increase in baseline response after serotonin exposure already at the behavioral output level? It is generally unclear how naturalistic the chosen odor concentrations are. This is especially important as behavioral responses to different concentrations of odors are differently modulated after serotonin injection (Figure 2: Linalool and Ammonium).

Regarding recordings of potential PNs - the authors do not provide evidence that they did record from projection neurons and not other types of antennal lobe neurons. Thus, these claims should be phrased more carefully.

The presented model suggests labeled lines in the antennal lobe output of locusts. Could the presented model also explain a shift in behavior from aversion to attraction - such as seen in locusts when they switch from a solitarious to a gregarious state? The authors might want to discuss other possible scenarios, such as that odor evaluation and decision-making take place in higher brain regions, or that other neuromodulators might affect behavioral output. Serotonin injections could affect behavior via modulation of other cell types than antennal lobe neurons. This should also be discussed - the same is true for potential PNs - serotonin might not directly affect this cell type, but might rather shut down local inhibitory neurons.

Finally, the authors claim that serotonin injection can mimic the starved state behavioral response. However, this is only shown for one of the four odors that are tested for behavior (HEX), thus the data does not support this claim.

Reviewer #1 (Public Review):

Summary:<br /> Animals in natural environments need to identify predator-associated cues and respond with the appropriate behavioral response to survive. In rodents, some chemical cues produced by predators (e.g., cat saliva) are detected by chemosensory neurons in the vomeronasal organ (VNO). The VNO transmits predator-associated information to the accessory olfactory bulb, which in turn projects to the medial amygdala and the bed nucleus of the stria terminalis, two regions implicated in the initiation of antipredator defensive behaviors. A downstream area to these two regions is the ventromedial hypothalamus (VMH), which has been shown to control both active (i.e., flight) and passive (i.e, freezing) antipredator defensive responses via distinct efferent projections to the anterior hypothalamic nucleus or the periaqueductal gray, respectively. However, whether differences in predator-associated sensory information initially processed in the VNO and further conveyed to the VMH can trigger different types of behavioral responses remained unexplored. To address this question, here the authors investigated the behavioral responses of mice exposed to either fresh or old cat saliva, and further compared the underlying neural circuits that are activated by cat saliva with different freshness.

The scientific question of the study is valid, the experiments were well-performed, and the statistical analyses are appropriate. However, there are some concerns that may directly affect the main interpretation of the results.

Major Concerns:<br /> 1. An important point that the authors should clarify in this study is whether mice are detecting qualitative or quantitative differences between fresh and old cat saliva. Do the environmental conditions in which the old saliva was maintained cause degradation of Fel d 4, the main protein known for inducing a defensive response in rodents? (see Papes et al, 2010 again). If that is the case, one would expect that a lower concentration of Fel d 4 in the old saliva after protein degradation would result in reduced antipredator responses. Alternatively, if the authors believe that different proteins that are absent in the old saliva are contributing to the increased defensive responses observed with the fresh saliva, further protein quantification experiments should be performed. An important experiment to differentiate qualitative versus quantitative differences between the two types of saliva would be diluting the fresh saliva to verify if the amount of protein, rather than the type of protein, is the main factor regulating the behavioral differences.

2. The authors claim that fresh saliva is recognized as an immediate danger by rodents, whereas old saliva is recognized as a trace of danger. However, the study lacks empirical tests to support this interpretation. With the current experimental tests, the behavioral differences between animals exposed to fresh vs. old saliva could be uniquely due to the reduced amount of the exact same protein (e.g., Fel d 4) in the two samples of saliva.

3. In Figure 4H, the authors state that there were no significant differences in the number of cFos-positive cells between the two saliva-exposed groups. However, this result disagrees with the next result section showing that fresh and old saliva differentially activate the VMH. It is unclear why cFos quantification and behavioral correlations were not performed in other upstream areas that connect the VNO to the VMH (e.g., BNST, MeA, and PMCo). That would provide a better understanding of how brain activity correlates with the different types of behaviors reported with the fresh vs. old saliva.

4. The interpretation that fresh and old saliva activates different subpopulations of neurons in the VMH based on the observation that cFos positively correlates with freezing responses only with the fresh saliva lacks empirical evidence. To address this question, the authors should use two neuronal activity markers to track the response of the same population of VHM cells within the same animals during exposure to fresh vs. old saliva. Alternatively, they could use single-cell electrophysiology or imaging tools to demonstrate that cat saliva of distinct freshness activates different subpopulations of cells in the VMH. Any interpretation without a direct within-subject comparison or the use of cell-type markers would become merely speculative. Furthermore, the authors assume that differential activations of mitral cells between fresh and old saliva result in the differential activation of VMH subpopulations (page 13, line 3). However, there are intermediate structures between the mitral cells and the VMH, which are completely ignored in this study (e.g., BNST, medial amygdala).

5. The authors incorrectly cited the Papes et al., 2010 article on several occasions across the manuscript. In the introduction, the authors cited the Papes et al 2010 study to make reference to the response of rodents to chemical cues, but the Papes et al. study did not use any of the chemical cues listed by the authors (e.g., fox feces, snake skin, cat fur, and cat collars). Instead, the Papes et al. 2010 article used the same chemical cue as the present study: cat saliva. The Papes et al. 2010 article was miscited again in the results section where the authors cited the study to make reference to other sources of cat odor that differ from the cat saliva such as cat fur and cat collars. Because the Papes et al. 2010 article has previously shown the involvement of Trpc2 receptors in the VNO for the detection of cat saliva and the subsequent expression of defensive behaviors by using Trpc2-KO mice, the authors should properly cite this study in the introduction and across the manuscript when making reference to their findings.

6. In the introduction, the authors hypothesized that the VNO detects predator cues and sends sensory signals to the VMH to trigger defensive behavioral decisions and stated that direct evidence to support this hypothesis is still missing. However, the evidence that cat saliva activates the VMH and that activity in the VMH is necessary for the expression of antipredator defensive response in rodents has been previously demonstrated in a study by Engelke et al., 2021 (PMID: 33947849), which was entirely omitted by the authors.

7. In the discussion, the authors stated that their findings suggest that the induction of robust freezing behavior is mediated by a distinct subpopulation of VMH neurons. The authors should cite the study by Kennedy et al., 2020 (PMID: 32939094) that shows the involvement of VMH in the regulation of persistent internal states of fear, which may provide an alternative explanation for why distinct concentrations of saliva could result in different behavioral outcomes.

8. The anatomical connectivity between the olfactory system and the ventromedial hypothalamus (VMH) in the abstract is unclear. The authors should clarify that the VMH does not receive direct inputs from the vomeronasal organ (VNO) nor the accessory olfactory bulb (AOB) as it seems in the current text.

Reviewer #2 (Public Review):

In this study, Nguyen et al. showed that cat saliva can robustly induce freezing behavior in mice. This effect is mediated through the accessory olfactory system as it requires physical contact and is abolished in Trp2 KO mice. The authors further showed that V2R-A4 cluster is responsive to cat saliva. Lastly, they demonstrated c-Fos induction in AOB and VMHdm/c by the cat saliva. The c-Fos level in the VMHdm/c is correlated with the freezing response.

Strength:<br /> The study opens an interesting direction. It reveals the potential neural circuit for detecting cat saliva and driving defense behavior in mice. The behavior results and the critical role of the accessory olfactory system in detecting cat saliva are clear and convincing.

Weakness:<br /> The findings are relatively preliminary. The identities of the receptor and the ligand in the cat saliva that induces the behavior remain unclear. The identity of VMH cells that are activated by the cat saliva remains unclear. There is a lack of targeted functional manipulation to demonstrate the role of V2R-A4 or VMH cells in the behavioral response to cat saliva.

Reviewer #3 (Public Review):

Summary:<br /> Nguyen et al show data indicating that the vomeronasal organ (VNO) and ventromedial hypothalamus (VMH) are part of a circuit that elicits defensive responses induced by predator odors. They also show that using fresh or old predator saliva may be a method to change the perceived imminence of predation. The authors also identify a family of VNO receptors that are activated by cat saliva. Next, the authors show how different components of this defensive circuit are activated by saliva, as measured by fos expression. Though interesting, the findings are not all integrated into a single narrative, and some of the results are only replications of earlier findings using modern methods. Overall, these findings provide incremental advance.

Strengths:<br /> 1 Predator saliva is a stimulus of high ethological relevance<br /> 2 The authors performed a careful quantification of fos induction across the anterior-posterior axis in Figure 6.

Weaknesses:<br /> 1 It is unclear if fresh and old saliva indeed alter the perceived imminence predation, as claimed by the authors. Prior work indicates that lower imminence induces anxiety-related actions, such as re-organization of meal patterns and avoidance of open spaces, while slightly higher imminence produces freezing. Here, the authors show that fresh and old predator saliva only provoke different amounts of freezing, rather than changing the topography of defensive behaviors, as explained above. Another prediction of predatory imminence theory would be that lower imminence induced by old saliva should produce stronger cortical activation, while fresh saliva would activate the amygdala, if these stimuli indeed correspond to significantly different levels of predation imminence.

2 It is known that predator odors activate and require AOB, VNO, and VMH, thus replications of these findings are not novel, decreasing the impact of this work.

3 There is a lack of standard circuit dissection methods, such as characterizing the behavioral effects of increasing and decreasing the neural activity of relevant cell bodies and axonal projections, significantly decreasing the mechanistic insights generated by this work.

4 The correlation shown in Figure 5c may be spurious. It appears that the correlation is primarily driven by a single point (the green square point near the bottom left corner). All correlations should be calculated using Spearman correlation, which is non-parametric and less likely to show a large correlation due to a small number of outliers. Regardless of the correlation method used, there are too few points in Figure 5c to establish a reliable correlation. Please add more points to 5c.

5 Some of the findings are disconnected from the story. For example, the authors show that V2R-A4-expressing cells are activated by predator odors. Are these cells more likely to be connected to the rest of the predatory defense circuit than other VNO cells?

6 Were there other behavioral differences induced by fresh compared to old saliva? Do they provoke differences in stretch-attend risk evaluation postures, number of approaches, the average distance to odor stimulus, the velocity of movements towards and away from the odor stimulus, etc?

Reviewer #3 (Public Review):

The main problem with the work is that the results are only descriptive and do not allow any inferences or conclusions about the importance of the function of G4 structures. The discussion and conclusions are poor. The results are preliminary and in order to try to make the analysis more interesting, it should be further extended and the data must be explored in a much greater depth.

Reviewer #1 (Public Review):

Summary:

This study explores the relationship between guanine-quadruplex (G4) structures and pathogenicity islands (PAIs) in 89 pathogenic strains. G4 structures were found to be non-randomly distributed within PAIs and conserved within the same strains. Positive correlations were observed between G4s and GC content across various genomic features, suggesting a link between G4 structures and GC-rich regions. Differences in GC content between PAIs and the core genome underscored the unique nature of PAIs. High-confidence G4 structures in Escherichia coli's regulatory regions were identified, influencing DNA integration within PAIs. These findings shed light on the molecular mechanisms of G4-PAI interactions, enhancing our understanding of bacterial pathogenicity and G4 structures in infectious diseases.

Strengths:

The findings of this study hold significant implications for our understanding of bacterial pathogenicity and the role of guanine-quadruplex (G4) structures.

Molecular Mechanisms of Pathogenicity: The study highlights that G4 structures are not randomly distributed within pathogenicity islands (PAIs), suggesting a potential role in regulating pathogenicity. This insight into the uneven distribution of G4s within PAIs provides a basis for further research into the molecular mechanisms underlying bacterial pathogenicity.

Conservation of G4 Structures: The consistent conservation of G4 structures within the same pathogenic strains suggests that these structures might play a vital and possibly conserved role in the pathogenicity of these bacteria. This finding opens doors for exploring how G4s influence virulence across different pathogens.

Unique Nature of PAIs: The differences in GC content between PAIs and the core genome underscore the unique nature of PAIs. This distinction suggests that factors such as DNA topology and G4 structures might contribute to the specialized functions and characteristics of PAIs, which are often associated with virulence genes.

Regulatory Role of G4s: The identification of high-confidence G4 structures within regulatory regions of Escherichia coli implies that these structures could influence the efficiency or specificity of DNA integration events within PAIs. This finding provides a potential mechanism by which G4s can impact the pathogenicity of bacteria.

Weaknesses:

No weaknesses were identified by this reviewer.

Overall, the study provides fundamental insights into the pathogenicity island and conservation of G4 motifs.

Reviewer #2 (Public Review):

Summary:

In the manuscript entitled "The Intricate Relationship of G-Quadruplexes and Pathogenicity Islands: A Window into Bacterial Pathogenicity" Bo Lyu explored the interactions between guanine-quadruplex (G4) structures and pathogenicity islands (PAIs) in 89 bacterial genomes through a rigorous computational approach. This paper handles an intriguing and complex topic in the field of pathogenomics. It has the potential to contribute significantly to the understanding of G4-PAI interactions and bacterial pathogenicity.

Strengths:

- The chosen research area.<br /> - The summarizing of the results through neat illustrations.

Weaknesses:

This reviewer did not find any significant weaknesses.

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.

Weaknesses:

While these data compellingly establish IBTK as a binding partner and modifier of eIF4A1, a remaining weakness is the lack of direct measurements showing IBTK regulates eIF4A1 helicase activity and translation of target mRNAs. While the effects of IBTK knockout/overexpression on bulk protein synthesis are shown, the expression of multiple 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 #1 (Public Review):

In this study, the authors examined the role of IBTK, a substrate-binding adaptor of the CRL3 ubiquitin ligase complex, in modulating the activity of the eiF4F translation initiation complex. They find that IBTK mediates the non-degradative ubiquitination of eiF4A1, promotes cap-dependent translational initiation, nascent protein synthesis, oncogene expression, and tumor cell growth. Correspondingly, phosphorylation of  IBTK by mTORC1/ S6K1 increases eIF4A1 ubiquitination and sustains oncogenic translation.

Strengths:

This study utilizes multiple biochemical, proteomic, functional, and cell biology assays to substantiate their results.  Importantly, the work nominates IBTK as a unique substrate of mTORC1, and further validates eiF4A1 ( a crucial subunit of the ei44F complex) as a promising therapeutic target in cancer. Since IBTK interacts broadly with multiple members of the translational initial complex - it will be interesting to examine its role in eiF2alpha-mediated ER stress as well as eiF3-mediated translation. Additionally, since IBTK exerts pro-survival effects in multiple cell types, it will be of relevance to characterize the role of IBTK in mediating increased mTORC1 mediated translation in other tumor types, thus potentially impacting their treatment with eiF4F inhibitors.

Limitations/Weaknesses:

The findings are mostly well supported by data, but some areas need clarification and could potentially be enhanced with further experiments:

1) Since eiF4A1 appears to function downstream of IBTK1, can the effects of IBTK1 KO/KD in reducing puromycin incorporation (in Fig 3A),  cap-dependent luciferase reporter activity (Fig 3G), reduced oncogene expression ( Fig 4A) or 2D growth/ invasion assays (Fig 4) be overcome or bypassed by overexpressing eiF4A1? These could potentially be tested in future studies. 

2) The decrease in nascent protein synthesis in puromycin incorporation assays in Figure 3A suggest that the effects of IBTK KO are comparable to and additive with silvesterol. It would be of interest to examine whether silvesterol decreases nascent protein synthesis or increases stress granules in the IBTK KO cells stably expressing IBTK as well. 

3) The data presented in Figure 5 regarding the role of mTORC1 in IBTK-mediated eiF4A1 ubiquitination needs further clarification on several points:

- It is not clear if the experiments in Figure 5F with Phos-tag gels are using the FLAG-IBTK deletion mutant or the peptide containing the mTOR sites as it is mentioned on line 517, page 19 "To do so, we generated an IBTK deletion mutant (900-1150 aa) spanning the potential mTORC1-regulated phosphorylation sites" This needs further clarification.

-It may be of benefit to repeat the Phos tag experiments with full-length FLAG-IBTK and/or endogenous IBTK with molecular weight markers indicating the size of migrated bands.

-Additionally, torin or Lambda phosphatase treatment may be used to confirm the specificity of the band in separate experiments.

-Phos-tag gels with the IBTK CRISPR KO line would also help confirm that the non-phosphorylated band is indeed IBTK. 

-It is unclear why the lower, phosphorylated bands seem to be increasing (rather than decreasing) with AA starvation/ Rapa in Fig 5H.

Reviewer #1 (Public Review):

Summary:<br /> In this study, the authors investigated the mechanisms to repair DSBs induced in euchromatic (Eu) or heterochromatic (Het) contexts in Drosophila. They used a previously described reporter construct that can be used to differentiate between HR, SSA, and mutagenic end joining in response to an I-SceI-induced DSB. Different sub-pathways of end joining (NHEJ, MMEJ, and SD-MMEJ) could be further distinguished by DNA sequence analysis. The main findings of the study are: (1) HR repair is more frequent in Het than in the Eu context; (2) mutagenic EJ repair is more frequent than HR in both contexts; (3) sub-pathways of mutagenic EJ are variable even within the same chromatin domain; and (4) SD-MMEJ repair is associated with larger deletions in the Eu than within the Het compartment.

Strengths:<br /> Overall, the study is well designed and the use of the Bam promoter to drive I-SceI removes some of the variability observed in previous studies. Importantly, the observation of different repair outcomes using the same reporter integrated at different genomic sites suggests that repair is influenced by chromatin state in addition to local DNA sequence context.

Weaknesses:<br /> The main concern I have is the use of only one Eu site versus four for the Het insertions. Given the variability observed between the Het insertions, analysis of a second Eu insertion would give more confidence that the differences observed are significant. One puzzling finding is that HR is increased when the reporter is inserted within the Het domain relative to the Eu domain, suggesting more end resection, yet deletions are smaller for the Het insertions. Bright Ddc2/ATRIP focus formation at DSBs induced in the Het domain is consistent with extensive end resection in this compartment. The authors speculate that this finding could indicate differences in the density of RPA loading or recruitment of Pol theta near ends. I recognize that measuring RPA density on single-stranded DNA would be extremely challenging, but is it known if Pol theta is recruited to DSBs within the Het domain before they move to the periphery?

Reviewer #2 (Public Review):

Summary:<br /> The authors seek to vary the integration site of a double-strand break repair reporter and assess how the chromatin state of different reporter integration sites impacts the contribution of various DSB repair pathways.

Strengths:<br /> It addresses repair in vivo. The reporter improves assay reliability (relative to previous fly DSB repair substrates) by inducing I-SceI within a more narrow and well-defined expression window. The authors' characterization of the spectrum of a-EJ products by sequencing is largely rigorous and thorough, and this often difficult to communicate data is presented in a clear and easily digested manner.

Weaknesses:<br /> The use of the single euchromatic site undercuts their ability to generalize the impact of chromatin state. This concern is minor when considering repair by HR, as repair efficiency appears to vary little when comparing repair across the 4 different heterochromatic sites. Still, it is possible the single euchromatic site they used is an outlier in its sparing use of HR. The assessment of repair by alt-EJ is more problematic, though, since the character of repair appears to vary as much across the different heterochromatic sites as it does comparing a given heterochromatic site vs. the euchromatic site. For example, focusing on their central argument (decreased deletion during SD-MMEJ at heterochromatic sites), the difference between Het2 and all other sites appears to be more dramatic than the difference between Het1 and the single euchromatic site (Figure 5A, Supp Fig 2).

Reviewer #3 (Public Review):

Summary:<br /> In this manuscript, Chiolo and colleagues adapt a Drosophila induced-DSB repair outcome assay to the spermatogonia. In order to compare the outcomes in H3K9me-rich centromeric heterochromatin with a euchromatic site they use a cross to a silencing mutant to reveal the sequence changes in the reporter, which otherwise are not expressed. The authors corroborate that homologous recombination (HR) is up-regulated in this chromatin context, consistent with prior studies. Applying sequencing to mutagenic products the authors reveal context-dependent preferences in mutagenic end joining pathways and mechanisms, although these seem less categorical in terms of hetero- and euchromatin and instead sensitive to more subtle aspects of the local chromatin landscape. One theme, however, is that the microhomologies used for synthesis-dependent end joining are nearer to the induced DSB in heterochromatin than seen for the euchromatic DSB.

Strengths:<br /> 1. The use of the mitotically active spermatogonia and transient expression of the I-SceI to induce the DSB mitigates some caveats of prior experimental approaches including the fact that the cells are universally mitotically active. This approach also enables the outcomes to be assayed in the next generation, which is necessary for reporters expressed within heterochromatin. Thus, this is a technological tool that will be useful to other groups.

2. The observations suggest that MMEJ within heterochromatin (inferred to be Pol theta-dependent) prefers to use microhomologies close to the DSB. This suggests that either DSB end resection or RPA loading/removal is modulated by chromatin context, which is a new finding.

Weaknesses:<br /> 1. The observation that HR is preferred in heterochromatin has been documented in many prior systems.

2. Although the conclusions of the authors are well-supported by the data, the study is somewhat limited in mechanistic detail and would be strengthened by additional use of the genetic tools in the model system, particularly with regard to whether the preference for using microhomologies near the DSB in heterochromatin arises due to modulation of resection or RPA loading stability (the latter is the preferred interpretation of the authors, but goes untested). Nucleosome stability, presence of HP1, etc. seem attractive.

3. Given the variability observed for EJ pathway usage at the four heterochromatic genomic sites probed in the manuscript there is some concern that a single euchromatic site may not be sufficient for rigorous comparisons. This is particularly true because there seems to be little transcription at the "euchromatic" region (Fig. S5). Given that we do not know what matters to dictate the outcomes (epigenetic modifications and/or transcriptional status), this is concerning.

4. (Minor) Some caution should be stated in comparing the HR frequency between this system (low single digits) and prior induction/tissue systems (~20%) because the time domain of cut and repair cycles is vastly different.

5. (Minor) While there are certainly strengths to using the spermatogonia system, one also wonders if it might not have some unique biology given the importance of maintaining genome integrity in this tissue (e.g. the piRNA pathways to repress transposon mobilization). A comment on this point would be welcomed.

6. (Minor) The authors argue that alt-EJ is less mutagenic as a consequence of the observed use of microhomologues closer to the DSB, but what they really mean perhaps is that less sequence is lost? A mutagenic outcome can be equally deleterious in other cases if 1, 5, or 20+ bps are lost, depending on the context.

Reviewer #1 (Public Review):

The authors sought to resolve the coordinated functions of the two muscles that primarily power flight in birds (supracoracoideus and pectoralis), with particular focus on the pectoralis. Technology has limited the ability to resolve some details of pectoralis function, so the authors developed a model that can make accurate predictions about this muscle's function during flight. The authors first measured aerodynamic forces, wing shape changes, and pectoralis muscle activity in flying doves. They used cutting-edge techniques for the aerodynamic and wing shape measurements and they used well-established methods to measure activity and length of the pectoralis muscle. The authors then developed two mathematical models to estimate the instantaneous force vector produced by the pectoralis throughout the wing stroke. Finally, the authors applied their mathematical models to other-sized birds in order to compare muscle physiology across species.

The strength of the methods is that they smoothly incorporate techniques from many complementary fields to generate a comprehensive model of pectoralis muscle function during flight. The high-speed structured-light technique for quantifying surface area during flight is novel and cutting-edge, as is the aerodynamic force platform used. These methods push the boundaries of what has historically been used to quantify their respective aspects of bird flight and their use here is exciting. The methods used for measuring muscle activation and length are standard in the field. Together, these provide both a strong conceptual foundation for the model and highlight its novelty. This model allows for estimations of muscle function that are not feasible to measure in live birds during flight at present. The weakness of this approach is that it relies heavily on a series of assumptions. While the research presented in this paper makes use of powerful methods from multiple fields, those methods each have assumptions inherent to them that simplify the biological system of study. This reduction in the complexity of phenomena allows specific measurements to be made. In joining the techniques of multiple fields to study greater complexity of the phenomenon of interest, the assumptions are all incorporated also. Furthermore, assumptions are inherent to mathematical modelling of biological phenomena. That being said, the authors acknowledge and justify their assumptions at each step and their model seems to be quite good at predicting muscle function.

Indeed, the authors achieve their aims. They effectively integrate methods from multiple disciplines to explore the coordination and function of the pectoralis and supracoracoideus muscles during flight. The conclusions that the authors derive from their model address the intended research aim.

The authors demonstrate the value of such interdisciplinary research, especially in studying complex behaviors that are difficult or infeasible to measure in living animals. Additionally, this work provides predictions for muscle function that can be tested empirically. These methods are certainly valuable for understanding flight, but also have implications for biologists studying movement and muscle function more generally.

Reviewer #2 (Public Review):

In this work, the authors investigated the pectoralis work loop and the function of the supracoracoideus muscle in the down stroke during slow flight in doves. The aim of this study was to determine how aerodynamic force is generated, using simultaneous high-speed measurements of the wings' kinematics, aerodynamics, and activation and strain of pectoralis muscles during slow flight. The measurements show a reduction in the angle of attack during mid-downstroke, which induces a peak power factor and facilitates the tensioning of the supracoracoideus tendon with pectoralis power, which then can be released in the up-stroke. By combining the data with a muscle mechanics model, the timely tuning of elastic storage in the supracoracoideus tendon was examined and showed an improvement of the pectoralis work loop shape factor. Finally, other bird species were integrated into the model for a comparative investigation.

The major strength of the methods is the simultaneous application of four high-speed techniques - to quantify kinematics, aerodynamics and muscle activation and strain - as well as the implementation of the time-resolved data into a muscle mechanics model. With a thorough analysis which supports the conclusions convincingly, the authors achieved their goal of reaching an improved understanding of the interplay of the pectoralis and supracoracoideus muscles during slow flight and the resulting energetic benefits.

Reviewer #1 (Public Review):

Summary:<br /> This manuscript builds upon the authors' previous work on the cross-talk between transcription initiation and post-transcriptional events in yeast gene expression. These prior studies identified an mRNA 'imprinting' phenomenon linked to genes activated by the Rap1 transcription factor (TF), a surprising role for the Sfp1 TF in promoting RNA polymerase II (RNAPII) backtracking, and a role for the non-essential RNAPII subunits Rpb4/7 in the regulation of mRNA decay and translation. Here the authors aimed to extend these observations to provide a more coherent picture of the role of Sfp1 in transcription initiation and subsequent steps in gene expression. They provide evidence for (1) a physical interaction between Sfp1 and Rpb4, (2) Sfp1 binding and stabilization of mRNAs derived from genes whose promoters are bound by both Rap1 and Sfp1 and (3) an effect of Sfp1 on Rpb4 binding or conformation during transcription elongation.

Strengths:<br /> This study provides evidence that a TF (yeast Sfp1), in addition to stimulating transcription initiation, can at some target genes interact with their mRNA transcripts and promote their stability. Sfp1 thus has a positive effect on two distinct regulatory steps. Furthermore, evidence is presented indicating that strong Sfp1 mRNA association requires both Rap1 and Sfp1 promoter binding and is increased at a sequence motif near the polyA track of many target mRNAs. Finally, they provide compelling evidence that Sfp1-bound mRNAs have higher levels of RNAPII backtracking and altered Rpb4 association or conformation compared to those not bound by Sfp1.

Weaknesses:<br /> The Sfp1-Rpb4 association is supported only by a two-hybrid assay that is poorly described and lacks an important control. Furthermore, there is no evidence that this interaction is direct, nor are the interaction domains on either protein identified (or mutated to address function).

The contention that Sfp1 nuclear export to the cytoplasm is transcription-dependent is not well supported by the experiments shown, which are not properly described in the text and are not accompanied by any primary data.<br /> The presence of Sfp1 in P-bodies is of unclear relevance and the authors do not ask whether Sfp1-bound mRNAs are also present in these condensates.

Further analysis of Sfp1-bound mRNAs would be of interest, particularly to address the question of whether those from ribosomal protein genes and other growth-related genes that are known to display Sfp1 binding in their promoters are regulated (either stabilized or destabilized) by Sfp1.

The authors need to discuss, and ideally address, the apparent paradox that their previous findings showed that Rap1 acts to destabilize its downstream transcripts, i.e. that it has the opposite effect of Sfp1 shown here.

Finally, recent studies indicate that the drugs used here to measure mRNA stability induce a strong stress response accompanied by rapid and complex effects on transcription. Their relevance to mRNA stability in unstressed cells is questionable.

Reviewer #1 (Public Review):

Li et al. report here on the expression of a G-protein subunit Gng13 in ectopic tuft cells that develop after severe pulmonary injury in mice. By deleting this gene in ectopic tuft cells as they arise, the authors observed worsened lung injury and greater inflammation after influenza infection, as well as a decrease in the overall number of ectopic tuft cells. This was in stark contrast to the deletion of Trpm5, a cation channel generally thought to be required for all functional gustatory signaling in tuft cells, where no phenotype is observed. Strengths here include a thorough assessment of lung injury via a number of different techniques. Weaknesses are notable: confusingly, these findings are at odds with reports from other groups demonstrating no obvious phenotype upon influenza infection in mice lacking the transcription factor Pou2f3, which is essential for all tuft cell specification and development. The authors speculate that heterogeneity within nascent tuft cell populations, specifically the presence of pro- and anti-inflammatory tuft cells, may explain this difference, but they do not provide any data to support this idea.

Reviewer #2 (Public Review):

Summary:<br /> The study by Li et al. aimed to demonstrate the role of the G𝛾13-mediated signal transduction pathway in tuft cell-driven inflammation resolution and repairing injured lung tissue. The authors showed a reduced number of tuft cells in the parenchyma of G𝛾13 null lungs following viral infection. Mice with a G𝛾13 null mutation showed increased lung damage and heightened macrophage infiltration when exposed to the H1N1 virus. Their further findings suggested that lung inflammation resolution, epithelial barrier, and fibrosis were worsened in G𝛾13 null mutants.

Strengths:<br /> The beautiful immunostaining findings do suggest that the number of tuft cells is decreased in Gr13 null mutants.

Weaknesses:<br /> The description of phenotypes, and the approaches used to measure the phenotypes are problematic. Rigorous investigation of the mouse lung phenotypes is needed to draw meaningful conclusions.

Reviewer #1 (Public Review):

Summary:<br /> In this paper, Song, Shi, and Lin use an existing deep learning-based sequence model to derive a score for each haplotype within a genomic region, and then perform association tests between these scores and phenotypes of interest. The authors then perform some downstream analyses (fine-mapping, various enrichment analyses, and building polygenic scores) to ensure that these associations are meaningful. The authors find that their approach allows them to find additional associations, the associations have biologically interpretable enrichments in terms of tissues and pathways, and can slightly improve polygenic scores when combined with standard SNP-based PRS.

Strengths:<br /> - I found the central idea of the paper to be conceptually straightforward and an appealing way to use the power of sequence models in an association testing framework.<br /> - The findings are largely biologically interpretable, and it seems like this could be a promising approach to boost power for some downstream applications.

Weaknesses:<br /> - The methods used to generate polygenic scores were difficult to follow. In particular, a fully connected neural network with linear activations predicting a single output should be equivalent to linear regression (all intermediate layers of the network can be collapsed using matrix-multiplication, so the output is just the inner product of the input with some vector). Using the last hidden layer of such a network for downstream tasks should also be equivalent to projecting the input down to a lower dimensional space with some essentially randomly chosen projection. As such, I am surprised that the neural network approach performs so well, and it would be nice if the authors could compare it to other linear approaches (e.g., LASSO or ridge regression for prediction; PCA or an auto-encoder for converting the input to a lower dimensional representation).

- A very interesting point of the paper was the low R^2 between the HFS scores in adjacent windows, but the explanation of this was unclear to me. Since the HFS scores are just deterministic functions of the SNPs, it feels like if the SNPs are in LD then the HFS scores should be and vice versa. It would be nice to compare the LD between adjacent windows to the average LD of pairs of SNPs from the two windows to see if this is driven by the fact that SNPs are being separated into windows, or if sei is somehow upweighting the importance of SNPs that are less linked to other SNPs (e.g., rare variants).

- There were also a number of robustness checks that would have been good to include in the paper. For instance, do the findings change if the windows are shifted? Do the findings change if the sequence is reverse-complemented?

- It was also difficult to contextualize the present work in terms of recent results showing that sequence models tend to not do very well at predicting cross-individual expression changes (and such results presumably hold for predicting cross-individual chromatin changes). In particular, it would be good for the authors to contrast their findings with the work of Alex Sasse and colleagues (https://www.biorxiv.org/content/10.1101/2023.03.16.532969.abstract) and Connie Huang and colleagues (https://www.biorxiv.org/content/10.1101/2023.06.30.547100.abstract).

Reviewer #2 (Public Review):

Summary:<br /> In this work, Song et al. propose a locus-based framework for performing GWAS and related downstream analyses including finemapping and polygenic risk score (PRS) estimation. GWAS are not sufficiently powered to detect phenotype associations with low-frequency variants. To overcome this limitation, the manuscript proposes a method to aggregate variant impacts on chromatin and transcription across a 4096 base pair (bp) loci in the form of a haplotype function score (HFS). At each locus, an association is computed between the HFS and trait. Computing associations at the level of imputed functional genomic scores should enable the integration of information across variants spanning the allele frequency spectrum and bolster the power of GWAS.

The HFS for each locus is derived from a sequence-based predictive model. Sei. Sei predicts 21,907 chromatin and TF binding tracks, which can be projected onto 40 pre-defined sequence classes ( representing promoters, enhancers, etc.). For each 4096 bp haplotype in their UKB cohort, the proposed method uses the Sei sequence class scores to derive the haplotype function score (HFS). The authors apply their method to 14 polygenic traits, identifying ~16,500 HFS-trait associations. They finemap these trait-associated loci with SuSie, as well as perform target gene/pathway discovery and PRS estimation.

Strengths:<br /> Sequence-based deep learning predictors of chromatin status and TF binding have become increasingly accurate over the past few years. Imputing aggregated variant impact using Sei, and then performing an HFS-trait association is, therefore, an interesting approach to bolster power in GWAS discovery. The manuscript demonstrates that associations can be identified at the level of an aggregated functional score. The finemapping and pathway identification analyses suggest that HFS-based associations identify relevant causal pathways and genes from an association study. Identifying associations at the level of functional genomics increases the portability of PRSs across populations. Imputing functional genomic predictions using a sequence-based deep learning model does not suffer from the limitation of TWAS where gene expression is imputed from a limited-size reference panel such as GTEx.

However, there are several major limitations that need to be addressed.

Major concerns/weaknesses:<br /> 1. There is limited characterization of the locus-level associations to SNP-level associations. How does the set of HFS-based associations differ from SNP-level associations?

2. A clear advantage of performing HFS-trait associations is that the HFS score is imputed by considering variants across the allele frequency spectrum. However, no evidence is provided demonstrating that rare variants contribute to associations derived by the model. Similarly, do the authors find evidence that allelic heterogeneity is leveraged by the HFS-based association model? It would be useful to do simulations here to characterize the model behavior in the presence of trait-associated rare variants.

3. Sei predicts chromatin status / ChIP-seq peaks in the center of a 4kb region. It would therefore be more relevant to predict HFS using overlapping sequence windows that tile the genome as opposed to using non-overlapping windows for computing HFS scores. Specifically, in line 482, the authors state that "the HFS score represents overall activity of the entire sequence, not only the few bp at the center", but this would not hold given that Sei is predicting activity at the center for any sequence.

4. Is the HFS-based association going to miss coding variation and several regulatory variants such as splicing variants? There are also going to be cases where there's an association driven by a variant that is correlated with a Sei prediction in a neighboring window. These would represent false positives for the method, it would be useful to identify or characterize these cases.

Additional minor concerns:<br /> 1. It's not clear whether SuSie-based finemapping is appropriate at the locus level, when there is limited LD between neighboring HFS bins. How does the choice of the number of causal loci and the size of the segment being finemapped affect the results and is SuSie a good fit in this scenario?

2. It is not clear how a single score is chosen from the 117 values predicted by Sei for each locus. SuSie is run assuming a single causal signal per locus, an assumption which may not hold at ~4kb resolution (several classes could be associated with the trait of interest). It's not clear whether SuSie, run in this parameter setting, is a good choice for variable selection here.

3.. A single HFS score is being chosen from amongst multiple tracks at each locus independently. Does this require additional multiple-hypothesis correction?

4. The results show that a larger number of loci are identified with HFS-based finemapping & that causal loci are enriched for causal SNPs. However, it is not clear how the number of causal loci should relate to the number of SNPs. It would be really nice to see examples of cases where a previously unresolved association is resolved when using HFS-based GWAS + finemapping.

5. Sequence-based deep learning model predictions can be miscalibrated for insertions and deletions (INDELs) as compared to SNPs. Scaling INDEL predictions would likely improve the downstream modeling.

Reviewer #1 (Public Review):

Summary:<br /> Shakhawat et al., investigated how enhancement of plasticity and impairment could result in the same behavioral phenotype. The authors tested the hypothesis that learning impairments result from saturation of plasticity mechanisms and had previously tested this hypothesis using mice lacking two class I major histocompatibility molecules. The current study extends this work by testing the saturation hypothesis in a Purkinje-cell (L7) specific Fmr1 knockout mouse mice, which have enhanced parallel fiber-Purkinje cell LTD. The authors found that L7-Fmr1 knockout mice are impaired on an oculomotor learning task and both pre-training, to reverse LTD, and diazepam, to suppress neural activity, eliminated the deficit when compared to controls.

Strengths:

This study tests the "saturation hypothesis" to understand plasticity in learning using a well-known behavior task, VOR, and an additional genetic mouse line with a cerebellar cell-specific target, L7-Fmr1 KO. This hypothesis is of interest to the community as it evokes a novel inquisition into LTD that has not been examined previously.

Utilizing a cell-specific mouse line that has been previously used as a genetic model to study Fragile X syndrome is a unique way to study the role of Purkinje cells and the Fmr1 gene. This increases the understanding in the field in regards to Fragile X syndrome and LTD.

The VOR task is a classic behavior task that is well understood, therefore using this metric is very reliable for testing new animal models and treatment strategies. The effects of pretraining are clearly robust and this analysis technique could be applied across different behavior data sets.

The rescue shown using diazepam is very interesting as this is a therapeutic that could be used in clinical populations as it is already approved.

There was a proper use of controls and all animal information was described. The statistical analysis and figures are clear and well describe the results.

Weaknesses:<br /> While the proposed hypothesis is tested using genetic animal models and the VOR task, LTD itself is not measured. This study would have benefited from a direct analysis of LTD in the cerebellar cortex in the proposed circuits.

Diazepam was shown to rescue learning in L7-Fmr1 KO mice, but this drug is a benzodiazepine and can cause a physical dependence. While the concentrations used in this study were quite low and animals were dosed acutely, potential side-effects of the drug were not examined, including any possible withdrawal. This drug is not specific to Purkinje cells or cerebellar circuits, so the action of the drug on cerebellar circuitry is not well understood for the study presented.

It was not mentioned if L7-Fmr1 KO mice have behavior impairments that worsen with age or if Purkinje cells and the cerebellar microcircuit are intact throughout the lifespan. Connections between Purkinje cells and interneurons could also influence the behavior results found.

While males and females were both used for the current study, only 7 of each sex were analyzed, which could be underpowered. While it might be justified to combine sexes for this particular study, it would be worth understanding this model in more detail.

Training was only shown up to 30 minutes and learning did not seem to plateau in most cases. What would happen if training continued beyond the 30 minutes? Would L7-Fmr1 KO mice catch-up to WT littermates?

The pathway discussed as the main focus for VOR in this learning paradigm was connections between parallel fibers (PF) and Purkinje cells, but the possibility of other local or downstream circuitry being involved was not discussed. PF-Purkinje cell circuits were not directly analyzed, which makes this claim difficult to assess.

The authors mostly achieved their aim and the results support their conclusion and proposed hypothesis. This work will be impactful on the field as it uses a new Purkinje-cell specific mouse model to study a classic cerebellar task. The use of diazepam could be further analyzed in other genetic models of neurodevelopmental disorders to understand if effects on LTD can rescue other pathways and behavior outcomes.

Reviewer #2 (Public Review):

This manuscript explores the seemingly paradoxical observation that enhanced synaptic plasticity impairs (rather than enhances) certain forms of learning and memory. The central hypothesis is that such impairments arise due to saturation of synaptic plasticity, such that the synaptic plasticity required for learning can no longer be induced. A prior study provided evidence for this hypothesis using transgenic mice that lack major histocompatibility class 1 molecules and show enhanced long-term depression (LTD) at synapses between granule cells and Purkinje cells of the cerebellum. The study found that a form of LTD-dependent motor learning-increasing the gain of the vestibulo-ocular reflex (VOR)-is impaired in these mice and can be rescued by manipulations designed to "unsaturate" LTD. The present study extends this line of investigation to another transgenic mouse line with enhanced LTD, namely, mice with the Fragile X gene knocked out. The main findings are that VOR gain increased learning is selectively impaired in these mice but can be rescued by specific manipulations of visuomotor experience known to reverse cerebellar LTD. Additionally, the authors show that a transient global enhancement of neuronal inhibition also selectively rescues gain increases learning. This latter finding has potential clinical relevance since the drug used to boost inhibition, diazepam, is FDA-approved and commonly used in the clinic. The evidence provided for the saturation is somewhat indirect because directly measuring synaptic strength in vivo is technically difficult. Nevertheless, the experimental results are solid. In particular, the specificity of the effects to forms of plasticity previously shown to require LTD is remarkable. The authors should consider including a brief discussion of some of the important untested assumptions of the saturation hypothesis, including the requirement that cerebellar LTD depends not only on pre- and postsynaptic activity (as is typically assumed) but also on the prior history of synaptic activation.

Reviewer #1 (Public Review):

Summary:

Direction selectivity (DS) in the visual system is first observed in the radiating dendrites of starburst amacrine cells (SACs). Studies over the last two decades have aimed to understand the mechanisms that underlie these unique properties. Most recently, a 'space-time' model has garnered special attention. This model is based on two fundamental features of the circuit. First, distinct anatomical types of bipolar cells (BCs) are connected to proximal/distal regions of each of the SAC dendritic sectors (Kim et al., 2014). Second, that input across the length of the starburst is kinetically diverse, a hypothesis that has only recently gained some experimental support using iGluSnFR imaging (Srivastava et al., 2022). However, in these prior studies, the sustained/transient distinctions in BC input that are proposed to underlie direction selectivity were shown to be present mainly in responses to stationary stimuli. When BC receptive field properties are probed using white noise stimuli, the kinetic differences between proximal/distal BC input are relatively subtle or nonexistent (Gaynes et al., 2022; Strauss et al., 2022, Srivastava et al., 2022). Thus, if and how BCs contribute to direction selectivity driven by moving spots that are commonly used to probe the circuit remains to be clarified. To address this issue, Gaynes et al., combine evolutionary computational modeling (Ankri et al., 2020) with two-photon iGluSnFR imaging to address to what degree BCs contribute to the generation of direction selectivity in the starburst dendrites.

Strengths:

Combining theoretical models and iGluSnFR imaging is a powerful approach as it first provides a basic intuition on what is required for the generation of robust DS, and then tests the extent to which the experimentally measured BC output meets these requirements.

The conclusion of this study builds on the previous literature and comprehensively considers the diverse BC receptive field properties that may contribute to DS (e.g. size, lag, rise time, decay time).

By 'evolving' bipolar inputs to produce robust DS in a model network, these authors provide a sound framework for understanding which kinetic properties could potentially be important for driving downstream DS. They suggest that response delay/decay kinetics, rather than the center/surround dynamics are likely to be most relevant (albeit the latter could generate asymmetric responses to radiating/looming stimuli).

Weaknesses:

Finally, these authors report that the experimentally measured BC responses are far from optimal for generating DS. Thus, the BC-based DS mechanism does not appear to explain the robust DS observed experimentally (even with mutual inhibition blocked). Nevertheless, I feel the comprehensive description of BC kinetics and the solid assessment of the extent to which they may shape DS in SAC dendrites, is a significant advancement in the field.

Reviewer #2 (Public Review):

Summary:

In this study, the authors sought to understand how the receptive fields of bipolar cells contribute to direction selectivity in starburst amacrine cell (SAC) dendrites, their post synaptic partners. In previous literature, this contribution is primarily conceptualized as the 'space-time wiring model', whereby bipolar cells with slow-release kinetics synapse onto proximal dendrites while bipolar cells with faster kinetics synapse more distally, leading to maximal summation of the slow proximal and fast distal depolarizations in response to motion away from the soma. The space-time wiring contribution to SAC direction selectivity has been extensively tested in previous literature using connectomic, functional, and modeling approaches. However, the authors argue that previous functional studies of bipolar cell kinetics have focused on static stimuli, which may not accurately represent the spatiotemporal properties of the bipolar cell receptive field in response to movement. Moreover, this group and others have recently shown that bipolar cell signal processing can change directionally when visual stimuli starts within the receptive field rather than passing through it, complicating the interpretation of moving stimuli that start within a bipolar cell of interest's receptive field (e.g. stimulating only one branch of a SAC or expanding/contracting rings). Thus, the authors choose to focus on modeling and functionally mapping bipolar cell kinetics in response to moving stimuli across the entire SAC dendritic field.

General Comments:

There have been several studies that have addressed the contribution of space-time wiring to SAC process direction selectivity. This study offers a more complete assessment of potential impact space-time wiring can have on this dendrite computation. The experimental results based on glutamate imaging assess the kinetics of glutamate release under conditions of visual stimulation across a large region of retina largely confirm previous observations. By combining their model with this experiment data, they conclude that even the optimal space-time wiring is not sufficient to explain the SAC process DS. Though there is no conclusion which of the many other proposed cellular and circuit mechanisms could potentially contribute to this computation, the limited role for spacetime wiring is firmly established.

Reviewer #3 (Public Review):

Summary:

Gaynes et al. investigated the presynaptic and postsynaptic mechanisms of starburst amacrine cell (SAC) direction selectivity in the mouse retina by computational modeling and glutamate sensitivity (iGluSnFR) imaging methods. Using the SAC computational simulation, the authors initially tested bipolar cell contributions (space-time wiring model, presynaptic effect) and SAC axial resistance contributions (postsynaptic effect) to the SAC DS. Then, the authors conducted two-photon iGluSnFR imaging from SACs to examine the presynaptic glutamate release and found seven clusters of ON-responding and six clusters of OFF-responding bipolar cells. They were categorized based on their response kinetics: delay, onset phase, decay time, and others. Finally, the authors used cluster data to reconstruct bipolar cell inputs to SACs that generate direction selectivity. They concluded that presynaptic effects through the space-time wiring model only account for a fraction of SAC DS.

The article has many interesting findings, and the data presentation is superb. Strengths and weaknesses are summarized below.

Major Strengths:

The authors utilized solid technology to conduct computational modeling with Neuron software and a machine-learning approach based on evolutionary algorithms. Results are effectively and thoroughly presented.

The space-time wiring model was evaluated by changing bipolar cell response properties in the proximal and distal SAC dendrites. Many response parameters in bipolar cells are compared, and DSI is compared in Figure 3. These parameter comparisons are valuable to the field.

Two-photon microscopy was used to measure the bipolar cell glutamate outputs onto SACs by conducting iGluSnFR imaging. All the data sets, including images and transients, are elegantly presented. The authors analyzed the response based on various parameters, which generated more than several response clusters. The clustering is convincing.

Major Weaknesses:

The computational modeling demonstrates intriguing results: SAC dendritic morphology produces dendritic isolation, and a massive input overcomes the dendritic isolation (Figure 1). This modeling seems to be generated by basic dendritic cable properties. However, it has been reported that SAC dendrites express Kv3 and voltage-gated Ca channels. Are they incorporated into this model? If not, how about comparing these channel contributions?

In Figure 9 the authors generated the bipolar cell cluster alignment based on the space-time wiring model. The space-time wiring model has been proposed based on the EM study that distinct types of bipolar cells synapse on distinct parts of SAC dendrites (Green et al 2016, Kim et al 2014). While this is one of the representative Reicardt models, it is not fully agreed upon in the field (see Stincic et al 2016). Therefore, the authors' approach might be only hypothetical without concrete evidence for geographical cluster distributions. Is there any data suggesting each cluster's location on the SAC dendrites? I assume that the iGluSnFR imaging was conducted on the SAC dendritic network, which does not provide geographical information. How about injecting the iGluSnFR-AAV at a lower titer, which labels only some SACs in a tissue? This method may reveal each cluster's location on SAC dendrites.

The authors found that there are seven ON clusters and six OFF clusters, which are supposed to be bipolar cell terminals. However, bipolar cells reported to provide synaptic inputs are T-7, T-6, and multiple T-5s for ON SACs and T-1, T-2, and T-3s for OFF SACs. The number of types is less than the number of clusters. Is there a possibility of clusters belonging to glutamatergic amacrine cells? Please provide a discussion regarding the relations between clusters and cell types.

In Figure 5B, representative traces are shown responding to moving bars in horizontal directions. These did not show different responses to two directional stimuli. Is there any directional preference from other ROIs? Yonehara's group recently exhibited the bipolar cells' direction selectivity (Matsumoto et al 2021). Did you see any correlations with their results? Please discuss.

Reviewer #1 (Public Review):

Summary: The authors set out to clarify the molecular mechanism of endocytosis (re-uptake) of synaptic vesicle (SV) membrane in the presynaptic terminal following release. They have examined the role of presynaptic actin, and of the actin regulatory proteins diaphanous-related formins ( mDia1/3), and Rho and Rac GTPases in controlling the endocytosis. They successfully show that presynaptic membrane-associated actin is required for normal SV endocytosis in the presynaptic terminal and that the rate of endocytosis is increased by activation of mDia1/3. They show that RhoA activity and Rac1 activity act in a partially redundant and synergistic fashion together with mDia1/3 to regulate the rate of SV endocytosis. The work adds substantially to our understanding of the molecular mechanisms of SV endocytosis in the presynaptic terminal.

Strengths: The authors use state-of-the-art optical recording of presynaptic endocytosis in primary hippocampal neurons, combined with well-executed genetic and pharmacological perturbations to document effects of alteration of actin polymerization on the rate of SV endocytosis. They show that removal of the short amino-terminal portion of mDia1 that associates with the membrane interrupts the association of mDia1 with membrane actin in the presynaptic terminal. They then use a wide variety of controlled perturbations, including genetic modification of the amount of mDia1/3 by knock-down and knockout, combined with inhibition of activity of RhoA and Rac1 by pharmacological agents, to document the quantitative importance of each agent and their synergistic relationship in regulation of endocytosis.<br /> The analysis is augmented by ultrastructural analyses that demonstrate the quantitative changes in numbers of synaptic vesicles and in uncoated membrane invaginations that are predicted by the optical recordings.<br /> The manuscript is well-written and the data are clearly explained. Statistical analysis of the data is strengthened by the very large number of data points analyzed for each experiment.

Weaknesses: There are no major weaknesses. The optical images as first presented are small and it is recommended that the authors provide larger, higher-resolution images.

Reviewer #2 (Public Review):

Summary:<br /> This manuscript expands on previous work from the Haucke group which demonstrated the role of formins in synaptic vesicle endocytosis. The techniques used to address the research question are state-of-the-art. As stated above there is a significant advance in knowledge, with particular respect to Rho/Rac signalling.

Strengths:<br /> The major strength of the work was to reveal new information regarding the control of both presynaptic actin dynamics and synaptic vesicle endocytosis via Rho/Rac cascades. In addition, there was further mechanistic insight regarding the specific function of mDia1/3. The methods used were state-of-the-art.

Weaknesses:<br /> There are a number of instances where the conclusions drawn are not supported by the submitted data, or further work is required to confirm these conclusions.

Reviewer #1 (Public Review):

Summary:<br /> O'Leary and colleagues present data identifying several procedures that alter discrimination between novel and familiar objects, including time, environmental enrichment, Rac-1, context reexposure, and brief reminders of the familiar object. This is complimented with an engram approach to quantify cells that are active during learning to examine how their activation is impacted following each of the above procedures at test. With this behavioral data, authors apply a modeling approach to understand the factors that contribute to good and poor object memory recall.

Strengths:<br /> • Authors systematically test several factors that contribute to poor discrimination between novel and familiar objects. These results are extremely interesting and outline essential boundaries of incidental, nonaversive memory.<br /> • These results are further supported by engram-focused approaches to examine engram cells that are reactivated in states with poor and good object recognition recall.

Weaknesses:<br /> • For the environmental enrichment, authors seem to suggest objects in the homecage are similar to (or reminiscent of) the familiar object. Thus, the effect of improved memory may not be related to enrichment per se as much as it may be related to the preservation of an object's memory through multiple retrievals, not the enriching experiences of the environment itself. This would be consistent with the brief retrieval figure. Authors should include a more thorough discussion of this.

• Authors should justify the marginally increased number of engram cells in the non-enrichment group that did not show object discrimination at test, especially relative to other figures. More specific cell counting criteria may be helpful for this. For example, was the DG region counted for engram and cfos cells or only a subsection?

• It is unclear why the authors chose a reactivation time point of 1hr prior to testing. While this may be outside of the effective time window for pharmacological interference with reconsolidation for most compounds, it is not necessarily outside of the structural and functional neuronal changes accompanied by reconsolidation-related manipulations.

• Figure 5: Levels of exploration at test are inconsistent between manipulations. This is problematic, as context-only reexposures seem to increase exploration for objects overall in a manner that I'm unsure resembles 'forgetting'. Instead, cross-group comparisons would likely reveal increased exploration time for familiar and novel objects. While I understand 'forgetting' may be accompanied by greater exploration towards objects, this is inconsistent across and within the same figure. Further, this effect is within the period of time that rodents should show intact recognition. Instead, context-only exposures may form a competing (empty context) memory for the familiar object in that particular context.

• I am concerned at the interpretation that a memory is 'forgotten' across figures, especially considering the brief reminder experiments. Typically, if a reminder session can trigger the original memory or there is rapid reacquisition, then this implies there is some savings for the original content of the memory. For instance, multiple context retrievals in the absence of an object reminder may be more consistent with procedures that create a distinct memory and subsequently recruit a distinct engram.

• Authors state that spine density decreases over time. While that may be generally true, there is no evidence that mature mushroom spines are altered or that this is consistent across figures. Additionally, it's unclear if spine volume is consistently reduced in reactivated and non-reactivated engram cells across groups. This would provide evidence that there is a functionally distinct aspect of engram cells that is altered consistently in procedures resulting in poor recognition memory (e.g. increased spine density relative to spine density of non-reactivated engram cells and non-engram cells)

• Authors should discuss how the enrichment-neurogenesis results here are compatible with other neurogenesis work that supports forgetting.

Reviewer #2 (Public Review):

Summary:<br /> The manuscript examines an important question about how an inaccessible, natural forgotten memory can be retrieved through engram ensemble reactivation. It uses a variety of strategies including optogenetics, behavioral and pharmacological interventions to modulate engram accessibility. The data characterize the time course of natural forgetting using an object recognition task, in which animals can retrieve 1 day and 1 week after learning, but not 2 weeks later. Forgetting is correlated with lower levels of cell reactivation (c-fos expression during learning compared to retrieval) and reduction in spine density and volume in the engram cells. Artificial activation of the original engram was sufficient to induce recall of the forgotten object memory while artificial inhibition of the engram cells precluded memory retrieval. Mice housed in an enriched environment had a slower rate of forgetting, and a brief reminder before the retrieval session promoted retrieval of a forgotten memory. Repeated reintroduction to the training context in the absence of objects accelerated forgetting. Additionally, activation of Rac1-mediated plasticity mechanisms enhanced forgetting, while its inhibition prolonged memory retrieval. The authors also reproduce the behavioral findings using a computational model inspired by Rescorla-Wagner model. In essence, the model proposes that forgetting is a form of adaptive learning that can be updated based on prediction error rules in which engram relevancy is altered in response to environmental feedback.

Strengths:<br /> 1) The data presented in the current paper are consistent with the authors claim that seemingly forgotten engrams sometimes remain accessible. This suggests that retrieval deficits can lead to memory impairments rather than a loss of the original engram (at least in some cases).

2) The experimental procedures and statistics are appropriate, and the behavioral effects appear to be very robust. Several key effects are replicated multiple times in the manuscript.

Weaknesses:<br /> 1) My major issue with the paper is the forgetting model proposed in Figure 7. Prior work has shown that neutral stimuli become associated in a manner similar to conditioned and unconditioned stimuli. As a result, the Rescorla-Wagner model can be used to describe this learning (Todd & Homes, 2022). In the current experiments, the neutral context will become associated with the unpredicted objects during training (due to a positive prediction error). Consequently, the context will activate a memory for the objects during the test, which should facilitate performance. Conversely, any manipulation that degrades the association between the context and object should disrupt performance. An example of this can be found in Figure 5A. Exposing the mice to the context in the absence of the objects should violate their expectations and create a negative prediction error. According to the Rescorla-Wagner model, this error will create an inhibitory association between the context and the objects, which should make it harder for the former to activate a memory of the latter (Rescorla & Wagner, 1972). As a result, performance should be impaired, and this is what the authors find. However, if the cells encoding the context and objects were inhibited during the context-alone sessions (Figure 5D) then no prediction error should occur, and inhibitory associations would not be formed. As a result, performance should be intact, which is what the authors observe.

What about forgetting of the objects that occurs over time? Bouton and others have demonstrated that retrieval failure is often due to contextual changes that occur with the passage of time (Bouton, 1993; Rosas & Bouton, 1997, Bouton, Nelson & Rosas, 1999). That is, both internal (e.g. state of the animal) and external (e.g. testing room, chambers, experimenter) contextual cues change over time. This shift makes it difficult for the context to activate memories with which it was once associated (in the current paper, objects). To overcome this deficit, one can simply re-expose animals to the original context, which facilitates memory retrieval (Bouton, 1993). In Figure 2D, the authors do something similar. They activate the engram cells encoding the original context and objects, which enhances retrieval.

Therefore, the forgetting effects presented in the current paper can be explained by changes in the context and the associations it has formed with the objects (excitatory or inhibitory). The results are perfectly predicted by the Rescorla-Wagner model and the context-change findings of Bouton and others. As a result, the authors do not need to propose the existence of a new "forgetting" variable that is driven by negative prediction errors. This does not add anything novel to the paper as it is not necessary to explain the data (Figures 7 and 8).

2) I also have an issue with the conclusions drawn from the enriched environment experiment (Figure 3). The authors hypothesize that this manipulation alleviates forgetting because "Experiencing extra toys and objects during environmental enrichment that are reminiscent of the previously learned familiar object might help maintain or nudge mice to infer a higher engram relevancy that is more robust against forgetting.". This statement is completely speculative. A much simpler explanation (based on the existing literature) is that enrichment enhances synaptic plasticity, spine growth, etc., which in turn reduces forgetting. If the authors want to make their claim, then they need to test it experimentally. For example, the enriched environment could be filled with objects that are similar or dissimilar to those used in the memory experiments. If their hypothesis is correct, only the similar condition should prevent forgetting.

3) It is well-known that updating can both weaken or strengthen memory. The authors suggest that memory is updated when animals are exposed to the context in the absence of the objects. If the engram is artificially inhibited (opto) during context-only re-exposures, memory cannot be updated. To further support this updating idea, it would be good to run experiments that investigate whether multiple short re-exposures to the training context (in the presence of the objects or during optogenetic activation of the engram) could prevent forgetting. It would also be good to know the levels of neuronal reactivation during multiple re-exposures to the context in the absence versus context in the presence of the objects.

4) There are a number of studies that show boundary conditions for memory destabilization/reconsolidation. Is there any evidence that similar boundary conditions exist to make an inaccessible engram accessible?

5) More details about how the quantification of immunohistochemistry (c-fos, BrdU, DAPI) was performed should be provided (which software and parameters were used to consider a fos positive neurons, for example).

6) Duration of the enrichment environment was not detailed.

Reviewer #3 (Public Review):

Summary: The manuscript by Ryan and colleagues uses a well-established object recognition task to examine memory retrieval and forgetting. They show that memory retrieval requires activation of the acquisition engram in the dentate gyrus and failure to do so leads to forgetting. Using a variety of clever behavioural methods, the authors show that memories can be maintained and retrieval slowed when animals are reared in environmental enrichment and that normally retrieved memories can be forgotten if exposed to the environment in which the expected objects are no longer presented. Using a series of neural methods, the authors also show that activation or inhibition of the acquisition engram is key to memory expression and that forgetting is due to Rac1.

Strengths:<br /> This is an exemplary examination of different conditions that affect successful retrieval vs forgetting of object memory. Furthermore, the computational modelling that captures in a formal way how certain parameters may influence memory provides an important and testable approach to understanding forgetting.<br /> The use of the Rescorla-Wagner model in the context of object recognition and the idea of relevance being captured in negative prediction error are novel (but see below).<br /> The use of gain and loss of function approaches are a considerable strength and the dissociable effects on behaviour eliminate the possibility of extraneous variables such as light artifacts as potential explanations for the effects.

Weaknesses:<br /> Knowing what process (object retrieval vs familiarity) governed the behavioural effect in the present investigation would have been of even greater significance.

The impact of the paper is somewhat limited by the use of only one sex.

While relevance is an interesting concept that has been operationalized in the paper, it is unclear how distinct it is from extinction. Specifically, in the case where the animals are exposed to the context in the absence of the object, the paper currently expresses this as a process of relevance - the objects are no longer relevant in that context. Another way to think about this is in terms of extinction - the association between the context and the objects is reduced results in a disrupted ability of the context to activate the object engram.

Reviewer #1 (Public Review):

This manuscript provides an important case study for in-depth research on the adaptability of vertebrates in deep-sea environments. Through analysis of the genomic data of the hadal snailfish, the authors found that this species may have entered and fully adapted to extreme environments only in the last few million years. Additionally, the study revealed the adaptive features of hadal snailfish in terms of perceptions, circadian rhythms and metabolisms, and the role of ferritin in high-hydrostatic pressure adaptation. Besides, the reads mapping method used to identify events such as gene loss and duplication avoids false positives caused by genome assembly and annotation. This ensures the reliability of the results presented in this manuscript. Overall, these findings provide important clues for a better understanding of deep-sea ecosystems and vertebrate evolution.

Reviewer #2 (Public Review):

This paper presents improved, chromosome level assemblies of the hadal snailfish and Tanaka's snailfish. This is an extension and update of previous work from the group on the hadal snailfish genome. The chromosomal assemblies allow comparisons of genome architecture between a shallow water snailfish and the hadal snailfish to aid inference on timing of colonization of trenches and genomic changes that may have been adaptive for that move.

The comparisons in genomic architecture are compelling: genes present in Tanaka's snailfish that are lost in hadal snailfish that involve whole regions of the genome that no longer map even though adjacent regions do map between the species and across a large evolutionary distance to stickleback. Or genes that are duplicated in hadal snailfish but only appear as single copy in other fishes. The paper focuses on genes in the eye, in hearing, in circadian rythms, and in ROS scavaging. These are all functions that could play a role in adapting to the hadal environment.

The genomic comparisons all seem sound. Stylistically I would prefer if the authors could introduce the gene product and protein function every time they introduce a gene locus. They introduce a gene and general function, but don't usually note what the protein encoded by the gene is and what it's specific function is.

I found the paper generally well written, and the data compelling and creatively displayed.

Upon revision, the authors have commendably addressed all reviewer comments and added a slew of additional analyses. I find the paper stronger, better argued and have no further questions or comments.

Reviewer #1 (Public Review):

Summary:<br /> This valuable study analyzes the contribution of fungal and bacterial microbiota species to the growth and development of Drosophila. The authors use bacterial and fungal species associated with Drosophila in the wild to analyze their respective contributions in promoting larval growth in a decaying banana, mimicking the natural niche of fruit fly. They found that some fungal species and some fungus/bacteria combinations effectively promote growth by supplementing key branched amino acids in the food substratum. Production of these amino acids by Drosophila itself is not sufficient, and only fungal species that secrete these amino acids into the medium can sustain Drosophila growth. Thus, the authors clarify how facultative symbionts contribute to host growth in a natural setting by changing the food substratum in a dynamic manner.

Strengths:<br /> The natural setting developed by the authors to analyze the impact of the microbiota is clearly valuable, as is the focus on the role of fungal microbiota species. This complements studies of Drosophila microbiota that have previously focused on bacterial species and used a lab setting.

While there has been an extensive focus on obligate endosymbionts or gut symbionts, this study analyzes how facultative symbionts shape the food substratum and influence host growth.<br /> A last strength of this study is that it analyzes the contribution of Drosophila microbiota over a dynamic timeframe, analyzing how microbial species change in decaying fruit over time.

Weaknesses:<br /> 1) The author should better review what we know of fungal Drosophila microbiota species as well as the ecology of rotting fruit. Are the microbiota species described in this article specific to their location/setting? It would have been interesting to know if similar species can be retrieved in other locations using other decaying fruits. The term 'core' in the title suggests that these species are generally found associated with Drosophila but this is not demonstrated. The paper is written in a way that implies the microbiota members they have found are universal. What is the evidence for this? Have the fungal species described in this paper been found in other studies? Even if this is not the case, the paper is interesting, but there should be a discussion of how generalizable the findings are.

2) Can the author clearly demonstrate that the microbiota species that develop in the banana trap are derived from flies? Are these species found in flies in the wild? Did the authors check that the flies belong to the D. melanogaster species and not to the sister group D. simulans?

3) Did the microarrays highlight a change in immune genes (ex. antibacterial peptide genes)? Whatever the answer, this would be worth mentioning. The authors described their microarray data in terms of fed/starved in relation to the Finke article. This is fine they should clarify if they observed significant differences between species (differences between species within bacteria or fungi, and more generally differences between bacteria versus fungi).

4) The whole paper - and this is one of its merits - points to a role of the Drosophila larval microbiota in processing the fly food. Are these bacterial and fungal species found in the gut of larvae/adults? Are these species capable of establishing a niche in the cardia of adults as shown recently in by the Ludington lab (Dodge et al.,)? Previous studies have suggested that microbiota members stimulate the Imd pathway leading to an increase in digestive proteases (Erkosar/Leulier). Are the microbiota species studied here affecting gut signaling pathways beyond providing branched amino acids?

Reviewer #2 (Public Review):

Summary:<br /> In this manuscript, Mure et al investigated host-microbe interactions in wild-mimicked settings. They analyzed microbiome composition using bananas that had been fed on by wild larvae and found that the microbiota composition shifted from the early stage of feeding to the later stage of the fermentation process proceeded. They isolated several yeast and bacterial species from the food, and examined larval growth on banana-based food, mimicking natural setting where germ-free larvae cannot grow on it. The authors found that a yeast, Hanseniaspora uvarum, can support larval growth sufficiently, and insists that branched-chain amino acids (BCAAs) provided by the yeast may partly be accounted for the growth support. Interestingly, other isolated yeast species, some were non-supportive strains in terms of larval growth, can assist larval development when they were heat-killed. Besides, they showed that acetic acid bacteria, isolated from well-fermented banana (later-stage food), is sufficiently supportive but their presence depended on other microbes, lactic acid bacteria or yeast.

Strengths:<br /> So far, host-microbe studies using Drosophila melanogaster have relatively less focused on the roles of fungi and many studies used only "model" yeasts. In the experimental setting where natural conditions may be well mimicked, the authors successfully isolated wild yeast species and convincingly showed that wild yeast plays a critical role in promoting host growth. In addition, the authors provided intriguing observations that all of the heat-killed yeast promoted larval growth even though some of the yeast never support the development when they were alive, suggesting that wild yeasts produce the necessary nutrients for larval development, but the nutrients of non-supportive yeasts are not accessible to the host. This might be an interesting indication for further studies revealing host-fungi interactions.

Weaknesses:<br /> The experimental setting that, the authors think, reflects host-microbe interactions in nature is one of the key points. However, it is not explicitly mentioned whether isolated microbes are indeed colonized in wild larvae of Drosophila melanogaster who eat bananas. Another matter is that this work is rather descriptive. A molecular level explanation is missing in "interspecies interactions" between lactic acid bacteria (or yeast) and acetic acid bacteria that assure their inhabitation.

Reviewer #3 (Public Review):

Summary: In this manuscript, Mure et al. describe interactions between diet, microbiome, and host development using Drosophila as a model. By characterizing microbial communities in food sources and animals, the authors showed that microbial community dynamics in the food source is critical for host development.

Strengths: This is a very interesting study where authors managed to tackle a difficult question in an elegant manner. How the interactions between different microbial species within the microbiome shape host physiology is an area of great interest but equally challenging due to the complexity of intercellular interactions in complex, host-associated microbial communities. By using a simplified model and interrogating not only microbe-microbe and host-microbe interactions, but also the role played by diet, authors were able to identify significant interactions during fly development.

Weaknesses: All weaknesses observed in the original manuscript have been corrected in the current version.

Reviewer #1 (Public Review):

The manuscript investigates the binding of PHD-BD, a tandem of reader domains in the C-terminus of BPTF, to modified histone tail peptides and nucleosomes. It focuses on the differences in binding affinity between peptide and nucleosome substrates for BPTF PHD-BD. Using the dCypher approach, they find that multi-modified peptide substrates (both acetylation and methylation) do not increase PHD-BD binding affinity. They argue that histone peptide substrates do not support the histone code model, which champions that multivalent engagement by PHD-BD with a multi-modified substrate would lead to stronger binding when compared to the engagement of each domain alone. In contrast, when using nucleosome substrates, even though the overall affinity is reduced, the affinity for H3K4me3triac (double modification) is tighter than either modification on its own. This is consistent with the histone code model.

A strength of the manuscript is that it further delineates the contribution of each domain by again using dCypher to compare peptide and nucleosome binding of the PHD and BD domains alone, as well as tandem domain constructs where each domain has been inactivated by a point mutation (W2891A for the PHD and N3007A for the BD). PHD alone had a lower affinity for nucleosomes than peptides overall. With peptide substrates, PHD had the highest affinity for H3K4me3 and reduced affinity for H3K4me3triac; while with nucleosomes this trend was reversed. BD alone showed an affinity for acetylated H3 and H4 peptides but surprisingly was unable to bind nucleosomes. PHD requires the combination of H3K4 methylation and H3 tail acetylation for binding, and when partnered with BD, which is not able to bind nucleosomes alone, interestingly confers specificity for K14ac and K18ac. The in vivo relevance is argued using CUT&RUN analysis.

NMR spectroscopy is further used to show that PHD-BD binds acetylated H3 in a multivalent manner while forming a unique complex with H3K4me3triac. Deleting the N-terminal A1 region of H3 abolishes the binding of PHD-BD, implying its importance for recognition. The authors also discuss a "fuzzy complex" that forms between H3 and DNA, as well as H4 and DNA, which explains the occlusion of histone tail accessibility in the nucleosome. By changing the sidechain charge, such as with PTMs, this interaction can be weakened and allow PHD in this case to bind to the modified H3 tail. Comparisons between spectra of the H4 tail, H4 tail with DNA, and the H4 tail in the nucleosome are made and used to argue for H4-DNA interactions in the nucleosome.

The conclusions of the manuscript are very well-supported by the data and reveal a lot of insight into how the two reader domains of BPTF interact with modified nucleosomes. In many places, however, the manuscript is written more generally as if the conclusions apply in all cases (e.g. the title, abstract, and introduction) and this remains to be determined. It is also overstated that there is a belief that peptides perfectly recapitulate nucleosomes. It should also be pointed out that the nucleosomes are multi-valent and the data cannot discriminate binding of a single PHD-BD to single or multiple tails, and that the work is limited as it is using a construct of BPTF and in fact, there is at least one other reader domain involved.

Reviewer #2 (Public Review):

This manuscript by Musselman and coworkers uses a commercial library of modified histone peptides and mononucleosomes to probe the substrate specificity of the PHD-bromodomain combination of the BPTF protein. They arrive at the conclusion that BPTF preferably binds H3K4me3 and H3K18ac in the H3 tail. By using NMR with lableled H4 protein in nucleosomes they show that the H4 tail interacts with DNA, which may limit its ability to interact with BPTF. Finally, experiments in cells demonstrate that BPTF, H3K4me3, and H3K18ac occupy overlapping regions of chromatin. The authors suggest that recruitment of BPTF to specific regions of chromatin is driven by the co-binding of H3K4me3 and H3K18ac by BPTF. This study is of interest to readers interested in understanding the functions of the BPTF protein in cells.

In this reviewer's opinion, the manuscript needs some revision and the inclusion of some missing information.

1) The authors seem to have overlooked the fact that mononucleosome substrates have been in use for determining the substrate specificity and mechanisms of quite a few enzymes that simply do not act on peptide substrates. For example, Dot1L doesn't do anything with peptides nor does COMPASS/Set1, both of which require intact nucleosomal substrates to measure their activity in response to ubiquitylated H2B. Thus, the authors' refinement of the "histone code hypothesis" is unnecessary and overdone. I would suggest that they instead cite examples where nucleosome substrates have provided answers that cannot be obtained from peptide substrates alone. For example, extensive work from the Muir and Allis labs.

2) Ruthenburg and Allis in Cell 2011 conducted similar experimentation and concluded that H3K4me3-H4K16ac is a modification state bound by BPTF in cells. They also showed co-localization in ChIP-seq experiments and demonstrated preferential pulldowns with BPTF and semisynthetic methylated and acetylated nucleosomes. The authors have entirely ignored these previous results in their own discussions. Readers would benefit from a side-by-side comparison of the two acetylation states to get a sense of which is a stronger interaction and why both seemingly correlate in CUTnRUN or ChIP-seq.

3) The idea that electrostatics may modulate tail accessibility was reported by Musselman and coworkers for the H3 tail in eLife 2018. Yet the PHD domain of BPTF clearly binds H3K4me3 in nucleosomes. In light of this prior observation, the NMR experiments now with H4 tail seem repetitive and not informative regarding BPTF's bromodomain binding. Also, missing is the effect of H4K16acetylation on H4 tail dynamics, which would be pertinent to addressing the hypothesis regarding the BPTF bromodomain binding H4K16ac

4) The NMR experiments are all undertaken with 150mM KCl with no NaCl present. While NMR experimental constraints are understandable, the authors should avoid sweeping statements from NMR experiments regarding the dynamism of histone tails in chromatin, unless specific experiments are cited/conducted to demonstrate the same in cells. Many factors may contribute to the exclusion of BPTF from modified histone tails in cells, including the binding of other reader proteins, and the precise genomic localization of these modifications vis-a-vis BPTF. The important role of anchoring proteins must also be taken into account when considering binding/non-binding of substrates by CAPs. Thus, the NMR experiments presented in the manuscript do not report on whether BPTF binds H4K16ac in cells or indeed in vitro. If the PHD domain is capable of ultimately binding the H3 tail despite the tail's fuzzy interaction with DNA, the question remains as to why the bromodomain may not do so for acetylated H4 tails?

This manuscript reports several interesting elements regarding BPTF regulation, but as presented it is missing some key comparisons with prior information that makes it hard for readers to assess the relevance of the results presented.

Reviewer #1 (Public Review):

This paper combines an array of techniques to study the role of cholecystokinin (CCK) in motor learning. Motor learning in a pellet reaching task is shown to depend on CCK, as both global and locally targeted CCK manipulations eliminate learning. This learning deficit is linked to reduced plasticity in the motor cortex, evidenced by both slice recordings and two-photon calcium imaging. Furthermore, CCK receptor agonists are shown to rescue motor cortex plasticity and learning in knockout mice. While the behavioral results are clear, the specific effects on learning are not directly tested, nor is the specificity pathway between rhinal CCK neurons and the motor cortex. In general, the results present interesting clues about the role of CCK in motor learning, though the specificity of the claims is not fully supported.

Since all CCK manipulations were performed throughout learning, rather than after learning, it is not clear whether it is learning that is affected or if there is a more general motor deficit. Related to this point, Figure 1D appears to show a general reduction in reach distance in CCK-/- mice. A general motor deficit may be expected to produce decreased success on training day 1, which does not appear to be the case in Figure 1C and Figure 2B, but may be present to some degree in Figure 5B. Or, since the task is so difficult on day 1, a general motor deficit may not be observable. It is therefore inconclusive whether the behavioral effect is learning-specific.

The paper implicates motor cortex-projecting CCK neurons in the rhinal cortex as being a key component in motor learning. However, the relative importance of this pathway in motor learning is not pinned down. The necessity of CCK in the motor cortex is tested by injecting CCK receptor antagonists into the contralateral motor cortex (Figure 2), though a control brain region is not tested (e.g. the ipsilateral motor cortex), so the specificity of the motor cortex is not demonstrated. The learning-related source of CCK in the motor cortex is also unclear, since even though it is demonstrated that CCK neurons in the rhinal cortex project to the motor cortex in Figure 4D, Figure 4C shows that there is also a high concentration of CCK neurons locally within the motor cortex. Likewise, the importance of the projection from the rhinal cortex to the motor cortex is not specifically tested, as rhinal CCK neurons targeted for inactivation in Figure 5 include all CCK cells rather than motor cortex-projecting cells specifically.

CCK is suggested to play a role in producing reliable activity in the motor cortex through learning through two-photon imaging experiments. This is useful in demonstrating what looks like normal motor cortex activity in the presence of CCK receptor antagonist, indicating that the manipulations in Figure 2 are not merely shutting off the motor cortex. It is also notable that, as the paper points out, the activity appears less variable in the CCK manipulations (Figure 3G). However, this could be due to CCK manipulation mice having less-variable movements throughout training. The Hausdorff distance is used for quantification against this point in Figure 1E, though the use of the single largest distance between trajectories seems unlikely to give a robust measure of trajectory similarity, which is reinforced by the CCK-/- traces looking much less variable than WT traces in Figure 1D. The activity effects may therefore be expected from a general motor deficit if that deficit prevented the mice from normal exploratory movements and restricted the movement (and activity) to a consistently unsuccessful pattern.

Finally, slice experiments are used to demonstrate the lack of LTP in the motor cortex following CCK knockout, which is rescued by CCK receptor agonists. This is a nice experiment with a clear result, though it is unclear why there are such striking short-term depression effects from high-frequency stimulation observed in Figure 6A that are not observed in Figure 1H. Also, relating to the specificity of the proposed rhinal-motor pathway, these experiments do not demonstrate the source of CCK in the motor cortex, which may for example originate locally.

Reviewer #2 (Public Review):

This study aims to test whether and if so, how cholecystokinin (CCK) from the mice rhinal cortex influences neural activity in the motor cortex and motor learning behavior. While CCK has been previously shown to be involved in neural plasticity in other brain regions/behavioral contexts, this work is the first to demonstrate its relationship with motor cortical plasticity in the context of motor learning. The anatomical projection from the rhinal cortex to the motor cortex is also a novel and important finding and opens up new opportunities for studying the interactions between the limbic and motor systems. I think the results are convincing to support the claim that CCK and in particular CCK-expressing neurons in the rhinal cortex are critical for learning certain dexterous movements such as single pellet reaching. However, more work needs to be done, or at least the following concerns should be addressed, to support the hypothesis that it is specifically the projection from the rhinal cortex to the motor cortex that controls motor learning ability in mice.

1) Because CCK is expressed in multiple brain regions, as the authors recognized, results from the CCK knock-out mice could be due to a global loss of neural plasticity. In comparison, the antagonist experiment is in my opinion the most convincing result to support the specific effect of CCK in the motor cortex. However, it is unclear to me whether the CCK knock-out mice exhibited an impaired ability to learn in general, i.e., not confined to motor skills. For instance, it would be very valuable to show whether these mice also had severe memory deficits; this would help the field to understand different or similar behavioral effects of CCK in the case of global vs. local loss of function. If the CCK knock-out mice only exhibited motor learning deficits, that would be surprising but also very interesting given previous studies on its effect in other brain areas.

2) Related to my last point, I believe that normal neural plasticity should be essential to motor skill learning throughout development not just during the current task. Thus, it would be important to show whether these CCK knock-out mice present any motor deficits that could have resulted from a lack of CCK-mediated neural plasticity during development. If not, the authors should explain how this normal motor learning during development is consistent with their major hypothesis in this study (e.g., is CCK not critical for motor learning during early development).

3) Lines 198-200 and Fig. 2C: The authors found that the vehicle group showed significantly increased "no grasp" behavior, and reasoned that the implantation of a cannula may have caused injuries to the motor cortex. In order to support their reasoning and make the control results more convincing, I think it would be helpful to show histology from both the antagonist and control groups and demonstrate motor cortical injury in some mice of the vehicle group but not the antagonist group. Otherwise, I'm a bit concerned that the methods used here could be a significant confounding factor contributing to motor deficits.

4) The authors showed that chemogenetic inhibition of CCK neurons in the rhinal cortex impaired motor skill learning in the pellet-reaching task. However, we know that the rhinal cortex projects to multiple brain regions besides the motor cortex (e.g., other cortical areas and the hippocampus). Thus, the conclusion/claim that the observed behavioral deficits resulted from inhibited rhinal-motor cortical projections is not strongly supported without more targeted loss-of-function or rescue experiments.

It would also be very informative to the field to compare the specific behavioral deficits, if any, of inhibiting specific downstream targets of the rhinal CCK neurons. As a concrete example, the hippocampus may be involved in learning more sophisticated motor skills (as the authors pointed out in the Discussion) besides the motor cortex. It would be a critical result if the authors could either show or exclude the possibility that the motor learning deficits observed in CCK-/- mice were at least partially due to the inhibition of hippocampal plasticity. This echoes my earlier point (point 1) that it is unclear whether the effect of lacking CCK in knock-out mice is specific in the motor cortex or engages multiple brain regions.

Lastly, because Fig. 4 only showed histology in the rhinal and motor cortices, I am not sure whether the motor cortex solely receives CCK input from the rhinal cortex. A more comprehensive viral tracing result could be important to both supporting the circuit-specificity of the observed behavior in this study and providing a clearer picture of where the motor cortex receives CCK inputs.

5) I am glad to see the CCK4 rescue experiment to demonstrate the sufficiency of CCK in promoting motor learning. However, the rescue experiment lacked specificity: IP injection did not allow specific "gain of function" in the motor cortex but instead, the improved learning ability in CCK knock-out mice could be a result of a global effect of CCK4 across multiple brain regions. CCK4 injection specifically targeted at the motor cortex would be necessary to support the sufficiency of CCK-regulated neuroplasticity in the motor cortex to promote motor learning.

Reviewer #1 (Public Review):

This is a review of the manuscript entitled "Pharmacologic hyperstabilisation of the HIV-1 capsid lattice induces capsid failure" by Faysal et al., in this manuscript the authors used an elegant single virion fluorescence assay based on TIRF to measure the stability of mature HIV cores. Virions were biotinylated and captured onto glass coverslips through specific Biotin-Avidin interactions. Immobilized virions were then introduced to the imaging buffer which contained the pore-forming protein DLY, and fluorescently labeled CypA. Mature virions were identified through the binding of CypA which had a red fluorescent tag allowing them to measure the dynamics of GFP trapped within the mature cores as well as the CypA bound outside the core. The authors show that the addition of LEN starting from about 50nM stabilized the mature cores even after cores have ruptured and released their internal GFP. Higher concentration of Len results in ultrastabilization of the cores and rapid rupture leading to the release of GFP at an earlier timepoint. A biochemical assembly assay was performed which showed uM quantities of Len synergized with IP6 to promote CA assembly. Purified mature virions were also treated with 700nM of Len and analyzed by CryoET, this analysis showed an increased representation of irregular cores within the Len-treated sample. Putting all of this together, the authors concluded that Len facilitates core rupture through hyperstabilization of HIV cores, as described in the title.

While I have found this work technically well performed and well explained, I do not believe that the presented data supports the conclusions reached by the authors.

Reviewer #3 (Public Review):

In this article, Faisal et. al., use a combinatorial approach to look at the mechanisms of HIV-capsid inhibition by the highly potent drug Lenacepavir (LEN). The authors conclude that LEN induces capsid opening, but hyper-stabilizes the remaining capsid lattice during the early stages, and adversely affects the assembly of capsids during late stages of HIV-1 infection. Additionally, they suggest that hyper-stabilization effects of LEN on the capsid-lattice are induced by a low occupancy of this highly potent drug, while less potent inhibitors like PF74 need high occupancy on the lattice to induce similar effects. Taken together their findings shine a light on the importance of the capsid binding pocket targeted by multiple inhibitors including LEN, PF74, BI-2, and host-factor CPSF6 on overall capsid assembly, its stability in cells, and its role in HIV-1 infection.

Strengths:<br /> 1. Combinatorial approach using single-molecule imaging, cryoET and cellular assays show the adverse effects of LEN on HIV-1 capsid assembly, capsid disassembly, and block to virus infectivity.<br /> 2. Several novel insights are obtained in this paper, including the cryoET-data showing 2-layers of capsid formation in the presence of LEN. CPSF6-peptide binding to capsids, and their effect on stability.

Weakness:<br /> 1. Interpretation of the capsid stability data is focused on single virus traces rather than population analysis, which might paint a different picture of the conclusions.<br /> 2. The description and interpretation of the data in the results sections and the conclusions are inconsistent, and somewhat confusingly presented for the general non-expert audience.

Reviewer #2 (Public Review):

The authors provide a nice resource of putative direct BMP target genes in Nematostella vectensis by performing ChIP-seq with an anti-pSmad1/5 antibody, while also performing bulk RNA-seq with BMP2/4 or GDF5 knockdown embryos. Genes that exhibit pSmad1/5 binding and have changes in transcription levels after BMP signaling loss were further annotated to identify those with conserved BMP response elements (BREs). Further characterization of one of the direct BMP target genes (zswim4-6) was performed by examining how expression changed following BMP receptor or ligand loss of function, as well as how loss or gain of function of zswim4-6 affected development and BMP signaling. The authors concluded that zswim4-6 modulates BMP signaling activity and likely acts as a pSMAD1/5 dependent co-repressor. However, the mechanism by which zswim4-6 affects the BMP gradient or interacts with pSMAD1/5 to repress target genes is not clear. The authors test the activity of a zswim4-6 homologue in zebrafish (zswim5) by over-expressing mRNA and find that pSMAD1/5/9 labeling is reduced and that embryos have a phenotype suggesting loss of BMP signaling, and conclude that zswim4-6 is a conserved regulator of BMP signaling. This conclusion needs further support to confirm BMP loss of function phenotypes in zswim5 over-expression embryos.

Major comments

1. The BMP direct target comparison was performed between Nematostella, Drosophila, and Xenopus, but not with existing data from zebrafish (Greenfeld 2021, Plos Biol). Given the functional analysis with zebrafish later in the paper it would be nice to see if there are conserved direct target genes in zebrafish, and in particular, is zswim5 (or other zswim genes) are direct targets. Since conservation of zswim4-6 as a direct BMP target between Nematostella and Xenopus seemed to be part of the rationale for further functional analysis, it would also be nice to know if this is a conserved target in zebrafish.

Related to this, in the discussion it is mentioned that zswim4/6 is also a direct BMP target in mouse hair follicle cells, but it wasn't obvious from looking at the supplemental data in that paper where this was drawn from.

2. The loss of zswim4-6 function via MO injection results in changes to pSmad1/5 staining, including a reduction in intensity in the endoderm and gain of intensity in the ectoderm, while over-expression results in a loss of intensity in the ectoderm and no apparent change in the endoderm. While this is interesting, it is not clear how zswim4-6 is functioning to modify BMP signaling, and how this might explain differential effects in ectoderm vs. endoderm. Is the assumption that the mechanism involves repression of chordin? And if so one could test the double knockdown of zswim4-6 and chordin and look for the rescue of pSad1/5 levels or morphological phenotype.

3. Several experiments are done to determine how zswim4-6 expression responds to the loss of function of different BMP ligands and receptors, with the conclusion being that swim4-6 is a BMP2/4 target but not a GDF5 target, with a lot of the discussion dedicated to this as well. However, the authors show a binary response to the loss of BMP2/4 function, where zswim4-6 is expressed normally until pSmad1/5 levels drop low enough, at which point expression is lost. Since the authors also show that GDF5 morphants do not have as strong a reduction in pSmad1/5 levels compared to BMP2/4 morphants, perhaps GDF5 plays a positive but redundant role in swim4-6 expression. To test this possibility the authors could inject suboptimal doses of BMP2/4 MO with GDF5 MO and look for synergy in the loss of zswim4-6 expression.

4. The zswim4-6 morphant embryos show increased expression of zswim4-6 mRNA, which is said to indicate that zswim4-6 negatively regulates its own expression. However in zebrafish translation blocking MOs can sometimes stabilize target transcripts, causing an artifact that can be mistakenly assumed to be increased transcription (https://www.ncbi.nlm.nih.gov/pmc/articles/PMC7162184/). Some additional controls here would be warranted for making this conclusion.

5. Zswim4-6 is proposed to be a co-repressor of pSmad1/5 targets based on the occupancy of zswim4-6 at the chordin BRE (which is normally repressed by BMP signaling) and lack of occupancy at the gremlin BRE (normally activated by BMP signaling). This is a promising preliminary result but is based only on the analysis of two genes. Since the authors identified BREs in other direct target genes, examining more genes would better support the model.

6. The rationale for further examination of zswim4-6 function in Nematostella was based in part on it being a conserved direct BMP target in Nematostella and Xenopus. The analysis of zebrafish zswim5 function however does not examine whether zswim5 is a BMP target gene (direct or indirect). BMP inhibition followed by an in situ hybridization for zswim5 would establish whether its expression is activated downstream of BMP.

7. Although there is a reduction in pSmad1/5/9 staining in zebrafish injected with zswim5 mRNA, it is difficult to tell whether the resulting morphological phenotypes closely resemble zebrafish with BMP pathway mutations (such as bmp2b). More analysis is warranted here to determine whether stereotypical BMP loss of function phenotypes are observed, such as dorsalization of the mesoderm and loss of ventral tail fin.

Reviewer #3 (Public Review):

To identify direct targets of BMP signal in Nematostella, the authors performed ChIP-seq using an antibody against phosphorylated SMAD1/5 (pSMAD1/5) at late gastrula and late planula stages. In accordance with the highly dynamic BMP activity detected using immunofluorescence, pSMAD1/5 binding profiles change drastically as the larvae develop, with only a fraction of target genes shared between these two time points. The authors then followed up with RNA-seq in control versus BMP2/4 KD embryos and identified significant expression changes in many transcription factors and signaling molecules, including the Gbx-Hox genes, which are known to regulate endoderm patterning. These results, in conjunction with a thorough validation using in situ hybridization, strongly support the authors' claim that the BMP signal in Nematostella directly controls a small set of second-tier targets which in turn execute the morphogenic functions.

Next, the authors explored the conservation of BMP downstream targets by intersecting their candidate list with two published datasets from Drosophila (2-3hpf) and Xenopus (NF20 stage). Results from such an analysis should be taken with a grain of salt, as the developmental time points and biological context examined here are not necessarily comparable. Furthermore, whole genome duplication in vertebrates means multiple copies of transcription factors and signaling molecules belonging to the same family exist in Xenopus, making a homology-based comparison difficult. A handful of shared targets were identified between different species, although no statics were provided to support the significance of such an observation.

The authors then focused on Zswim4-6, one of the identified BMP targets with a high pSMAD1/5 enrichment level, and dissected its regulatory properties on BMP activity. Using complimentary knockdown and overexpression experiments, the authors rigorously demonstrated that Zswim4-6 is crucial to maintaining the proper pSMAD1/5 gradient at the late gastrula stage. By ectopically overexpressing a GFP tagged form of Zswim4-6, the authors performed low input ChIP-qPCR and confirmed that Zswim4-6 selectively binds to a regulatory region of a BMP-repressed gene, suggesting it may function as a co-repressor for certain BMP targets.<br /> Lastly, the authors examined the effect of Zswim5, a bilaterian homolog of Zswim4-6, during zebrafish D-V axis establishment. Overexpression of Zswim5 leads to a dampened pSMAD1/5 gradient and dorsalization of the fish larvae, hinting at the possibility that Zswim5 may function as a BMP modulator in zebrafish as well.

Overall, despite certain caveats, the experimental evidence supports the claims from the authors that Zswim4-6 is directly activated by and reciprocally modulates the BMP activity in Nematostella. The work presented here opens exciting possibilities to further dissect the gene regulatory networks downstream of the cnidarian BMP signaling pathway and expands our knowledge on the evolution of a bilaterally symmetric body plan.

Reviewer #1 (Public Review):

Summary:

Through a series of psychophysical experiments, Merkel et al examined the process of feature-based resource allocation during parallel feature value tracking, where subjects are asked to simultaneously track changing but spatially inseparable color streams. They find that tracking precision is highly imbalanced between streams, and the tracking precision changes over time by alternating between streams at a rate of ~1Hz.

Strengths:

The study addresses an intriguing research question that fills a gap in existing literature, and was carefully designed and well-executed, with a series of experiments and control experiments.

Weaknesses:

1. My main concern is the null effect of precision estimation pattern between cued and un-cued trials. It is well established that relative to the un-cued stimuli, the cued stimuli obtain more attentional resource and this study claimed serial attentional resource allocation during parallel feature value tracking. However, all Experiments 3a-c did not find any difference in precision estimates between these two types of trials.<br /> 2. Results of Exp.1 in the main text were different from those in Figure.<br /> 3. It would be helpful to add more details for the assignation of response 1 and response 2 to target 1 and target 2, respectively, in all experiments.

Reviewer #2 (Public Review):

The authors asked the question about whether and how changing feature values within the same feature dimensions are tracked. Using a series of behavioral studies combined with modeling approaches, the authors report interesting results regarding a robust, uneven distribution of attentional resources between two changing feature values (in a 2:1 ratio), alternating at 1 Hz. Although the results are clear, it is important to rule out the possible biases due to computational processes. The results advanced our understanding of how parallel tracking of multiple feature values within the same dimension is achieved.

Reviewer #3 (Public Review):

The study is interesting and the results are informative in how well people can report colors of two superimposed dot clouds. It reveals that there are trade-offs between reporting two colors. However, I have a few basic but major concerns with the present study and its conclusions about people's abilities to continuously track color values and the rate at which attention may be allocated across the two streams which I am outlining below.

1) The first concern regards the task that was used to measure continuous tracking of feature values, which in my view is ambiguous in whether it truly assesses active tracking of features or rather short-term memory of the last-seen colors. Specifically, participants were viewing two colored dot clouds that then turned gray, and were asked to report each of the colors they saw using continuous report. The test usually occurred after 6-8s (in Exp. 1 &2), so while not completely predictable, participants could easily perform the task without tracking both feature streams continuously and simply perform the color report based on the very last colors they saw. In other words, it does not seem necessary to know which color belonged to which stream, or what color it was before, to perform the task successfully. Thus, it is unclear to what extent this task is actually measuring active tracking, the same way tracking of spatial locations in multiple-object tracking tasks has been studied, which is the literature that the authors are trying to draw parallels to. In multiple-object tracking tasks, targets and nontarget objects look identical and so to keep track of which of the moving objects are targets, participants need to attend to them actively and selectively. (Similarly, the original feature-tracking study by Blaser et al., at least in their main experiment, people were asked to track an object superimposed on a second object which required continuous and selective tracking of that object).

2) The main claim that tracking two colors relies on a shared and strictly limited resource is primarily based on the relation between the two responses people give, such that the first response about one color tends to be higher accuracy than for the second response of the other color across participants. In my view, this is a relatively weak version of looking at trade-offs in resources, and it would have been more compelling to show such trade-offs at a single-trial level, or assess them with well-established methods that have been developed to look at attentional bottlenecks such as attention-operating characteristics that allow quantifying the cost of adding an additional task in a precise and much more direct manner.

3) Finally, the data of the last experiment is taken as evidence that feature-based selection oscillates at 1Hz between the two streams. This is based on response errors changing across time points with respect to an exogenous cue that is thought to "reset" attentional allocation to one stream. Only one of three data sets (which uses relatively sparse temporal sampling) shows a significant interaction between cue and time, and given that there was no a priori prediction of when such interaction should occur, this result begs for a replication to ensure that this is not a false positive result. Furthermore, based on the analyses done in the paper, it may very well be the case that the presumed "switching rate" is entirely non-oscillatory based on a recent very important paper by Geoffrey Brookshire (2022, Nature Human Behavior) that demonstrates that frequency analysis are not just sensitive to periodic but also aperiodic temporal structures. The paper also has a series of suggested analyses that could be used here to further test the current conclusions.

Reviewer #3 (Public Review):

This paper studies the role of the core PCP pathway on tissue morphogenesis of the Drosophila pupil wing. The authors used three different core PCP mutants to compare the cell dynamics with the wild type and conclude that core PCP does not guide the global patterns of cell dynamics during pupal wing morphogenesis. They use the previously published "triangle method" to extract modes of deformation (total shear, cell elongation, cell rearrangements) and find that they are the same (to within error) in the core PCP mutants. Moreover, the global shape of the wing at the end of the process is nearly the same, too.

Using laser ablation and a rheological model, the paper also investigates the effect of the core PCP pathway on the short-time mechanical properties of the tissue. The authors find that the short-time mechanical response is different in core PCP mutants. This is surprising, as most researchers in the field assume that the short-time recoil velocity is a proxy for tissue mechanics, and therefore also predictive of global tissue deformations. So the observation that the short-time recoils are different, while the global response is the same, is important for the field to understand.

A challenge with the paper as written is that it does not clearly explain how to reconcile these two observations, stating in the discussion that "the proportionality factor [which relates short-time recoil to tissue mechanics] can depend on the genotype and can change in time". It is possible that the data and model in the paper could be used to make a more convincing and clear statement.

The paper is conceptually interesting, methodologically sound, and likely impactful to the broad area of tissue mechanics and mechanobiology.

Reviewer #1 (Public Review):

Mohibi et al. utilized genetic approaches to determine the role of FDX1 in the regulation of development, oncogenesis, and metabolism. The strengths of the current study are the utilization of both in vivo and in vitro methods coupled to classical biochemical/molecular biology tools and lipidomic screening. The data provided is convincing demonstrating genetic loss of even one allele of FDX1 promotes premature death, increased incidence of adenocarcinoma, and dysregulated lipid metabolism. The authors provide further mechanistic evidence showing enhanced SREBP2 activation, which could potentially be underlying the altered lipid metabolism observed in their model. These findings are likely to provide a novel target for the amelioration to lipid metabolic disorders as the authors show genetic overexpression of FDX1 can reduce intracellular lipid accumulation.

Reviewer #2 (Public Review):

In this manuscript, the Chen group aimed to understand the role of FDX1 in vivo. While its role in the biogenesis of steroids and bile acids, Vitamin A/D metabolism, and lipoylation of TCA enzymes has been extensively studied biochemically, its role in physiology and lipid metabolism is still unknown. The authors established a conditional Fdx1 KO mice and performed a series of experiments to demonstrate the physiological role of Fdx1 in mice. The obtained evidence convincingly supports the major conclusion of the study. The manuscript is well and concisely written.

Strengths:<br /> • Solid data showing that Fdx1+/- mice are prone to steatohepatitis and Fdx1+/- cells accumulate lipids<br /> • Untargeted MS profiling the changes of lipids upon Fdx1 KO.<br /> • Clear evidence indicating that the ABCA1-SREBP1/2 pathway is involved in the function of Fdx1 in lipid metabolism.

Weaknesses:<br /> • use of Fdx1+/- MEFs, instead of using Fdx1-/- MEFs, could be well justified.

Reviewer #1 (Public Review):

Weber et al. collect locus coeruleus (LC) tissue blocks from 5 neurotypical European men, dissect the dorsal pons around the LC, and prepare 2-3 tissue sections from each donor on a slide for 10X spatial transcriptomics. From three of these donors, they also prepared an additional section for 10x single nucleus sequencing. Overall, the results validate well-known marker genes for the LC (e.g. DBH, TH, SLC6A2), and generate a useful resource that lists genes that are enriched in LC neurons in humans, with either of these two techniques. A comparison with publicly available mouse and rat datasets identifies genes that show reliable LC enrichment across species. Their analyses also support recent rodent studies that have identified subgroups of interneurons in the region surrounding the LC, which show enrichment for different neuropeptides. In addition, the authors claim that some LC neurons co-express cholinergic markers and that a population of serotonin (5-HT) neurons is located within or near the LC. These last two claims must be taken with great caution, as several technological limitations restrict the interpretation of these results. Technical limitations currently limit the ability to integrate spatial and single-nucleus sequencing, yet the manuscript presents a valuable resource on the gene expression landscape of the human LC.

Reviewer #2 (Public Review):

The data generated for this paper provides an important resource for the neuroscience community. The locus coeruleus (LC) is the known seed of noradrenergic cells in the brain. Due to its location and size, it remains scarcely profiled in humans. Despite the physically minute structure containing these cells, its impact is wide-reaching due to the known neuromodulatory function of norepinephrine (NE) in processes like attention and mood. As such, profiling NE cells has important implications for most neurological and neuropsychiatric disorders. This paper generates transcriptomic profiles that are not only cell-specific but which also maintain their spatial context, providing the field with a map for the cells within the region.

Strengths:

Using spatial transcriptomics in a morphologically distinct region is a very attractive way to generate a map. Overlaying macroscopic information, i.e. a region with greater pigmentation, with its corresponding molecular profile in an unbiased manner is an extremely powerful way to understand the specific cellular and molecular composition of that brain structure.

The technologies were used with an astute awareness of their limitations, as such, multiple technologies were leveraged to paint a more complete and resolved picture of the cellular composition of the region. For example, the lack of resolution in the spatial transcriptomic platform was compensated by complementary snRNA-seq and single molecule FISH.

This work has been made publicly available and accessible through a user-friendly application such that any interested researcher can investigate the level of expression of their gene of interest within this region.

Two important implications from this work are 1) the potential that the gene regulatory profiles of these cells are only partially conserved across species, humans, and rodents, and 2) that there may be other neuromodulatory cell types within the region that were otherwise not previously localized to the LC

Weaknesses:

Given that the markers used to identify cells are not as specific as they need to be to definitively qualify the desired cell type, the results may be over-interpreted. Specifically, TH is the primary marker used to qualify cells as noradrenergic, however, TH catalyzes the synthesis of L-DOPA, a precursor to dopamine, which in turn is a precursor for epinephrine and norepinephrine suggesting some of the cells in the region may be dopaminergic and not NE cells. Indeed, there are publications to support the presence of dopaminergic cells in the LC (see Kempadoo et al. 2016, Takeuchi et al., 2016, Devoto et al. 2005). This discrepancy is further highlighted by the apparent lack of overlap per given Visium spots with TH, SCL6A2, or DBH. While the single-nucleus FISH confirms that some of the cells in the region are noradrenergic, others very possibly represent a different catecholamine. As such it is suggested that the nomenclature for the cells be reconsidered.

The authors are unable to successfully implement unsupervised clustering with the spatial data, this greatly reduces the impact of the spatial technology as it implies that the transcriptomic data generated in the study did not have enough resolution to identify individual cell types.

The sample contribution to the results is highly unbalanced, which consequently, may result in ungeneralizable findings in terms of regional cellular composition, limiting the usefulness of the publicly available data.

This study aimed to deeply profile the LC in humans and provide a resource to the community. The combination of data types (snRNA-seq, SRT, smFISH) does in fact represent this resource for the community. However, due to the limitations, of which, some were described in the manuscript, we should be cautious in the use of the data for secondary analysis. For example, some of the cellular annotations may lack precision, the cellular composition also may not reflect the general population, and the presence of unexpected cell types may represent the accidental inclusion of adjacent regions, in this case, serotonergic cells from the Raphe nucleus.

Nonetheless having a well-developed app to query and visualize these data will be an enormous asset to the community especially given the lack of information regarding the region in general.

Reviewer #3 (Public Review):

In this study, the authors present the first comprehensive transcriptome map of the human locus coeruleus using two independent but complementary approaches, spatial transcriptomics and single-nucleus RNA sequencing. Several canonical features of locus coeruleus neurons that have been described in rodents were conserved, but potentially important species differences were also identified. This work lays the foundation for future descriptive and experimental approaches to understanding the contribution of the locus coeruleus to healthy brain function and disease.

This study has many strengths. It is the first reported comprehensive map of the human LC transcriptome and uses two independent but complementary approaches (spatial transcriptomics and snRNA-seq). Some of the key findings confirmed what has been described in the rodent LC, as well as some intriguing potential genes and modules identified that may be unique to humans and have the potential to explain LC-related disease states. The main limitations of the study were acknowledged by the authors and include the spatial resolution probably not being at the single cell level and the relatively small number of samples (and questionable quality) for the snRNA-seq data. Overall, the strengths greatly outweigh the limitations. This dataset will be a valuable resource for the neuroscience community, both in terms of methodology development and results that will no doubt enable important comparisons and follow-up studies.

Reviewer #1 (Public Review):

The work by Ohigashi and colleagues addresses the developmental and lineage relationship of a newly characterized thymus epithelial cell (TEC) progenitor subset. The authors take advantage of an elegant and powerful set of experimental approaches to demonstrate that CCL21-expressing TECs appear early in thymus organogenesis and that these cells, which are centrally located, go on to give rise to medullary (m)TECs. What makes the findings intriguing is that these CCL21-expressing mTECs are a distinct subset, which do not express RANK or AIRE, and transcriptomic and lineage tracing approaches point to these cells as potential mTEC progenitor-like cells. Of note, using in vitro and in vivo precursor-product cell transfer experiments, the authors show that this subset has a developmental potential to give rise to AIRE+ self-antigen-displaying mTECs, revealing that CCL21-expressing mTECs can give rise to distinct mTEC subsets. This functional duality provides an attractive rationale for the necessary function of mTECs, which is to attract CCR7+ thymocytes that have just undergone positive selection in the thymus cortex to enter the medulla to undergo tolerance-induction against self-antigen-displaying mTECs. Overall, the work is well supported and offers new insights into the diverse functions of the medullary compartment, and how two distinct subsets of mTECs can achieve it.

Reviewer #2 (Public Review):

Summary:

The authors set out to discover a developmental pathway leading to functionally diverse mTEC subsets. They show that Ccl21 is expressed early during thymus ontogeny in the medullary area. Fate-mapping gives evidence for the Ccl21 positive history of Aire positive mTECs as well as of thymic tuft cells and postnatally of a certain percentage of cTECs. Therefore, the differentiation potential of Ccl21+ TECs is tested in reaggregate thymus experiments - using embryonic or postnatal Ccl21+ TECs. From these experiments, the authors conclude that at least embryonic mTECs in large part pass through a Ccl21 positive stage prior to differentiation towards an Aire expressing or tuft cell stage.

The authors are using Ccl21a as a marker for a bipotent progenitor that is detectable in the embryonic thymus and is still present at the adult stage mainly giving rise to mTECs. The choice of this marker gene is very interesting since Ccl21 expression can directly be linked to an important aspect in thymus biology: the expression of Ccl21 by cells in the thymic medulla allows trafficking of T cells into the medulla in order to undergo T cell selection.

Making use of the Ccl21 detection, the authors can nicely show that cells actively expressing Ccl21 are localized throughout the medulla at an embryonic stage but also in adult thymus tissue. This suggests, that this progenitor is not accumulating at a specific area inside the medulla. This is a new finding.

Moreover, the finding that a Ccl21+ progenitor population plays a functional role in thymocyte trafficking towards the medulla has not been described. Thus, Ccl21 expression may be used to localize a late bipotent progenitor in the thymic lobes.<br /> In addition, in Fig.8, the authors provide evidence that these progenitor cells have the potential to self-maintain as well as to differentiate in reaggregate experiments at E17 (not at 4 weeks of age). The first point is of great interest and importance since these cells in theory can be of therapeutic use.

Overall assessment:

The authors highlight a developmental pathway starting from a Ccl21-expressing TEC progenitor that contributes to a functionally diverse mTEC repertoire. This is a welcome addition to current knowledge of TEC differentiation.

Reviewer #3 (Public Review):

In this manuscript, the authors define the developmental trajectory resulting in a diverse mTEC compartment. Using a variety of approaches, including a novel CCL21-fate mapping model, data is presented to argue that embryonic CCL21-expressing thymocyte attracting mTECs naturally convert to into self-antigen displaying mTEC subsets, including Aire+ mTECs and thymic tuft cells. Perhaps somewhat surprisingly, a large fraction of cTECs were also marked for having expressed CCL21, suggesting that there exists some conversion of mTEC (progenitors) into cTEC, a developmentally interesting observation that could be followed up later. Overall, the experimental setup, writing, and conclusions, are all outstanding.

Reviewer #1 (Public Review):

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

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

Weaknesses: The protocol is not clear. I could not even find how many women were going to be enrolled, the timelines of the study, the statistical methods ("comparing" is not statistics) or the power calculations.<br /> Tables 2 and 3 are too schematic - surely the authors must have an approximate idea of what the actual numbers are behind the green, red and yellow colors.<br /> Figure 1 comparing screening and vaccination is somewhat misleading. They screen 20 birth cohorts but vaccinate only 5 birth cohorts. Furthermore, the theoretical gains of screening has not really been attained in any country in practise. Modelling can be a difficult task and the commentary does not provide any detail on how to evaluate what was done. It just seems unnecessary to attack vaccination as a motivation on why screening needs to be modernised.

Reviewer #2 (Public Review):

Summary:

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

Strengths and weaknesses

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

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

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

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

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

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

Reviewer #3 (Public Review):

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

Strengths:

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

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

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

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

Weaknesses:

Potential ascertainment bias due to the lack of specified biopsy (such as small four quadrant biopsies or small biopsies across the transformation zone) when aceto-white areas are not identified. This has the potential lead to lead to an over-estimate of sensitivity of the triage approach, particularly in the setting of VIA as compared to colposcopy. While the authors specify endocervical sampling in this setting, using curette or brush (for cytology), this may not be as sensitive unless clinicians are experienced in endocervical curette procedures.

Reviewer #1 (Public Review):

Summary:<br /> The presented study focuses on the role of formin-like 2 (FMNL2) in oocyte meiosis. The authors assessed FMNL2 expression and localization in different meiotic stages and subsequently, by using siRNA, investigated the role of FMNL2 in spindle migration, polar body extrusion, and distribution of mitochondria and endoplasmic reticulum (ER) in mouse oocytes.

Strengths:<br /> Novelty in assessing the role of formin-like 2 in oocyte meiosis.

Weaknesses:<br /> Methods are not properly described.<br /> Overstating presented data.<br /> It is not clear what statistical tests were used.

My main concern is that there are missing important details of how particular experiments and analyses were done. The material and methods section is not written in the way that presented experiments could be repeated - it is missing basic information (e.g., used mouse strain, timepoints of oocytes harvest for particular experiments, used culture media, image acquisition parameters, etc.). Some of the presented data are overstated and incorrectly interpreted. It is not clear to me how the analysis of ER and mitochondria distribution was done, which is an important part of the presented data interpretation. I'm also missing important information about the timing of particular stages of assessed oocytes because the localization of both ER and mitochondria differs at different stages of oocyte meiosis. The data interpretation needs to be justified by proper analysis based on valid parameters, as there is considerable variability in the ER and mitochondria structure and localization across oocytes based on their overall quality and stage.

Reviewer #2 (Public Review):

Summary:<br /> This research involves conducting experiments to determine the role of Fmnl2 during oocyte meiosis I.

Strengths:<br /> Identifying the role of Fmnl2 during oocyte meiosis I is significant.

Weaknesses:<br /> The quantitative analysis and the used approach to perturb FMNL2 function are currently incomplete and would benefit from more confirmatory approaches and rigorous analysis.

1- Most of the results are expected. The new finding here is that FMNL2 regulates cytoplasmic F-actin in mouse oocytes, which is also expected given the role of FMNL2 in other cell types. Given that FMNL2 regulates cytoplasmic F-actin, it is very expected to see all the observed phenotypes. It is already established that F-actin is required for spindle migration to the oocyte cortex, extruding a small polar body and normal organelle distribution and functions.

2-The authors used Fmnl2 cRNA to rescue the effect of siRNA-mediated knockdown of Fmnl2. It is not clear how this works. It is expected that the siRNA will also target the exogenous cRNA construct (which should have the same sequence as endogenous Fmnl2) especially when both of them were injected at the same time. Is this construct mutated to be resistant to the siRNA?

3-The authors used only one approach to knockdown FMNL2 which is by siRNA. Using an additional approach to inhibit FMNL2 would be beneficial to confirm that the effect of siRNA-mediated knockdown of FMNL2 is specific.

Reviewer #3 (Public Review):

Summary:<br /> The authors focus on the role of formin-like protein 2 in the mouse oocyte, which could play an important role in actin filament dynamics. The cytoskeleton is known to influence a number of cellular processes from transcription to cytokinesis. The results show that downregulation of FMNL2 affects spindle migration with resulting abnormalities in cytokinesis in oocyte meiosis I.

Weaknesses:<br /> The overall description of methods and figures is overall dismissively poor. The description of the sample types and number of replicate experiments is impossible to interpret throughout, and the quantitative analysis methods are not adequately described. The number of data points presented is unconvincing and unlikely to support the conclusions. On the basis of the data presented, the conclusions appear to be preliminary, overstated, and therefore unconvincing.

Reviewer #1 (Public Review):

Summary:<br /> Fukuhara, Maenaka, and colleagues report a crystal structure of the canine distemper virus (CDV) attachment hemagglutinin protein globular domain. The structure shows a dimeric organization of the viral protein and describes the detailed amino-acid side chain interactions between the two protomers. The authors also use their best judgement to comment on predicted sites for the two cellular receptors - Nectin-4 and SLAM - and thus speculate on the CDV host tropism. A complementary AFM study suggests a breathing movement at the hemagglutinin dimer interface.

Strengths:<br /> The study of CDV and related Paramyxoviruses is significant for human/animal health and is very timely. The crystallographic data seem to be of good quality.

Weaknesses:<br /> While the recent CDV hemagglutinin cryo-EM structure is mentioned, it is not compared to the present crystal structure, and thus the context of the present study is poorly justified. Additionally, the results of the AFM experiment are not unexpected. Indeed, other paramyxoviral RBP/G proteins also show movement at the protomer interface.

Reviewer #2 (Public Review):

Summary:<br /> The authors solved the crystal structure of CDV H-protein head domain at 3,2 A resolution to better understand the detailed mechanism of membrane fusion triggering. The structure clearly showed that the orientation of the H monomers in the homodimer was similar to that of measles virus H and different from other paramyxoviruses. The authors used the available co-crystal strictures of the closely related measles virus H structures with the SLAM and Nectin4 receptors to map the receptor binding site on CDV H. The authors also confirmed which N-linked sites were glycosylated in the CDV H protein and showed that both wildtype and vaccine strains of CDV H have the same glycosylation pattern. The authors documented that the glycans cover a vast majority of the H surface while leaving the receptor binding site exposed, which may in part explain the long-term success of measles virus and CDV vaccines. Finally, the authors used HS-AFM to visualize the real-time dynamic characteristics of CDV-H under physiological conditions. This analysis indicated that homodimers may dissociate into monomers, which has implications for the model of fusion triggering.

The structural data and analysis were thorough and well-presented. However, the HS-AFM data, while very exciting, was not presented in a manner that could be easily grasped by readers of this manuscript. I have some suggestions for improvement.

1) The authors claim their structure is very similar to the recently published croy-EM structure of CDV H. Can the authors provide us with a quantitative assessment of this statement?

2) The results for the HS-AFM are difficult to follow and it is not clear how the authors came to their conclusions. Can the authors better explain this data and justify their conclusions based on it?

3) The fusion triggering model in Figure 8 is ambiguous as to when H-F interactions are occurring and when they may be disrupted. The authors should clarify this point in their model.

Reviewer #1 (Public Review):

In the manuscript, the authors tried to explore the molecular alterations of adipose tissue and skeletal muscle in PCOS by global proteomic and phosphorylation site analysis. In the study, the samples are valuable, while there are no repeats for MS and there are no functional studies for the indicted proteins, phosphorylation sites. The authors achieved their aims to some extent, but not enough.

Reviewer #2 (Public Review):

This study provides the proteomic and phosphoproteomics data for our understanding of the molecular alterations in adipose tissue and skeletal muscle from women with PCOS. This work is useful for understanding of the characteristics of PCOS, as it may provide potential targets and strategies for the future treatment of PCOS. While the manuscript presents interesting findings on omics and phenotypic research, the lack of in-depth mechanistic exploration limits its potential impact.

The study primarily presents findings from omics and phenotypic research, but fails to provide a thorough investigation into the underlying mechanisms driving the observed results. Without a thorough elucidation of the mechanistic underpinnings, the significance and novelty of the study are compromised.

Reviewer #1 (Public Review):

In this revised preprint the authors investigate whether a presumably allosteric P2RX7 activating compound that they previously discovered reduces fibrosis in a bleomycin mouse model. They chose this particular model as publicly available mRNA data indicate that the P2RX7 pathway is downregulated in idiopathic pulmonary fibrosis patients compared to control individuals. In their revised manuscript, the authors use three proxies of lung damage, Ashcroft score, collagen fibers, and CD140a+ cells, to assess lung damage following the administration of bleomycin. These metrics are significantly reduced on HEI3090 treatment. Additional data implicate specific immune cell infiltrates and cytokines, namely inflammatory macrophages and damped release of IL-17A, as potential mechanistic links between their compound and reduced fibrosis. Finally, the researchers transplant splenocytes from WT, NLRP3-KO, and IL-18-KO mice into animals lacking the P2RX7 receptor to specifically ascertain how the transplanted splenocytes, which are WT for P2RX7 receptor, respond to HEI3090 (a P2RX7 agonist). Based on these results, the authors conclude that HEI3090 enhanced IL-18 production through the P2RX7-NLRP3 inflammasome axis to dampen fibrosis.

These findings could be interesting to the field, as there are conflicting results as to whether NLRP3 activation contributes to fibrosis and if so, at what stage(s) (e.g., acute damage phase versus progression). The revised manuscript is more convincing in that three orthogonal metrics for lung damage were quantified. However, major weaknesses of the study still include inconsistent and small effect sizes of HEI3090 treatment versus either batch effects from transplanted splenocytes or the effects of different genetic backgrounds. Moreover, the fundamental assumption that HEI3090 acts specifically and functionally through the P2RX7 pathway in this model cannot be directly tested, as the authors now provide results indicating that P2RX7 knockout mice do not establish lung fibrosis on bleomycin treatment.

In order to provide clear evidence that HEI3090 functions through P2RX7, a different lung fibrosis model that does not require P2RX7 would be necessary. For example, in such a system the authors could demonstrate a lack of HEI3090-mediated therapeutic effect on P2RX7 knockout. Molecularly, additional evidence on specificity, such as thermal proteome profiling and direct biophysical binding experiments, would also enhance the authors' argument that the compound indeed binds P2RX7 directly and specifically. Since all small molecules have some degree of promiscuity, the absence of an additional P2RX7 modulator, or direct recombinant IL-18 administration (as suggested by another reviewer), is needed to orthogonally validate the functional importance of this pathway. Another way the authors could probe pathway specificity would involve co-administering α-IL-18 with HEI3090 in several key experiments (similar to Figure 4L).

Reviewer #2 (Public Review):

In the study by Hreich et al, the potency of P2RX7-specific positive modulator HEI3090, developed by the authors, for the treatment of Idiopathic pulmonary fibrosis (IPF) was investigated. Recently, the authors have shown that HEI3090 can protect against lung cancer by stimulating dendritic cell P2RX7, resulting in IL-18 production that stimulates IFN-γ production by T and NK cells (DOI: 10.1038/s41467-021-20912-2). Interestingly, HEI3090 increases IL-18 levels only in the presence of high eATP. Since the treatment options for IPF are limited, new therapeutic strategies and targets are needed. The authors first show that P2RX7/IL-18/IFNG axis is downregulated in patients with IPF. Next, they used a bleomycin-induced lung fibrosis mouse model to show that the use of a positive modulator of P2RX7 leads to the activation of the P2RX7/IL-18 axis in immune cells that limits lung fibrosis onset or progression. Mechanistically, treatment with HEI3090 enhanced IL-18-dependent IFN-γ production by lung T cells leading to a decreased production of IL-17 and TGFβ, major drivers of IPF. The major novelty is the use of the small molecule HEI3090 to stimulate the immune system to limit lung fibrosis progression by targeting the P2RX7, which could be potentially combined with current therapies available. Overall, the study was well performed and the manuscript is clear. However, there is need for more details on the description and interpretation of the adoptive transfer experiments, as well as the statistical analyses and number of replicate independent experiments.

Reviewer #1 (Public Review):

Summary:

In this manuscript, the authors observed that miR-199b-5p is elevated in osteoarthritis (OA) patients. They also found that overexpression of miR-199b-5p induced OA-like pathological changes in normal mice and inhibiting miR-199b-5p alleviated symptoms in knee OA mice. They concluded that miR-199b-5p is not only a potential micro-target for knee OA but also provides a potential strategy for the future identification of new molecular drugs.

Strengths:

The data are generated from both human patients and animal models.

Weaknesses:

The data presented in this manuscript is not solid enough to support their conclusions. There are several questions that need to be addressed to improve the quality of this study.

The following questions that need to be addressed to improve the quality of the study.

1. Exosomes were characterized by electron microscopy and western blot analysis (for CD9, 264 CD63, and CD81). However, figure S1 only showed two sample WB results and there is no positive and negative control as well as the confused not clear WB figure.

2. The sequencing of miRNAs in serum exosomes showed that 88 miRNAs were upregulated and 89 miRNAs were downregulated in KOA patients compared with the control group based on fold change > 1.5 and p < 0.05. Figure 2 legend did not clearly elucidate what those represent and why the authors chose those five miRNAs to further validate although they did mention it with several words in line 108 'based on the p-value and exosomal'.

3. In Figure 3 legend and methods, the authors did not mention how they performed the cell viability assay. What cell had been used? How long were they treated and all the details? Other figure legends have the same problem without detailed information.

4. The authors claimed that Gcnt2 and Fzd6 are two target genes of miR-199b-5p. However, there is no convincing evidence such as western blot to support their bioinformatics prediction.

5. To verify the binding site on 3'UTR of two potential targets, the authors designed a mouse sequence for luciferase assay, but not sure if it is the same when using a human sequence.

Reviewer #2 (Public Review):

Summary:

The authors identified miR-199b-5p as 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. Validates the binding of miR-199b-5p with Fzd6 and binding of miR-199b-5p with Gcnt2.

Weaknesses:

1. The authors may overinterpret their results. The current work shows the possible bindings between miR-199b-5p and Fzd6 as well as bindings between miR-199b-5p and Gcnt2. However, whether miR-199b-5p truly functions through Fzd6 and/or Gcnt2 requires genetic knockdown of Fzd6 and Gcnt2 in the presence of miR-199b-5p.<br /> 2. In vitro chondrocyte experiments were conducted in a 2D manner, which led to chondrocyte de-differentiation and thus may not represent the chondrocyte response to the treatments.<br /> 3. There is a lack of description for bioinformatic analysis.<br /> 4. There are several errors in figure labeling.

Reviewer #2 (Public Review):

Summary:

In this study, Christin Krause et al mapped the hepatic miRNA-transcriptome of type 2 diabetic obese subjects, and identified miR-182-5p and its target genes LRP6 as potential drivers of dysregulated glucose tolerance and fatty acid metabolism in obese T2-diabetics.

Strengths:

This study contains some interesting findings and is valuable for the understanding of the key regulatory role of miRNAs in the pathogenesis of T2D.

Weaknesses:

The authors didn't systemically investigate the function of miR-182 in T2DM or NAFLD.

Reviewer #1 (Public Review):

Summary:

This study demonstrated a novel exciting link between the conserved miRNA-target axis of miR-182-Lrp6 in liver metabolism which causatively contributes to type 2 diabetes and NAFLD in mice and, potentially, humans.

Strengths:

The direct interaction and inhibition of Lrp6 by miR-182 are convincingly shown. The effects of miR-182-5p on insulin sensitivity are also credible for the in vivo and in vitro gain-of-function experiments.

Weaknesses:

However, the DIO cohorts lack key assays for insulin sensitivity such as ITT or insulin-stimulated pAKT, as well as histological evidence to support their claims and strengthen the link between miR-182-5p and T2D or NAFLD. Besides, the lack of loss-of-function experiments limits its aptitude as a potential therapeutic target.

Reviewer #3 (Public Review):

Summary:

In this manuscript, Krause and colleagues identify miR-182 as diabetes-associated microRNA: miR-182 is increased in bariatric surgery patients with versus without T2D; miR-182 was the only microRNA associated with three metabolic traits; miR-182 levels were associated with increased body weight in mice under different dietary manipulations; overexpression in Hep-G2 led to a decrease in LRP6; and overexpression in HFD fed mice led to increased insulin and liver TG. The manuscript provides a potentially useful resource for microRNA expression in human livers, though the functional importance of miR-182 remains unclear.

Strengths:

The use of human tissues and good sample sizes is strong.

Weaknesses:

The study is primarily correlative; the in vivo overexpression is non-physiological; and the mechanisms by which miR-182 exerts its effects are not rigorously tested.

Reviewer #2 (Public Review):

Summary:<br /> 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 the 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:<br /> 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:<br /> The major weakness comes from the potential limitations in the measurements of surface expression of severely misfolded mutants. This point is discussed quite fairly in the paper, in statements like "the W107A variant already exhibits marginal surface immunostaining" and many others. It seems that only about 5% of the W107A makes it to the plasma membrane compared to wild-type (Figures 2 and 3). This might be a low starting point from which to accurately measure the effects of secondary mutations.

Still, the authors claim that measurements of W107A double mutants "still contain cellular subpopulations with surface immunostaining intensities that are well above or below that of the W107A single mutant, which suggests that this fluorescence signal is sensitive enough to detect subtle differences in the PME of these variants". I was not entirely convinced that this was true. Firstly, I think it would be important to test how much noise these measurements have and how much surface immunostaining the W107A mutant displays above the background of cells that do not express the protein at all. But more importantly, it is not clear if under this regimen surface expression still reports on stability/protein fitness. It is unknown if the W107A retains any function or folding at all. For example, it is possible that the low amount of surface protein represents misfolded receptors that escaped the ER quality control. The differential clustering of epistatic mutations (Fig. 6) provides some interesting insights as to the rules that dictate epistasis, but these too are dominated by the magnitude of destabilization caused by one of the mutations. In this case, the secondary mutations that had the most interesting epistasis were exceedingly destabilizing. With this in mind, it is hard to interpret the results that emerge regarding the epistatic interactions of W107A. Furthermore, the most significant positive epistasis is observed when W107A is combined with additional mutations that almost completely abolish surface expression. It is likely that either mutation destabilizes the protein beyond repair. Therefore, what we can learn from the fact that such mutations have positive epistasis is not clear to me. Based on this, I am not sure that another mutation that disrupts the tertiary folding more mildly would not yield different results.

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

Additionally, the study draws general conclusions from the characterization of only two mutations, W107A and V276T. At this point, it is hard to know if other mutations that perturb insertion or tertiary folding would behave similarly. This should be emphasized in the text.

Some statistical aspects of the study could be improved:

1. It would be nice to see the level of reproducibility of the biological replicates in a plot, such as scatter or similar, with correlation values that give a sense of the noise level of the measurements. This should be done before filtering out the inconsistent data.

2. The statements "Variants bearing mutations within the C- terminal region (ICL3-TMD6-ECL3-TMD7) fare consistently worse in the V276T background relative to WT (Fig. 4 B & E)." and "In contrast, mutations that are 210 better tolerated in the context of W107A mGnRHR are located 211 throughout the structure but are particularly abundant among residues 212 in the middle of the primary structure that form TMD4, ICL2, and ECL2 213 (Fig. 4 C & F)." are both hard to judge. Inspecting Figures 4B and C does not immediately show these trends, and importantly, a solid statistical test is missing here. In Figures 4E and F the locations of the different loops and TMs are not indicated on the structure, making these statements hard to judge.

3. The following statement lacks a statistical test: "Notably, these 98 variants are enriched with TMD variants (65% TMD) relative to the overall set of 251 variants (45% TMD)." Is this enrichment significant? Further in the same paragraph, the claim that "In contrast to the sparse epistasis that is generally observed between mutations within soluble proteins, these findings suggest a relatively large proportion of random mutations form epistatic interactions in the context of unstable mGnRHR variants". Needs to be backed by relevant data and statistics, or at least a reference.

Reviewer #1 (Public Review):

Summary:<br /> The paper carries out an impressive and exhaustive non-sense mutagenesis using deep mutational scanning (DMS) of the gonadotropin-releasing hormone receptor for the WT protein and two single point mutations that I) influence TM insertion (V267T) and ii) influence protein stability (W107A), and then measures the effect of these mutants on correct plasma membrane expression (PME).

Overall, most mutations decreased mGnRHR PME levels in all three backgrounds, indicating poor mutational tolerance under these conditions. The W107A variant wasn't really recoverable with low levels of plasma membrane localisation. For the V267T variant, most additional mutations were more deleterious than WT based on correct trafficking, indicating a synergistic effect. As one might expect, there was a higher degree of positive correlation between V267T/W107A mutants and other mutants located in TM regions, confirming that improper trafficking was a likely consequence of membrane protein co-translational folding. Nevertheless, context is important, as positive synergistic mutants in the V27T could be negative in the W107A background and vice versa. Taken together, this important study highlights the complexity of membrane protein folding in dissecting the mechanism-dependent impact of disease-causing mutations related to improper trafficking.

Strengths:<br /> This is a novel and exhaustive approach to dissecting how receptor mutations under different mutational backgrounds related to co-translational folding, could influence membrane protein trafficking.

Weaknesses:<br /> The premise for the study requires an in-depth understanding of how the single-point mutations analysed affect membrane protein folding, but the single-point mutants used seem to lack proper validation. Furthermore, plasma membrane expression has been used as a proxy for incorrect membrane protein folding, but this not necessarily be the case, as even correctly folded membrane proteins may not be trafficked correctly, at least, under heterologous expression conditions. In addition, mutations can affect trafficking and potential post-translational modifications, like glycosylation.

Reviewer #1 (Public Review):

The Eph receptor tyrosine kinase family plays a critical function in multiple physiological and pathophysiological processes. Hence, understating the regulation of these receptors is a highly important question. Through extensive experiments in cell lines and cultured neurons Chang et.al show that the signaling hub protein, MYCBP2 positively regulates the overall stability of a specific member of the family, EPHB2, and by that the cellular response to ephrinBs.<br /> Overall, this work sheds light on the divergent in the regulatory mechanisms of the Eph receptors family. Although the physiological importance of this new regularly mechanism in mammals awaits to be discovered, the authors provide genetic evidence using C.elegans that it is evolutionarily conserved.

Reviewer #2 (Public Review):

Members of the EphB family of tyrosine kinase receptors are involved in a multitude of diverse cellular functions, ranging from the control of axon growth to angiogenesis and synaptic plasticity. In order to provide these diverse functions, it is expected that these receptors interact in a cell-type specific manner with a diverse variety of downstream signalling molecules.

The authors have used proteomics approaches to characterise some of these molecules in further detail. This molecule, myc-binding protein 2 (MYCBP2) is also known as highwire, has been identified in the context of establishment of neural connectivity. Another molecule coming up on this screen was identified as FBXO45.

The authors use classical methods of co-IP to show a kinase-independent binding of MYCBP2 to EphB2. They further showed that FBXO45 within a ternary complex increased the stability of the EphB2/MYCBP2 complex.

To define the interacting domains, they used clearly designed swapping experiments to show that the extracellular and transmembrane domains are necessary and sufficient for the formation of the ternary complex.

Using a cellular contraction assay, the authors showed the necessity of MYCBP2 in mediating the cytoskeletal response of EphB2 forward signalling. Furthermore, they used the technically challenging stripe assay of alternating lanes of ephrinB-Fc and Fc to show that also in this migration-based essay MYCBP2 is required for EphB mediated differential migration pattern.

MYCBP2 in addition is necessary to stabilize EphB2, that is in the absence of MYCBP2, EphB2 is degraded in the lysosomal pathway.

Interestingly, the third protein in this complex, Fbxo45, was further characterized by overexpression of the domain of MYCBP2, known to interact with Fbxo45. Here the authors showed that this approach led to the disruption of the EphB2 / MYCBP2 complex, and also abolished the ephrinB mediated activation of EphB2 receptors and their differential outgrowth on ephrinB2-Fc / Fc stripes.

Finally, the authors demonstrated an in vivo function of this complex using another model system, C elegans where they were able to show a genetic interaction.

Data show in a nice set of experiments a novel level of EphB2 forward signalling where a ternary complex of this receptor with multifunctional MYCBP2 and Fbxo45 controls the activity of EphB2, allowing a further complex regulation of this important receptors. Additionally, the authors challenge pre-existing concepts of the function of MYCBP2 which might open up novel ways to think about this protein.<br /> Of interest is this work also in terms of development of the retinotectal projection in zebrafish where MYCBP2/highwire plays a crucial role, and thus might lead to a better understanding of patterning along the DV axis, for which it is known that EphB family members are crucial.

Overall, the experiments are classical experiments of co-immunoprecipitations, swapping experiments, collapse assays, and stripe assays which all are well carried out and are convincing.

Reviewer #3 (Public Review):

In this improved version of the manuscript, Chang et al set out to find direct interactions with the Eph-B2 receptor, as our knowledge of its function/regulation is still incomplete. Using proteomic analysis of Hela cells expressing EPHB2, they identified MYCBP2 a potential binder, which they then confirm using extensive biochemical analyses, an interaction that seems to be negatively affected by binding of ephrin-B2 (but not B1). Furthermore, they find that FBXO45, a known MYCBP2 interaction, strongly facilitates its binding to EPHB2. Intriguingly, these interactions depend on the extracellular domains of EPHB2, suggesting the involvement of additional proteins as MYCBP2 is thought to be a cytoplasmic protein. Finally, they find that, in contrast to what could be expected given the known function of MYCBP2 as a ubiquitin E3 ligase, it actually positively regulates EPHB2 protein stability, and function.

The strength of this manuscript is the extensive biochemical analysis of the EPHB2/MYCBP2/FBXO43 interactions. The vast majority of the conclusions are supported by the data.

The attempt to extend the study to an in vivo animal using the worm is important, however the additive insight is, unfortunately, minimal.

Reviewer #1 (Public Review):

The study presented in this manuscript presents very convincing evidence that purifying selection is the main force shaping the landscape of TE polymorphisms in B. distachyon, with only a few putatively adaptive variants detected, even though most conclusions are based on the 10% of polymorphisms contributed by retrotransposons. That first conclusion is not novel, however, as it had already been clearly established in natural A. thaliana strains (Baduel et al. Genome Biol 2021) and in experimental D. simulans lines (Langmüller et al. NAR 2023), two studies that the authors do not mention, or improperly mention. In contrast to the conclusions reached in A. thaliana, however, Horvath et al. report here a seemingly deleterious effect of TE insertions even very far away from genes (>5kb), a striking observation for a genome of relatively similar size. If confirmed, as a caveat of this study is the lack of benchmarking of the TE polymorphisms calls by a pipeline known for a high rate of false positives (see detailed Private Recommendations #1), this set of observations would make an important addition to the knowledge of TE dynamics in the wild and questioning our understanding of the main molecular mechanisms through which TEs can impact fitness.

Reviewer #2 (Public Review):

Summary:<br /> Transposable elements are known to have a strong potential to generate diversity and impact gene regulation, and they are thought to play an important role in plant adaptation to changing environments. Nevertheless, very few studies have performed genome-wide analyses to understand the global effect of selection on TEs in natural populations. Horvath et al. used available whole-genome re-sequencing data from a representative panel of B. distachyon accessions to detect TE insertion polymorphisms (TIPs) and estimate their time of origin. Using a thorough combination of population genomics approaches, the authors demonstrate that only a small amount of the TE polymorphisms are targeted by positive selection or potentially involved in adaptation. By comparing the age-adjusted population frequencies of TE polymorphisms and neutral SNPs, the authors found that retrotransposons are affected by purifying selection independently of their distance to genes. Finally, using forward simulations they were able to quantify the strength of selection acting on TE polymorphisms, finding that retrotransposons are mainly under moderate purifying selection, with only a minority of the insertions evolving neutrally.

Strengths:<br /> Horvath et al., use a convincing set of strategies, and their conclusions are well supported by the data. I think that incorporating polymorphism's age into the analysis of purifying selection is an interesting way to reduce the possible bias introduced by the fact that SNPs and TEs polymorphisms do not occur at the same pace. The fact that TE polymorphisms far from genes are also under purifying selection is an interesting result that reinforces the idea that the trans-regulatory effect of TE insertions might not be a rare phenomenon, a matter that may be demonstrated in future studies.

Weaknesses:<br /> TEs from different classes and orders strongly differ in multiple features such as size, the potential impact of close genes upon insertion, insertion/elimination ratio (ie, MITE/TIR excision, solo-LTR formation), or insertion preference. Given such diversity, it is expected that their survival rates on the genome and the strength of selection acting on them could be different. The authors differentiate DNA transposons and retrotransposons in some of the analyses, the specificities of the most abundant plant TE types (ie, LTR/Gypsy, LTR/Copia, MITE DNA transposons) are not considered.

The authors used a short-read-based approach to detect TIPs and TAPs. It is known that detecting TE polymorphisms is challenging and can lead to false negatives, depending on the method used and the sequencing coverage. The methodology used here (TEPID) has been previously applied to other species, but it is unclear if the sensitivity of the TIP/TAP caller is equivalent to that of the SNP caller and how these potential differences may affect the results.

Reviewer #1 (Public Review):

The regulation of motor autoinhibition and activation is essential for efficient intracellular transport. This manuscript used biochemical approaches to explore two members in the kinesin-3 family. They found that releasing UNC-104 autoinhibition triggered its dimerization whereas unlocking KLP-6 autoinhibition is insufficient to activate its processive movement, which suggests that KLP-6 requires additional factors for activation, highlighting the common and diverse mechanisms underlying motor activation. They also identified a coiled-coil domain crucial for the dimerization and processive movement of UNC-104. Overall, these biochemical and single-molecule assays were well performed, and their data support their statements. The manuscript is also clearly written, and these results will be valuable to the field.

Reviewer #2 (Public Review):

The Kinesin superfamily motors mediate the transport of a wide variety of cargos which are crucial for cells to develop into unique shapes and polarities. Kinesin-3 subfamily motors are among the most conserved and critical classes of kinesin motors which were shown to be self-inhibited in a monomeric state and dimerize to activate motility along microtubules. Recent studies have shown that different members of this family are uniquely activated by to undergo transition from monomers to dimers.

Niwa and colleagues study two well-described members of the kinesin-3 superfamily, unc104 and KLP6, to uncover the mechanism of monomer to dimer transition upon activation. Their studies reveal that although both Unc104 and KLP6 are both self-inhibited monomers, their propensities for forming dimers are quite different. The authors relate this difference to a region in the molecules called CC2 which has a higher propensity for forming homodimers. Unc104 readily forms homodimers if its self-inhibited state is disabled while KLP6 does not.

The work suggests that although mechanisms for self-inhibited monomeric states are similar, variations in the kinesin-3 dimerization may present a unique forms of kinesin-3 motor regulation with implications on the forms of motility functions carried out by these unique kinesin-3 motors.

Reviewer #3 (Public Review):

In this work, Kita et al., aim to understand the activation mechanisms of the kinesin-3 motors KLP-6 and UNC-104 from C. elegans. As many other motor proteins involved in intracellular transport processes, KLP-6 and UNC-104 motors suppress their ATPase activities in the absence of cargo molecules. Relieving the autoinhibition is thus a crucial step that initiates directional transport of intracellular cargo. To investigate the activation mechanisms, the authors make use of mass photometry to determine the oligomeric states of the full length KLP-6 and the truncated UNC-104(1-653) motors at sub-micromolar concentrations. While full length KLP-6 remains monomeric, the truncated UNC-104(1-653) displays a sub-population of dimeric motors that is much more pronounced at high concentrations, suggesting a monomer-to-dimer conversion. The authors push this equilibrium towards dimeric UNC-104(1-653) motors solely by introducing a point mutation into the coiled-coil domain and ultimately unleash a robust processivity of the UNC-104 dimer. The authors find that the same mechanistic concept does not apply to the KLP-6 kinesin-3 motor, suggesting an alternative activation mechanism of the KLP-6 that remains to be resolved. The present study encourages further dissection of the kinesin-3 motors with the goal of uncovering the main factors needed to overcome the 'self-inflicted' deactivation.

Reviewer #1 (Public Review):

The study examines how hemocytes control whole-body responses to oxidative stress. Using single cell sequencing they identify several transcriptionally distinct populations of hemocytes, including one subset that show altered immune and stress gene expression. They also find that knockdown of DNA Damage Response (DDR) genes in hemocytes increases expression of the immune cytokine, upd3, and that both upd3 overexpression in hemocytes and hemocyte knockdown of DDR genes leads to increased lethality upon oxidative stress. And they find that the PQ-induced lethality seen when the DDR is disrupted can be rescued in upd3 null background, suggesting links between proper regulation of DDR in hemocytes, modulation of systemic upd3 signaling, and the control of oxidative stress survival.

The paper has two key strengths:

1, The single cell analyses provide a clear description of how oxidative stress can cause distinct transcriptional changes in different populations of hemocytes. These results add to the emerging them in the field that there functionally different subpopulations of hemocytes that can control organismal responses to stress.<br /> 2, The discovery that DDR genes are required upon oxidative stress to modulate upd3 cytokine production and lethality provides interesting new insight into the DDR may play non-canonical roles in controlling organismal responses to stress.

Reviewer #2 (Public Review):

Hersperger et al. investigated the importance of Drosophila immune cells, called hemocytes, in the response to oxidative stress in adult flies. They found that hemocytes are essential in this response, and using state-of-the-art single-cell transcriptomics, they identified expression changes at the level of individual hemocytes. This allowed them to cluster hemocytes into subgroups with different responses, which certainly represents very valuable work. One of the clusters appears to respond directly to oxidative stress and shows a very specific expression response that could be related to the observed systemic metabolic changes and energy mobilization.

Using hemocyte-specific genetic manipulation, the authors convincingly show that the DNA damage response in hemocytes regulates JNK activity and subsequent expression of the JAK/STAT ligand Upd3. Silencing of the DNA damage response or excessive activation of JNK and Upd3 leads to increased susceptibility to oxidative stress. This nicely demonstrates the importance of tight control of JNK-Upd3 signaling in hemocytes during oxidative stress. The treatment the authors used is quite harsh, and in such a situation it is simply better not to use upd3 signaling, but it is still worth bearing in mind that upd3 signaling may have a protective role under milder stresses, but Upd3 could require very tight control - this could be an interesting objective for future studies.

The authors demonstrate that hemocytes play an important role in energy mobilization during oxidative stress, suggesting that control of energy mobilization by hemocytes is essential for the response. They further postulate that "hemocyte-derived upd3 is most likely released by the activated plasmatocyte cluster C6 during oxidative stress in vivo and is subsequently controlling energy mobilization and subsequent tissue wasting upon oxidative stress." It is important to note here that the association of upd3 with the observed changes in energy metabolism has not been tested, and the subsequent tissue wasting allegedly caused by excessive upd3 as a cause of death remains an open question.

Reviewer #3 (Public Review):

In this study, Kierdorf and colleagues investigated the function of hemocytes in oxidative stress response and found that non-canonical DNA damage response (DDR) is critical for controlling JNK activity and the expression of cytokine unpaired3. Hemocyte-mediated expression of upd3 and JNK determines the susceptibility to oxidative stress and systemic energy metabolism required for animal survival, suggesting a new role for hemocytes in the direct mediation of stress response and animal survival.

In the revised manuscript, the authors provide additional evidence to support the role of DNA damage-modulated cytokine release by hemocytes during oxidative stress responses and strengthen the connection between DNA damage and the regulation of upd3 release from hemocytes. The authors have also included new analyses to emphasize the significance of hemocytes in the regulation of energy during oxidative stress. Following the reviewers' suggestions, the authors made improvements to the manuscript and the graphical abstract to better display their findings. Overall, the revised manuscript makes it easier to understand the main points, flows better, and is supported by convincing data and analysis throughout.

Reviewer #1 (Public Review):

Summary:

This study is one of several around the world to investigate how urban wildlife responded to changes in human activity during the lockdowns associated with the COVID-19 pandemic. Unlike several other studies on the topic that used observational data from citizen science programs, this project relied on passive acoustic monitoring to record bird vocalizations during and after stringent lockdown periods in an urban environment. The authors focused on three species that differ in their level of adaptation to human presence, providing an ecologically relevant comparison that highlights the importance of micro-habitats for species living in close proximity to humans.

Strengths:

The element that sets this study apart from most others examining avian responses to COVID-19 lockdowns is the use of passive acoustic monitoring. As the authors describe, this method offers several advantages over other methods (though, it does come with some limitations on what questions can be addressed). Perhaps the most relevant advantage is that it offers the ability to concurrently measure anthropogenic noise in the environment, which is one of the most likely mechanisms for effects on wildlife from changes to human activity. These authors were, therefore, able to show local-scale differences in bird responses to human activity measured at the same scale. To my knowledge, only one other study (Derryberry et al. Science. 2020) has used recordings of vocalizations to examine the influence of COVID-19 lockdowns on a bird species.

It was encouraging to see a study that focused on the local-scale impacts of lockdowns, with methods that could investigate effects within micro-habitats. Logistics prevented many other projects from operating at such fine scales, making the results from this study particularly useful for the examination of rapid changes in bird behavior. This does mean that comparisons between this study and others examining the effects of COVID-19 lockdowns on birds should be done with care, as the effects described here may have been the result of different processes, operating at different spatial and temporal scales. However, that also means this study fills an important gap in our knowledge of how wildlife reacts to human activity in urban spaces.

Weaknesses:

One drawback of the approach is that the acoustic sampling only occurred during the pandemic: samples were taken during several lockdown periods in the early spring (March through early May) of 2020 and then for a period of 10 days after the end of the final lockdown period in late May of 2020. Unfortunately, this means that the interpretation of the effect of lockdowns could have been affected by any shifts in the birds' vocal behavior that resulted from unmodeled environmental factors or normal seasonal phenology during that three-month period. However, the authors chose focal species that would be less prone to seasonal changes in vocal behavior and their approach did account for several factors to minimize any such effects.

Reviewer #2 (Public Review):

In this study, the authors tried to gauge the effect of human activity on three species, (1) the Hooded grow, an urban exploiter, (2) the Rose ring parakeet, an invasive, alien species that has adapted to exploit human resources, and (3) the Graceful prinia, an urban adapter, which is relatively shy of humans. A goal of the study was to increase awareness of the importance of urban parks.

Strengths:<br /> Strengths of the study include the fact that it was conducted at 17 different sites, including parks, roads and residential areas, and included three species with different habitat preferences. Each species produced relatively loud and repeatable vocalizations. To avoid the effect of seasonal changes, sounds were sampled within a 10 day period of the lockdown as well as post-lockdown. The analysis included a comparison of the number of sound files, binary values indicating emission of a common syllable, and also the total number of syllables emitted as a measurement of bird activity. Ambient temperatures and sound levels of human activity were also recorded. All of these factors speak to the comprehensive approach and analysis adopted in this study. The results are based on a rigorous statistical analysis, ruling out the effects of various extraneous parameters.

Weaknesses:<br /> Most significant changes may occur near the ambient noise levels and this could lead to a different conclusion, but the authors authors acknowledge this possibility and clarify that they only analyzed vocalizations with high signal-to-noise signals to avoid ambiguity. In the revised version, they also replaced the previous ambient noise parameter with an estimate of ambient noise under 1kHz, assuming that it reflects most anthropogenic noise (not restricted to human speech). This seems reasonable and this new model gave very similar results to the previous one.

In interpreting the data, the authors mention the effect of human activity on bird vocalizations in the context of inter-species predator-prey interactions; however, the presence of humans could also modify intraspecies interactions by acting as triggers for communication of warning and alarm, and/or food calls (as may sometimes be the case) to conspecifics. The behavioral significance of the syllables used to monitor animal activity could be informative in this context; however, the authors acknowledge this possibility in the Discussion. Most importantly, the authors acknowledge the possibility of the above-noted bias, and the potential of a transient nature of the observed effects.

Conclusion:<br /> In general, the authors achieved their aim of illustrating the complexity of the affect of human activity on animal behavior notwithstanding the caveats noted above. Their study also makes it clear that estimating such affects is not simple given the dynamics of animal behavior. For example, seasonality, temperature changes, animal migration and movement, as well as interspecies interactions, such as those related to predator-prey behavior, and inter/intra-species competition in other respects can all play into site-specific changes in the vocal activity of a particular species.

Reviewer #1 (Public Review):

Summary:<br /> This important study nicely integrates a breadth of experimental and computational data to address fundamental aspects of RNA methylation by an important for biology and health RNA methyltransferases (MTases). 



Strengths:<br /> The authors offer compelling and strong evidence, based on carefully performed work with appropriate and well-established techniques to shed light on aspects of the methyl transfer mechanism of the methyltransferase-like protein 3 (METTL3), which is part of the methyltransferase-like proteins 3 & 14 (METTL3-14) complex. 


Weaknesses:<br /> 
The significance of this foundational work is somewhat diminished mostly due to mostly efficient communication of certain aspects of this work. Parts of the manuscript are somewhat uneven and don't quite mesh well with one another. The manuscript could be enhanced by careful revision and significant textual and figure edits. 

Examples of recommended edits that would improve clarity and allow accessibility to a broader audience are highlighted in some detail below.

Reviewer #2 (Public Review):

Summary:<br /> Caflisch and coworkers investigate the methyltransferase activity of the complex of methyltransferase-like proteins 3 and 14 (METTL3-14). To obtain a high-resolution description of the complete catalytic cycle they have carefully designed a combination of experiments and simulations. Starting from the identification of bisubstrate analogues (BAs) as binders to stabilise a putative transition state of the reaction, they have determined multiple crystal structures and validated relevant interactions by mutagenesis and enzymatic assays.

Using the resolved structure and classical MD simulations they obtained a kinetic picture of the binding and release of the substrates. Of note, they accumulated very good statistics on these processes using 16 simulation replicates over a time scale of 500 ns. To compare the time scale of the release of the products with that of the catalytic step they performed state-of-the-art QM/MM free energy calculations (testing multiple levels of theory) and obtained a free energy barrier that indicates how the release of the product is slower than the catalytic step.

Strengths:<br /> All the work proceeds through clear hypothesis testing based on a combination of literature and new results. Eventually, this allows them to present in Figure 10 a detailed step-by-step description of the catalytic cycle. The work is very well crafted and executed.

Weaknesses:<br /> To fulfill its potential of guiding similar studies for other systems as well as to allow researchers to dig into their vast work, the authors should share the results of their simulations (trajectories, key structures, input files, protocols, and analysis) using repositories like Zenodo, the plumed-nest, figshare or alike.

Reviewer #3 (Public Review):

Summary:<br /> The manuscript by Coberski et al describes a combined experimental and computational study aimed to shed light on the catalytic mechanism in a methyltransferase that transfers a methyl group from S-adenosylmethionine (SAM) to a substrate adenosine to form N6-methyladenosine (m6A).

Strengths:<br /> The authors determine crystal structures in complex with so-called bi-substrate analogs that can bridge across the SAM and adenosine binding sites and mimic a transition state or intermediate of the methyl-transfer reaction. The crystal structures suggest dynamical motions of the substrate(s) that are examined further using classical MD simulations. The authors then use QM/MM calculations to study the methyl-transfer process. Together with biochemical assays of ligand/substrate binding and enzyme turnover, the authors use this information to suggest what the key steps are in the catalytic cycle. The manuscript is in most places easy to read.

Weaknesses:<br /> My main suggestion for the authors is that they show better how their conclusions are supported by the data. This includes how the electron density maps for example support the key interactions and water molecules in the active site and a better error analysis of the computational analyses.

Reviewer #1 (Public Review):

The manuscript by Dr. Shinkai and colleagues is about the posttranslational modification of a highly important protein, MT3, also known as the growth inhibitory factor. Authors postulate that MT3, or generally all MT isoforms, are sulfane sulfur binding proteins. The presence of sulfane sulfur at each Cys residue has, according to the authors, a critical impact on redox protein properties and almost does not affect zinc binding. They show a model in which 20 Cys residues with sulfane sulfur atoms can still bind seven zinc ions in the same clusters as unmodified protein. They also show that recombinant MT3 (but also MT1 and MT2) protein can react with HPE-IAM, an efficient trapping reagent of persulfides/polysulfides. This reaction performed in a new approach (high temperature and high reagent concentration) resulted in the formation of bis-S-HPE-AM product, which was quantitatively analyzed using LC-MS/MS. This analysis indicated that all Cys residues of MT proteins are modified by sulfane sulfur atoms. The authors performed a series of experiments showing that such protein can bind zinc, which dissociates in the reaction with hydrogen peroxide or SNAP. They also show that oxidized MT3 is reduced by thioredoxin. It gives a story about a new redox-dependent switching mechanism of zinc/persulfide cluster involving the formation of cystine tetrasulfide bridge.

The whole story is hard to follow due to the lack of many essential explanations or full discussion. What needs to be clarified is the conclusion (or its lack) about MT3 modification proven by mass spectrometry. Figure 1B shows the FT-ICR-MALDI-TOF/MS spectrum of recombinant MT3. It clearly shows the presence of unmodified MT3 protein without zinc ions. Ions dissociate in acidic conditions used for MALDI sample preparation. If the protein contained all Cys residues modified, its molecular weight would be significantly higher. Then, they show the MS spectrum (low quality) of oxidized protein (Fig. 1C), in which new signals (besides reduced apo-MT3) are observed. They conclude that new signals come from protein oxidation and modification with one or two sulfur atoms. If the conclusion on Cys residue oxidation is reasonable, how this protein contains sulfur is unclear. What is the origin of the sulfur if apo-MT does not contain it? Oxidized protein was obtained by acidification of the protein, leading to zinc dissociation and subsequent neutralization and air oxidation. Authors should perform a detailed isotope analysis of the isotopic envelope to prove that sulfur is bound to the protein. They say that the +32 mass increase is not due to the appearance of two oxygen donors. They do not provide evidence. This protein is not a sulfane sulfur binding protein, or its minority is modified. Moreover, it is unacceptable to write that during MT3 oxidation are "released nine molecules of H2". How is hydrogen molecule produced? Moreover, zinc is not "released", it dissociates from protein in a chemical process.

Another important point is a new approach to the HPE-IAM application. Zinc-binding MT3 was incubated with 5 mM reagent at 60oC for 36 h. Authors claim that high concentration was required because apoMT3 has stable conformation. Figure 2B shows that product concentration increases with higher temperature, but it is unclear why such a high temperature was used. Figure 1D shows that at 37oC, there is almost no reaction at 5 mM reagent. Changing parameters sounds reasonable only when the reaction is monitored by mass spectrometry. In conclusion, about 20 sulfane sulfur atoms present in MT3 would be clearly visible. Such evidence was not provided. Increased temperature and reagent concentration could cause modification of cysteinyl thiol/thiolates as well, not only persulfides/polysulfides. Therefore, it is highly possible that non-modified MT3 protein could react with HPE-IAM, giving false results. Besides mass spectrometry, which would clearly prove modifications of 20 Cys, authors should use very important control, which could be chemically synthesized beta- or alfa-domain of MT3 reconstituted with zinc (many protocols are present in the literature). Such models are commonly used to test any kind of chemistry of MTs. If a non-modified chemically obtained domain would undergo a reaction with HPE-IAM under such rigorous conditions, then my expectation would be right.

- The remaining experiments provided in the manuscript can also be applied for non-modified protein (without sulfane sulfur modification) and do not provide worthwhile evidence. For instance, hydrogen peroxide or SNAP may interact with non-modified MTs. Zinc ions dissociate due to cysteine residue modification, and TCEP may reduce oxidized residue to rescue zinc binding. Again, mass spectrometry would provide nice evidence.

- The same is thioredoxin (Fig. 7) and its reaction with oxidized MT3. Nonmodified and oxidized MT3 would react as well.

- If HPE-IAM reacts with Cys residues with unmodified MT3, which is more likely the case under used conditions, the protein product of such reaction will not bind zinc. It could be an explanation of the cyanolysis experiment (Fig. 6).

- Figure 4 shows the reactivity of (pol)sulfides with TCEP and HPE-IAM. What are redox potentials? Do they correlate with the obtained results?

- Raman spectroscopy experiments would illustrate the presence of sulfane sulfur in MT3 only if all Cys were modified.

- The modeling presented in this study is very interesting and confirms the flexibility of metallothioneins. MT domains are known to bind various metal ions of different diameters. They adopt in this way to larger size the ions. The same mechanism could be present from the protein site. The presence of 9 or 11 sulfur atoms in the beta or alfa domain would increase the size of the domains without changing the cluster structure.

- Comment to authors. Apo-MT is not present in the cell. It exists as a partially metallated species. The term "apo-MT" was introduced to explain that MTs are not fully saturated by metals and function as a metal buffer system. Apo-MT comes from old ages when MT was considered to be present only in two forms: apo-form and fully saturated forms.

Reviewer #3 (Public Review):

Summary:<br /> The authors were trying to show that a novel neuronal metallothionein of poorly defined function, GIF/MT3, is actually heavily persulfidated in both the Zn-bound and apo (metal-free) forms of the molecule as purified from a heterologous or native host. Evidence in support of this conclusion is compelling, with both spectroscopic and mass spectrometry evidence strongly consistent with this general conclusion. The authors would appear to have achieved their aims.

Strengths:<br /> The analytical data are compelling in support of the author's primary conclusions are strong. The authors also provide some modeling evidence that strongly supports the contention that MT3 (and other MTs) can readily accommodate sulfane sulfur on each of the 20 cysteines in the Zn-bound structure, with little perturbation of the structure. This is not the case with Cys trisulfides, which suggests that the persulfide-metallated state is clearly positioned at lower energy relative to the immediately adjacent thiolate- or trisulfidated metal coordination complexes.

Weaknesses:<br /> The biological significance of the findings is not entirely clear. On the one hand, the analytical data are clearly solid (albeit using a protein derived from a bacterial over-expression experiment), and yes, it's true that sulfane S can protect Cys from overoxidation, but everything shown in the summary figure (Fig. 8D) can be done with Zn release from a thiol by ROS, and subsequent reduction by the Trx/TR system. In addition, it's long been known that Zn itself can protect Cys from oxidation. I view this as a minor weakness that will motivate follow-up studies. Fig. 1 was incomplete in its discussion and only suggests that a few S atoms may be covalently bound to MT3 as isolated. This is in contrast to the sulfate S "release" experiment, which I find quite compelling.

Impact:<br /> The impact will be high since the finding is potentially disruptive to the metals in the biology field in general and the MT field for sure. The sulfane sulfur counting experiment (the HPE-IAM electrophile trapping experiment) may well be widely adopted by the field. Those of us in the metals field always knew that this was a possibility, and it will interesting to see the extent to which metal-binding thiolates broadly incorporate sulfate sulfur into their first coordination shells.

Reviewer #2 (Public Review):

Summary:<br /> In this manuscript, the authors reveal that GIF/MT-3 regulates zinc homeostasis depending on the cellular redox status. The manuscript technically sounds, and their data concretely suggest that the recombinant MTs, not only GIF/MT-3 but also canonical MTs such as MT-1 and MT-2, contain sulfane sulfur atoms for the Zn-binding. The scenario proposed by the authors seems to be reasonable to explain the Zn homeostasis by the cellular redox balance.

Strengths:<br /> The data presented in the manuscript solidly reveal that recombinant GIF/MT-3 contains sulfane sulfur.

Weaknesses:<br /> It is still unclear whether native MTs, in particular, induced MTs in vivo contain sulfane sulfur or not.

Reviewer #3 (Public Review):

Summary:<br /> This manuscript describes some biochemical experiments on the crucial virulence factor EsxA (ESAT-6) of Mycobacterium tuberculosis. EsxA is secreted via the ESX-1 secretion system. Although this system is recognized to be crucial for virulence the actual mechanisms employed by the ESX-1 substrates are still mostly unknown. The EsxA substrate is attracting the most attention as the central player in virulence, especially phagosomal membrane disruption. EsxA is secreted as a dimer together with EsxB. The authors show that EsxA is also able to form homodimers and even tetramers, albeit at very low pH (below 5). Furthermore, the addition of a nanobody that specifically binds EsxA blocks intracellular survival, as well as if the nanobody is produced in the cytosol of the infected macrophages.

Strengths:<br /> -Decent biochemical characterization of EsxA and identification of a new and interesting tool to study the function of EsxA (nanobody).

-The manuscript is well-written.

Weaknesses:<br /> The findings are not critically evaluated using extra experiments or controls.

For instance, tetrameric EsxA in itself is interesting and could reveal how EsxA works. But one would say that this is a starting point to make small point mutations that specifically affect tetramer formation and then evaluate what the effect is on phagosomal membrane lysis. Also one would like to see experiments to indicate whether these structures can be produced under in vitro conditions, especially because it seems that this mainly happens when the pH is lower than 5, which is not normally happening in phagosomes that are loaded with M. tuberculosis.

Also, the fact that the addition of the nanobody, either directly to the bacteria or produced in the cytosol of macrophages is interesting, but again it is the starting point for further experimentation. As a control, one would like to see the effect on an Esx-1 secretion mutant. Furthermore, does cytosolic production or direct addition of the nanobody affect phagosomal escape? What happens if an EsxA mutant is produced that does not bind the nanobody?

Finally, it is a bit strange that the authors use a non-native version of esxA that has not only an additional His-tag but also an additional 12 amino acids, which makes the protein in total almost 20% bigger. Of course, these additions do not have to alter the characteristics, but they might. On the other hand, they easily discard the natural acetylation of EsxA by mycobacteria itself (proven for M. marinum) as not relevant for the function because it might not happen in (the close homologue) M. tuberculosis.

Reviewer #1 (Public Review):

Summary:<br /> The authors sought to establish a biochemical strategy to study ESAT-6 and CFP-10 biochemistry. They established recombinant reagents to study these protein associations in vitro revealing an unexpected relationship at low pH. They next develop much-needed reagents to study these proteins in an infection context and reveal that treatment with an ESAT-6 nanobody enhances Mtb control.

Strengths:<br /> The biochemical conclusions are supported by multiple configurations of the experiments. They combine multiple approaches to study a complex problem.

Weaknesses:<br /> It would be valuable to understand if the nanobody is disrupting the formation of the ESAT6-CFP10 complex. It is unclear how the nanobody is functioning to enhance control in the infection context. More detail or speculation in the discussion would have been valuable. Where is the nanobody in the cell during infection?

Reviewer #2 (Public Review):

Summary:<br /> Bates TA. et al. studied the biochemical characteristics of ESAT-6, a major virulence factor of Mycobacterium tuberculosis (Mtb), as part of the heterodimer with CFP10, a molecular chaperon of ESAT-6, as in homodimer and in homotetramer using recombinant ESAT-6 and CFP10 expressed in E. coli by applying several biochemical assays including Biolayer Interferometry (BLI) assay. The main findings show that ESAT-6 forms a tight interaction with CFP10 as a heterodimer at neutral pH, and ESAT-6 forms homodimer and even tetramer-based larger molecular aggregates at acidic pH. Although the discussion of the potential problems associated with the contamination of ESAT-6 preparations with ASB-14 during the LPS removal step is interesting, this research does not test the potential impact of residual ASB-14 contaminant on the biochemical behavior ESAT-6-CFP10 heterodimer and ESAT-6 homodimer or tetramer and their hemolytic activity in comparison with the ones without ASB-14. The main strength of this study is the generation of ESAT-6 specific nanobodies and the demonstration of its anti-tuberculosis efficiency in THP-1 cell lines infected with Mtb strains with reporter genes.

Strengths:<br /> Generation and demonstration of the anti-ESAT-6 nanobodies against tuberculosis infection in a cell line based Mtb infection model.

Weaknesses:<br /> Although the biochemistry studies provide quantitative data about the interactions of ESAT-6 with its molecular chaperon CFP10 and the interaction of ESAT-6 homodimer and tetramers, the novel information from these studies is minimal.

Reviewer #1 (Public Review):

Summary:

Exposure to cranial irradiation (IR) leads to cognitive deficits in the survivors of brain cancer. IR upregulates miR-206-3p, which in turn reduces the PAK3-LIMK1 axis leading to the loss of F and G-actin ratio and, thereby, mature dendritic spine loss. Silencing miR-206-3p reverses these degenerative consequences.

Strengths:<br /> The authors show compelling data indicating a clear correlation between PAK3 knockdown and the loss of mature dendritic spine density. In contrast, overexpression of PAK3 in the irradiated neurons restored mature spine types and recovered the F/G ratio. These in vitro results support the authors' hypotheses that PAK3 and LIMK1-mediated downstream signaling impact neuronal structure and reorganization in vitro. These data were supported by similar experiments using differentiated human neurons. Importantly, silencing miR-206-30 using antagonist miR also reverses IR-induced downregulation of the PAK3-LIMK1 axis, preventing spine loss and cognitive deficits.

Weaknesses:

All the miR-206-3p data are presented from in vitro cortical neurons or human stem cell-derived neuron cultures. This data (IR-induced elevation of miR-206-3p) should also be confirmed in vivo using an irradiated mouse brain to correlate the cognitive dysfunction timepoint.

Antago-miR-206-3p reversed Ir-induced upregulation of miR-206 (in vitro), and prevent reductions in PAK3 and downstream markers. Importantly, it reversed cognitive deficits induced by IR. This data should be supported by in vivo staining for important dendritic markers, including cofillin, p-cofilin, PSD-95, F- and G-actin within the hippocampal and PFC regions.

Other neuronal and non-neuronal targets of miR-206-3p should be discussed and looked into as a downstream impact of IR-induced functional and physiological impairments in the brain.

Reviewer #2 (Public Review):

Summary:<br /> The paper entitled "PAK3 downregulation induces cognitive 1 impairment following cranial irradiation" by Lee et al. aimed at investigating the functional impact of cranial irradiation in mouse and propose PAK3 as molecular element involved in radiation-induced cognitive decrement. The results provided in this paper are problematic as both the irradiation paradigm (5X2 Gy) as well as the timing of investigation (3 to 8 days post-IR) are completely irrelevant to investigate radiation induced neurocognitive impairment. This testifies to the team's lack of knowledge in radiobiology/radiotherapy and the methodology to explore radiation induced neurocognitive damages. It precludes any further relevance of the molecular results.

Weaknesses:

First and according to the BED equation a single dose of 10 Gy cannot not be approximated by 5 fractions of 2 Gy, as fractionation is known to decrease normal tissue toxicity. Note that in radiobiology/radio-oncology, the BED stands for "Biologically Effective Dose." This equation is used to compare the effects of different radiation treatments on biological tissues, taking into account the dose, fractionation, and the overall biological response of the tissue to radiation.<br /> The BED equation is commonly used to calculate the equivalent dose of a fractionated radiation treatment, which is the dose that would produce the same biological effect as a single, higher dose delivered in a single fraction.<br /> The general formula for BED is:BED = D * (1 + d / α/β)<br /> D is the total physical dose of radiation delivered in Grays (Gy)<br /> d is the dose per fraction in Gy<br /> α/β is the tissue-specific ratio of the linear (α) and quadratic (β) components of the radiation response. It is measured in Gy and describes how the tissue responds to different fractionation schedules (usually equal to 3 for the normal brain).<br /> Please refer to radiobiology/radiotherapy textbooks by Hall or Joiner.

Second, the brain is a late responding organ. GBM patients treated with 60 Gy exhibit progressive and debilitating impairments in memory, attention and executive function several month post-irradiation. In mice, neurocognitive decrements after a single dose of 10 Gy delivered to the whole brain does occur at late time point, usually > 2 months post-exposure. Multiple publications such as the one by Limoli C lab, Rossi S lab, Britten R lab or earlier Fike J lab and Robin M lab support this. Next, 5 fractions of 2 Gy will be more protective than a single dose of 10 Gy and neurocognitive decrements will require at least 5-6 months to occur if they ever occur. In Figure 1, the decrement reported is marginal, the number of animals included (4 to 5 at most?) The number of animals is not specified) is too low to draw any significant conclusions. In addition to the timing issue, the strategy described for NOR analysis shows methodological issues with the habituation period being too short and exploration level being very low.

Reviewer #1 (Public Review):

In this study, authors performed multiple sets of mesoscale chromatin simulations at nucleosome resolution to study the effects of TF binding on chromatin structures. Through simulations at various conditions, authors performed systemically analysis to investigate how linker histone, tail acetylation, and linker DNA length can operate together with TFs to regulate chromatin architecture. Using gene Eed as one example, authors found that binding of Myc:Max could repress the gene expression by increasing fiber folding and compaction and this repression can be reversed by the linker histone. Understanding how transcription factors bind to regulatory DNA elements and modulate chromatin structure and accessibility is an essential question in epigenetics. Through modelling of TF binding to chromatin structures at nucleosome levels, authors demonstrated that TF binding could create microdomains that are visible in the ensemble-based contact maps and short DNA linkers prevent the formation microdomains. It has also been shown that tail acetylation and TF binding have opposite effects on chromatin compaction and linker histone can compete for the linker DNA with TF binding to impair the effect of TF binding. This study improves our knowledge on how TFs collaborate with different epigenetic marks and chromatin features to regulate chromatin structure and accessibility, which will be of broad interest to the community.

For this reviewer, there were a few notable limitations. One was the implicit model of TF binding, which is modelled by adding harmonic restraints at two DNA beads. The model is very simple and it lacks kind of validation of how the results can be extended to many other TFs. In addition, the results of TF binding creating microdomains are very interesting but it requires further quantitative analysis of how microdomains was affected under different conditions. Also, some definitions and protocols demand further elucidation.

Reviewer #2 (Public Review):

Summary: In this paper, Portillo-Ledesma et al. study chromatin organization in the length scale of a gene, simulating the polymer at nucleosome resolution. The authors have presented an extensive simulation study with an excellent model of chromatin. The model has linker DNA and nucleosomes with all relevant interactions (electrostatics, tails, etc). Authors simulate 10 to 26 kb chromatin with varying linker lengths, linker histones (LH), and acetylated tails. The authors then study the effect of a transcription factor (TF) Myc: Max binding. The critical physical feature of the TF in the model is that it binds to the linker region and bends the DNA to make loops/intra-chromatin contacts. Authors systematically investigate the interplay between different variables such as linker DNA length, LH density, and the TF concentration in determining chromatin compaction and 3D organization.

Strengths: The manuscript is well-written and is a relevant study with many useful results. The biggest strength of the work is the fact that the authors start with a relevant model that incorporates well-known biophysical properties of DNA, nucleosomes, linker histones, and the transcription factor Myc:Max. One of the novel results is the demonstration of how linker lengths play an important role in chromatin compaction (measured by computing packing ratio) in the presence of DNA-bending TFs. As the TF concentration increases, chromatin with short linker lengths does not compact much (only a small change in packing ratio). If the linker lengths are long, a higher percentage of TFs leads to an increase in packing ratio (higher compaction). Authors further show that TFs are able to compact Life-like chromatin fiber with linker length taken from a realistic distribution. The authors compute inter-nucleosomal contact maps from their simulated configurations and show that the map has features similar to what is observed in Hi-C/Micro-C experiments. Authors study the compaction of the Eed gene locus and show that TF binding leads to the formation of small domains known as micro-domains. Authors have predicted many relevant and testable quantities. Many of the results agree with known experiments like the formation of the micro-domains. Hence, the conclusions made in this study are justified - they follow from the simulation results.

Weaknesses: (1) While this has the advantage of a minimal model (model with minimal factors incorporated), it is a disadvantage for predicting in vivo organization; one might need to incorporate the action of many other proteins (for example, PRC, HP1, etc) and several other histone modifications to predict in vivo organization. (2) While this forward model produces features of relevant contact maps, one would need to tune some of the intra-chromatin interaction parameters to obtain an accurate contact map and radius of gyration.

Reviewer #1 (Public Review):

Summary:

This revised study follows up on previous work showing a female-specific enhancer region of PAX1 is associated with adolescent idiopathic scoliosis (AIS). This new analysis combines human GWAS analysis from multiple countries to identify a new AIS-associated coding variant in the COL11A1 gene (COL11A1P1335L). Using a Pax1 knockout mouse they go on to find that PAX1 and Collagen XI protein are expressed in the intervertebral discs (IVDs) and robustly in the growth plate, showing that COL11A1 expression is reduced in Pax1 mutant growth plate. Moreover, other AIS-associated genes, Gpr126 and Sox6, were also reduced in Pax1 mutant mice, suggesting a common pathway is involved in AIS.

Using SV40 immortalized costal cartilage cells, derived from floxed Col11a1 mice primary rib cage cartilage, they go to show that removal of Col11a1 leads to reduction of Mmp3 expression. In this context, the expression of wild-type Col11a1 restored regular levels of Mmp3 expression, while expression of the AIS-associated Col11a1P1335L allele failed to restore normal Mmp3 expression. This supports a model that the AIS-associated Col11a1P1335L allele leads to the dysregulation of ECM in vivo.

Using this culture system, they go on to test the role of the estrogen receptor ESR2, showing that loss of this receptor leads to reduced Mmp3 and Pax1 expression, and increased Col11a1 expression. They support this by showing similar gene expression changes and estrogen receptor function in Rat cartilage endplate cell culture.

Altogether, this study nicely brings together an impressive number of human genetic data from multi-ethnic AIS cohorts and controls from across the globe and functionally tests these findings in cell culture and animal models. This study wonderfully integrates other findings from other human and mouse work in AIS and supports a new molecular mechanism by which estrogen can interact and synergize with COL11A1/PAX1/MMP3 signaling to change ECM development and dynamics, thus providing a tangible model for mutations and dysregulation of this pathway can increase the susceptibility of scoliosis.

Strengths:

This work integrates a large cohort of human genetic data from AIS patient and control from diverse ethnic backgrounds, across the globe. This work attempts to functionally test their findings in vivio and by use of cell culture.

Weaknesses:

Many of the main functional work was done in cell culture and not in vivo.

Reviewer #2 (Public Review):

Summary:

In this manuscript, Yu and colleagues sought to identify new susceptibility genes for adolescent idiopathic scoliosis (AIS). Significance for this work is high, especially given the still large knowledge gap of the mechanistic underpinnings for AIS. In this multidisciplinary body of work, the authors first performed a genetic association study of AIS case-control cohorts (combined 9,161 cases and 80,731 controls) which leveraged common SNPs in 1027 previously defined matrisome genes. Two nonsynonymous variants were found to be significantly associated with AIS: MMP14 p.Asp273Asn and COL11A1 p.Pro1153Leu, the latter of which had the more robust association and remained significant when females were tested independent of males. Next, the authors followed a series of functional validation experiments to support biological involvement of COL11A1 p.Pro1153Leu in AIS through expression, biochemical, and histological studies in physiologically relevant cell and mouse models. Together, the authors propose a hitherto unreported model for AIS that involves the interplay of the COL11A1 susceptibility locus with estrogen signaling to alter a Pax1-Col11a1-Mmp3 signaling axis at the growth plate.

Strengths:

The manuscript is clearly written and follows a series of logical steps toward connecting multiple matrisome genes and putative AIS effectors in a new framework of pathomechanism. The multidisciplinary nature of the work makes it a strong body of work wherein multiple models offer multiple lines of supportive data.

Weaknesses:

This manuscript remains an important multidisciplinary study of the genetic and functional basis of adolescent idiopathic scoliosis (AIS). To the benefit of the overall manuscript quality, the reviewers have addressed most concerns to satisfaction. I have a few remaining suggestions:

1. Regarding the genetic association of the common COL11A1 variant rs3753841, p.Pro1335Leu, please soften this statement to indicate that the variant could be a "risk locus" rather than "causal" in the following sentence on page 7-8: "These observations suggested that rs3753841 itself could be causal, although our methods would not detect deep intronic variants that could contribute to the overall association signal."

2. Include the list of three rare missense variants mentioned in the response to reviewers as a supplementary table. Please also include methods for the SKATO rare variant burden analysis.

3. Thank you for addressing the question of whether p.Pro1335Leu is a loss of function, gain of function, or dominant negative variant. The rationale in the response to reviewers was helpful, so please include this line of reasoning, and that there remains uncertainty, in the Discussion of the main text of the manuscript.

Reviewer #3 (Public Review):

Summary:

This article demonstrates a Pax1-Col11a1-Mmp3 signaling axis associated with adolescent idiopathic scoliosis and finds that estrogen affects this signaling axis. In addition, the authors have identified a new COL11A1 mutation and verified its effect on the Pax1-Col11a1-Mmp3 axis.

Strengths:

1. Col11a1P1335L is verified in multicenter cohorts with high confidence.

2. The article identified a potential pathogenesis of AIS.

Weaknesses:

The SV40-immortalized cell line established from Col11a1fl/fl mouse rib cartilage was applied in the study, and overexpression system was used to confirm that P1335L variant in COL11A1 perturbs its regulation of MMP3. However, due to the absence of P1335L point mutant mice, it cannot be confirmed whether P1335L can actually cause AIS, and the pathogenicity of this mutation cannot be directly verified.

Reviewer #1 (Public Review):

Summary:<br /> The study's abstract, introduction, and conclusions are not supported by the methods and results conducted. In fact, the results presented suggest that Arabidopsis could easily adapt to an extremely high CO2 environment.

This study offers good evidence pointing to a genetic basis for Arabidopsis thaliana's response to elevated CO2 (eCO2) levels and its subsequent impact on the leaf ionome. The natural variation analyses in the study support the hypothesis that genetic factors, rather than local adaptation, guide the influence of eCO2 on the ionome of rosette leaves in Arabidopsis. However, the manuscript's claim regarding its role in "the development of biofortified crops adapted to a high-CO2 world" (line 23) is overstated, especially given the absence of any analysis on the influence of eCO2 on the seed ionome and Arabidopsis is a poor model for harvest index for any crop. The manuscript, in its current form, necessitates massive revisions, particularly in clarifying its broader implications and in providing more substantial evidence for some of its assertions.

Major Drawbacks and Questions:

1. Evidence for the Central Premise:<br /> The foundational premise of the study is the assertion that rising atmospheric CO2 levels result in a decline in plant mineral content. This phenomenon is primarily observed in C3 plants, with C4 plants seemingly less affected. The evidence provided on this topic is scant and, in some instances, contradicts the authors' own references. The potential reduction of certain minerals, especially in grains, can be debated. For instance, reduced nitrogen (N) and phosphorus (P) content in grains might not necessarily be detrimental for human and animal consumption. In fact, it could potentially mitigate issues like nitrogen emissions and phosphorus leaching. Labeling this as a "major threat to food security" (line 30) is exaggerated. While the case for microelements might be more compelling, the introduction fails to articulate this adequately. Furthermore, the introduction lacks any discussion on how eCO2 might influence nutrient allocation to grains, which would be crucial in substantiating the claim that eCO2 poses a threat to food security. A more comprehensive introduction that clearly delineates the adverse effects of eCO2 and its implications for food security would greatly enhance the manuscript.

2. Exaggerated Concerns:<br /> The paper begins with the concern that carbon fertilization will lead to carbon dilution in our foods. While we indeed face numerous genuine threats in the coming decades, this particular issue is manageable. The increase in CO2 alone offers many opportunities for boosting yield. However, the heightened heat and increased evapotranspiration will pose massive challenges in many environments.

Figure 4 in fact suggests that 43% of the REGMAP panel (cluster 3) is already pre-adapted to very high CO2 levels. This suggests annual species could adapt very rapidly.

3. Assumptions on CO2 Levels:<br /> The assumption of 900ppm seems to be based on a very extreme climate change scenario. Most people believe we will overshoot the 1.5{degree sign}C scenario, however, it seems plausible that 2.5 to 3{degree sign}C scenarios are more likely. This would correspond to around 500ppm of CO2. https://www.nature.com/articles/s41597-022-01196-7/tables/4

4. Focus on Real Challenges:<br /> We have numerous real challenges, such as extreme heat and inconsistent rainfall, to address in the context of climate change. However, testing under extreme CO2 conditions and then asserting that carbon dilution will negatively impact nutrition is exaggerated.

In contrast, the FACE experiments are fundamental and are conducted at more realistic eCO2 levels. Understanding the interaction between a 20% increase in CO2 and new precipitation patterns is key for global carbon flux prediction.

As I look at the literature on commercial greenhouse tomato production, 1000ppm of eCO2 is common, but it also looks like the breeders and growers have already solved for flavor and nutrition under these conditions.

Conclusion:<br /> While the study provides valuable insights into the genetic underpinnings of Arabidopsis thaliana's response to elevated CO2 levels, it requires an entirely revised writeup, especially in its abstract, broader claims and implications. The manuscript would benefit from a more thorough introduction, a clearer definition of its scope, and a clear focus on the limits of this study.

Reviewer #2 (Public Review):

Strengths:<br /> The authors have conducted a large, well-designed experiment to test the response to eCO2. Overall, the experimental design is sound and appropriate for the questions about how a change in CO2 affects the ionome of Arabidopsis. Most of the conclusions in this area are well supported by the data that the authors present.

Weakness:<br /> While the authors have done good experiments, it is a big stretch from Arabidopsis grown in an arbitrary concentration of CO2 to relevance to human and animal nutrition in future climates. Arabidopsis is a great model plant, but its leaves are not generally eaten by humans or animals.

The authors don't justify their choice of a CO2 concentration. Given the importance of the parameter for the experiment, the rationale for selecting 900 ppm as elevated CO2 compared to any other concentration should be addressed. And CO2 is just one of the variables that plants will have to contend with in future climates, other variables will also affect elemental concentrations.

Given these concerns, I think the emphasis on biofortification for future climates is unwarranted for this study.

Additionally, I have trouble with these conclusions:

-Abstract "Finally, we demonstrate that manipulating the function of one of these genes can mitigate the negative effect of elevated CO2 on the plant mineral composition. "<br /> -Discussion "Consistent with these results, we show that manipulating TIP2;2 expressions with a knock-out mutant can modulate the Zn loss observed under high CO2."

The authors have not included the data to support this conclusion as stated. They have shown that this mutant increases the Zn content of the leaves when compared to WT but have not demonstrated that this response is different than in ambient CO2. This is an important distinction: one way to ameliorate the reduction of nutrients due to eCO2 is to try to identify genes that are involved in the mechanism of eCO2-induced reduction. Another way is to increase the concentration of nutrients so that the eCO2-induced reduction is not as important (i.e. a 10% reduction in Zn due to eCO2 is not as important if you have increased the baseline Zn concentration by 20%). The authors identified tip2 as a target from the GWAS on difference, but their validation experiment only looks at eCO2.

Reviewer #1 (Public Review):

Peng et al develop a computational method to predict/rank transcription factors (TFs) according to their likelihood of being pioneer transcription factors--factors that are capable of binding nucleosomes--using ChIP-seq for 225 human transcription factors, MNase-seq and DNase-seq data from five cell lines. The authors developed relatively straightforward, easy to interpret computational methods that leverage the potential for MNase-seq to enable relatively precise identification of the nucleosome dyad. Using an established smoothing approach and local peak identification methods to estimate positions together with identification of ChIP-seq peaks and motifs within those peaks which they referred to as "ChIP-seq motifs", they were able to quantify "motif profiles" and their density in nucleosome regions (NRs) and nucleosome depleted regions (NDRs) relative to their estimated nucleosome dyad positions. Using these profiles, they arrived at an odd-ratio based motif enrichment score along with a Fisher's exact test to assess the odds and significance that a given transcription factor's ChIP-seq motifs are enriched in NRs compared to NDRs, hence, its potential to be a pioneer transcription factor. They showed that known pioneer transcription factors had among the highest enrichment scores, and they could identify a number of relatively novel pioneer TFs with high enrichment scores and relatively high expression in their corresponding cell line. They used multiple validation approaches including (1) calculating the ROC-AUC and Matthews correlation coefficient (MCC) and generating ROC and precision-recall curves associated with their enrichment score based on 32 known pioneer TFs among their 225 TFs which they used as positives and the remaining TFs (among the 225) as negatives; (2) use of the literature to note that known pioneer TFs that acted as key regulators of embryonic stem cell differentiation had a highest enrichment scores; (3) comparison of their enrichment scores to three classes of TFs defined by protein microarray and electromobility shift assays (1. strong binder to free and nucleosomal DNA, 2. weak binder to free and nucleosomal DNA, 3. strong binding to free but not nucleosomal DNA); and (4) correlation between their calculated TF motif nucleosome end/dyad binding ratio and relevant data from an NCAP-SELEX experiment. They also characterize the spatial distribution of TF motif binding relative to the dyad by (1) correlating TF motif density and nucleosome occupancy and (2) clustering TF motif binding profiles relative to their distance from the dyad and identifying 6 clusters.

The strengths of this paper are the use of MNase-seq data to define relatively precise dyad positions and ChIP-seq data together with motif analysis to arrive at relatively accurate TF binding profiles relative to dyad positions in NRs as well as in NDRs. This allowed them to use a relatively simple odds ratio based enrichment score which performs well in identifying known pioneer TFs. Moreover, their validation approaches either produced highly significant or reasonable, trending results.

The weaknesses of the paper are relatively minor, and the authors do a good job describing the limitations of the data and approach.

Reviewer #2 (Public Review):

In this study, the authors utilize a compendium of public genomic data to identify transcription factors (TF) that can identify their DNA binding motifs in the presence of nuclosome-wrapped chromatin and convert the chromatin to open chromatin. This class of TFs are termed Pioneer TFs (PTFs). A major strength of the study is the concept, whose premise is that motifs bound by PTFs (assessed by ChIP-seq for the respective TFs) should be present in both "closed" nucleosome wrapped DNA regions (measured by MNase-seq) as well as open regions (measured by DNAseI-seq) because the PTFs are able to open the chromatin. Use of multiple ENCODE cell lines, including the H1 stem cell line, enabled the authors to assess if binding at motifs changes from closed to open. Typical, non-PTF TFs are expected to only bind motifs in open chromatin regions (measured by DNaseI-seq) and not in regions closed in any cell type. This study contributes to the field a validation of PTFs that are already known to have pioneering activity and presents an interesting approach to quantify PTF activity.

For this reviewer, there were a few notable limitations. One was the uncertainty regarding whether expression of the respective TFs across cell types was taken into account. This would help inform if a TF would be able to open chromatin. Another limitation was the cell types used. While understandable that these cell types were used, because of their deep epigenetic phenotyping and public availability, they are mostly transformed and do not bear close similarity to lineages in a healthy organism. Next, the methods used to identify PTFs were not made available in an easy-to-use tool for other researchers who may seek to identify PTFs in their cell type(s) of interest. Lastly, some terms used were not define explicitly (e.g., meaning of dyads) and the language in the manuscript was often difficult to follow and contained improper English grammar.

Reviewer #3 (Public Review):

Peng et al. designed a computational framework for identifying pioneer factors using epigenomic data from five cell types. The identification of pioneer factors is important for our understanding of the epigenetic and transcriptional regulation of cells. A computational approach toward this goal can significantly reduce the burden of labor-intensive experimental validation.

The authors have addressed my previous comments.

The main issue identified in this re-review is based on the authors' additional experiments to investigate the reproducibility of the pioneer factors identified in the previously analysis that anchored on H1 ESCs.

The additional analysis that uses the other four cell types (HepG2, HeLa-S3, MCF-7, and K562) as anchors reveals the low reproducibility/concordance and high dependence on the selection of anchor cell type in the computational framework. In particular, now several stem cell related TFs (e.g. ESRRB, POU5F1) are ranked markedly higher when H1 ESC is not used as the anchor cell type as shown in Supplementary Figure 5.

Of note, the authors have now removed the shape labels that denote Yamanaka factors in Figure 2c (revised manuscript) that was presented in the main Figure 2a in the initial submission. The NFYs and ESRRB labels in Supplementary 4a are also removed and the boxplot comparing NFYs and ESRRB with other TF are also removed in this figure. Removing these results effectively hides the issues of the computational framework we identified in this revision. Please justify why this was done.

In summary, these new results reveal significant limitations of the proposed computational framework for identifying pioneer factors. The current identifications appear to be highly dependent on the choice of cell types.

Reviewer #2 (Public Review):

Summary:

In this article, the authors employed modified CRISPR screens ["guide-only (GO)-CRISPR"] in the attempt to identify the genes which may mediate cancer cell dormancy in the high grade serous ovarian cancer (HGSOC) spheroid culture models. Using this approach, they observed that abrogation of several of the components of the netrin (e.g., DCC, UNC5Hs) and MAPK pathways compromise the survival of non-proliferative ovarian cancer cells. This strategy was complemented by the RNAseq approach which revealed that a number of the components of the netrin pathway are upregulated in non-proliferative ovarian cancer cells and that their overexpression is lost upon disruption of DYRK1A kinase that has been previously demonstrated to play a major role in survival of these cells. Perampalam et al. then employed a battery of cell biology approaches to support the model whereby the Netrin signaling governs the MEK-ERK axis to support survival of non-proliferative ovarian cancer cells. Moreover, the authors show that overexpression of Netrins 1 and 3 bolsters dissemination of ovarian cancer cells in the xenograft mouse model, while also providing evidence that high levels of the aforementioned factors are associated with poor prognosis of HGSOC patients.

Strengths:

Overall it was thought that this study is of potentially broad interest inasmuch as it provides previously unappreciated insights into the potential molecular underpinnings of cancer cell dormancy, which has been associated with therapy resistance, disease dissemination, and relapse as well as poor prognosis. Notwithstanding the potential limitations of cellular models in mimicking cancer cell dormancy, it was thought that the authors provided sufficient support for their model that netrin signaling drives survival of non-proliferating ovarian cancer cells and their dissemination. Collectively, it was thought that these findings hold a promise to significantly contribute to the understanding of the molecular mechanisms of cancer cell dormancy and in the long term may provide a molecular basis to address this emerging major issue in the clinical practice.

Weaknesses:

Several issues were observed regarding methodology and data interpretation. The major concerns were related to the reliability of modelling cancer cell dormancy. To this end, it was relatively hard to appreciate how the employed spheroid model allows to distinguish between dormant and e.g., quiescent or even senescent cells. This was in contrast to solid evidence that netrin signaling stimulates abdominal dissemination of ovarian cancer cells in the mouse xenograft and their survival in organoid culture. Moreover, the role of ERK in mediating the effects of netrin signaling in the context of the survival of non-proliferative ovarian cancer cells was found to be somewhat underdeveloped.

Reviewer #1 (Public Review):

Summary:

Perampalam et al. describe novel methods for genome-wide CRISPR screening to identify and validate genes essential for HGSOC spheroid viability. In this study, they report that Netrin signaling is essential for maintaining disseminated cancer spheroid survival, wherein overexpression of Netrin pathway genes increases tumor burden in a xenograft model of ovarian cancer. They also show that high netrin expression correlates with poor survival outcomes in ovarian cancer patients. The study provides insights into the biology of netrin signaling in DTC cluster survival and warrants development of therapies to block netrin signaling for treating serous ovarian cancer.

Strengths:

- The study identifies Netrin signaling to be important in disseminated cancer spheroid survival<br /> - A Novel GO-CRISPR methodology was used to find key genes and pathways essential for disseminated cancer cell survival

Weaknesses:

- The term dormancy is not fully validated and requires additional confirmation to claim the importance of Netrin signaling in "dormant" cancer survival.<br /> - Findings shown in the study largely relate to cancer dissemination and DTS survival rather than cancer dormancy.

Reviewer #3 (Public Review):

Summary:

In this study, Warfvinge and colleagues use CITE-seq to interrogate how CML stem cells change between diagnosis and after one year of TKI therapy. This provides important insight into why some CML patients are "optimal responders" to TKI therapy while others experience treatment failure. CITE-seq in CML patients revealed several important findings. First, substantial cellular heterogeneity was observed at diagnosis, suggesting that this is a hallmark of CML. Further, patients who experienced treatment failure demonstrated increased numbers of primitive cells at diagnosis compared to optimal responders. This finding was validated in a bulk gene expression dataset from 59 CML patients, in which it was shown that the proportion of primitive cells versus lineage-primed cells correlates to treatment outcome. Even more importantly, because CITE-seq quantifies cell surface protein in addition to gene expression data, the authors were able to identify that BCR/ABL+ and BCR/ABL- CML stem cells express distinct cell surface markers (CD26+/CD35- and CD26-/CD35+, respectively). In optimal responders, BCR/ABL- CD26-/CD35+ CML stem cells were predominant, while the opposite was true in patients with treatment failure. Together, these findings represent a critical step forward for the CML field and may allow more informed development of CML therapies, as well as the ability to predict patient outcomes prior to treatment.

Strengths:

This is an important, beautifully written, well-referenced study that represents a fundamental advance in the CML field. The data are clean and compelling, demonstrating convincingly that optimal responders and patients with treatment failure display significant differences in the proportion of primitive cells at diagnosis, and the ratio of BCR-ABL+ versus negative LSCs. The finding that BCR/ABL+ versus negative LSCs display distinct surface markers is also key and will allow for a more detailed interrogation of these cell populations at a molecular level.

Weaknesses:

CITE-seq was performed in only 9 CML patient samples and 2 healthy donors. Additional samples would greatly strengthen the very interesting and notable findings.

Reviewer #1 (Public Review):

Summary:

This manuscript by Warfvinge et al. reports the results of CITE-seq to generate single-cell multi-omics maps from BM CD34+ and CD34+CD38- cells from nine CML patients at diagnosis. Patients were retrospectively stratified by molecular response after 12 months of TKI therapy using European Leukemia Net (ELN) recommendations. They demonstrate heterogeneity of stem and progenitor cell composition at diagnosis, and show that compared to optimal responders, patients with treatment failure after 12 months of therapy demonstrate increased frequency of molecularly defined primitive cells at diagnosis. These results were validated by deconvolution of an independent previously published dataset of bulk transcriptomes from 59 CML patients. They further applied a BCR-ABL-associated gene signature to classify primitive Lin-CD34+CD38- stem cells as BCR:ABL+ and BCR:ABL-. They identified variability in the ratio of leukemic to non-leukemic primitive cells between patients, showed differences in the expression of cell surface markers, and determined that a combination of CD26 and CD35 cell surface markers could be used to prospectively isolate the two populations. The relative proportion of CD26-CD35+ (BCR:ABL-) primitive stem cells was higher in optimal responders compared to treatment failures, both at diagnosis and following 3 months of TKI therapy.

Strengths:

The studies are carefully conducted and the results are very clearly presented. The data generated will be a valuable resource for further studies. The strengths of this study are the application of single-cell multi-omics using CITE-Seq to study individual variations in stem and progenitor clusters at diagnosis that are associated with good versus poor outcomes in response to TKI treatment. These results were confirmed by deconvolution of a historical bulk RNAseq data set. Moreover, they are also consistent with a recent report from Krishnan et al. and are a useful confirmation of those results. The major new contribution of this study is the use of gene expression profiles to distinguish BCR-ABL+ and BCR-ABL- populations within CML primitive stem cell clusters and then applying antibody-derived tag (ADT) data to define molecularly identified BCR:ABL+ and BCR-ABL- primitive cells by expression of surface markers. This approach allowed them to show an association between the ratio of BCR-ABL+ vs BCR-ABL- primitive cells and TKI response and study dynamic changes in these populations following short-term TKI treatment.

Weaknesses:

One of the limitations of the study is the small number of samples employed, which is insufficient to make associations with outcomes with confidence. Although the authors discuss the potential heterogeneity of primitive stem, they do not directly address the heterogeneity of hematopoietic potential or response to TKI treatment in the results presented. Another limitation is that the BCR-ABL + versus BCR-ABL- status of cells was not confirmed by direct sequencing for BCR-ABL. The BCR-ABL status of cells sorted based on CD26 and CD35 was evaluated in only two samples. We also note that the surface markers identified were previously reported by the same authors using different single-cell approaches, which limits the novelty of the findings. It will be important to determine whether the GEP and surface markers identified here are able to distinguish BCR-ABL+ and BCR-ABL- primitive stem cells later in the course of TKI treatment. Finally, although the authors do describe differential gene expression between CML and normal, BCR:ABL+ and BCR:ABL-, primitive stem cells they have not as yet taken the opportunity to use these findings to address questions regarding biological mechanisms related to CML LSC that impact on TKI response and outcomes.

Reviewer #2 (Public Review):

Summary:

The authors use single-cell "multi-comics" to study clonal heterogeneity in chronic myeloid leukemia (CML) and its impact on treatment response and resistance. Their main results suggest 1) Cell compartments and gene expression signatures both shared in CML cells (versus normal), yet 2) some heterogeneity of multiomic mapping correlated with ELN treatment response; 3) further definition of s unique combination of CD26 and CD35 surface markers associated with gene expression defined BCR::ABL1+ LSCs and BCR::ABL1- HSCs. The manuscript is well-written, and the method and figures are clear and informative. The results fit the expanding view of cancer and its therapy as a complex Darwinian exercise of clonal heterogeneity and the selective pressures of treatments.

Strengths:

Cutting-edge technology by one of the expert groups of single-cell 'comics.

Weaknesses:

Very small sample sizes, without a validation set.<br /> The obvious main problem with the study is that an enormous amount of results and conjecture arise from a very small data set: only nine cases for the treatment response section (three in each of the ELN categories), only two normal marrows, and only two patient cases for the division kinetic studies. Thus, it is very difficult to know the "noise" in the system - the stability of clusters and gene expression and the normal variation one might expect, versus patterns that may be reproducibly study artifact, effects of gene expression from freezing-thawing, time on the bench, antibody labeling, etc. This is not so much a criticism as a statement of reality: these elegant experiments are difficult, time-consuming, and very expensive. Thus in the Discussion, it would be helpful for the authors to just frankly lay out these limitations for the reader to consider. Also in the Discussion, it would be interesting for the authors to consider what's next: what type of validation would be needed to make these studies translatable to the clinic? Is there a clever way to use these data to design a faster/cheaper assay?

Reviewer #1 (Public Review):

Summary:

Mainali and colleagues provide evidence for Itaconate stabilising Cpt1a via a decrease in ubiquitination. This in turn likely regulates fatty acid oxidation which in turn would appear to be involved in thermoregulation in the context of sepsis.

Strengths:

These findings add to our knowledge of the role of Itaconate in sepsis and its rather complex effects on metabolism, specifically lipid metabolism.

Weaknesses:

1. This is a complex paper and would benefit from a schematic depicting the key findings.

2. The paper would benefit from additional supporting evidence. Would it be possible to measure fatty acid oxidation by metabolic tracing here, in IRG-deficient cells or in response to 4-OI? Although changes in protein level for Cpt1A are seen, this is correlated with fatty acid oxidation rather than direct demonstration. This may be challenging but would strengthen the manuscript.

3. The aspect concerning body temperature regulation is confusing. Would Itaconate not promote fatty acid oxidation to increase or maintain body temperature? Itaconate must therefore not be involved in the hypothermic response? Bringing UCP1 into the finding is confusing and needs to be better explained. Again a diagram would help, but enhanced BAT fatty acid oxidation and UCP1 expression appear linked here, with both being affected by Itaconate. This needs clarifying.

Reviewer #2 (Public Review):

Summary:

This manuscript provides important new findings regarding the connection between inflammation and metabolism. It also identifies a new type of post-translational modification and its connection to protein stability. This finding is expected to be generalizable to other protein targets. In vitro evidence is solid. In vivo evidence needs some additional controls.

Strengths:

A new connection between inflammation and metabolism.

A novel type of PTM was identified.

Findings would be of broad interest and the mechanisms are likely generalizable to related control systems.

In vitro data are well-supported.

The authors successfully demonstrated that treatment with 4-octyl Itaconate (4-OI), a prodrug form of itaconate, reduces neutral lipid accumulation in the AML12 cell line and primary hepatocytes. They show that 4-OI promotes fatty acid beta-oxidation through increased stability of CPT1a protein, the rate-limiting step in this process.

Weaknesses:

Some conclusions involving the Irg1 knockout mice require important controls and clarifications to be fully convincing and some controls are missing.

Reviewer #1 (Public Review):

The association of vitamin D supplementation in reducing Asthma risk is well studied, although the mechanistic basis for this remains unanswered. In the presented study, Kilic and co-authors aim to dissect the pathway of Vitamin D-mediated amelioration of allergic airway inflammation. They use initial leads from bioinformatic approaches, which they then associate with results from a clinical trial (VDAART) and then validate them using experimental approaches in murine models. The authors identify a role of VDR in inducing the expression of the key regulator Ikzf3, which possibly suppresses the IL-2/STAT5 axis, consequently blunting the Th2 response and mitigating allergic airway inflammation.

The major strength of the paper lies in its interdisciplinary approach, right from hypothesis generation, and linkage with clinical data, as well as in the use of extensive ex vivo experiments and in vivo approaches using knock-out mice. The study presents some interesting findings including an inducible baseline absence/minimal expression of VDR in lymphocytes, which could have physiological implications and needs to be explored in future studies.<br /> However, the study presents a potential for further dissection of relevant pathophysiological parameters using additional techniques, to explain certain seemingly associative results, and allow for a more effective translation.

Several results in the study suggest multiple factors and pathways influencing the phenotype seen, which remain unexplored. The inferences of this study also need to be read in the context of the different sub-phenotypes and endotypes of Asthma, where the Th2 response may not be predominant. While this does not undermine the importance of this elegant study, it is essential to emphasise a holistic picture while interpreting the results.

Reviewer #2 (Public Review):

Summary:<br /> This study seeks to advance our knowledge of how vitamin D may be protective in allergic airway disease in both adult and neonatal mouse models. The rationale and starting point are important human clinical, genetic/bioinformatic data, with a proposed role for vitamin D regulation of 2 human chromosomal loci (Chr17q12-21.1 and Chr17q21.2) linked to the risk of immune-mediated/inflammatory disease. The authors have made significant contributions to this work specifically in airway disease/asthma. They link these data to propose a role for vitamin D in regulating IL-2 in Th2 cells implicating genes associated with these loci in this process.

Strengths:<br /> Here the authors draw together evidence form. multiple lines of investigation to propose that amongst murine CD4+ T cell populations, Th2 cells express high levels of VDR, and that vitamin D regulates many of the genes on the chromosomal loci identified to be of interest, in these cells. The bottom line is the proposal that vitamin D, via Ikfz3/Aiolos, suppresses IL-2 signalling and reduces IL-2 signalling in Th2 cells. This is a novel concept and whilst the availability of IL-2 and the control of IL-2 signalling is generally thought to play a role in the capacity of vitamin D to modulate both effector and especially regulatory T cell populations, this study provides new data.

Weaknesses:<br /> Overall, this is a highly complicated paper with numerous strands of investigation, methodologies etc. It is not "easy" reading to follow the logic between each series of experiments and also frequently fine detail of many of the experimental systems used (too numerous to list), which will likely frustrate immunologists interested in this. There is already extensive scientific literature on many aspects of the work presented, much of which is not acknowledged and largely ignored. For example, reports on the effects of vitamin D on Th2 cells are highly contradictory, especially in vitro, even though most studies agree that in vivo effects are largely protective. Similarly other reports on adult and neonatal models of vitamin D and modulation of allergic airway disease are not referenced. In summary, the data presentation is unwieldy, with numerous supplementary additions, that makes the data difficult to evaluate and the central message lost. Whilst there are novel data of interest to the vitamin D and wider community, this manuscript would benefit from editing to make it much more readily accessible to the reader.

Wider impact: Strategies to target the IL-2 pathway have long been considered and there is a wealth of knowledge here in autoimmune disease, transplantation, GvHD etc - with some great messages pertinent to the current study. This includes the use of IL-2, including low dose IL-2 to boost Treg but not effector T cell populations, to engineered molecules to target IL-2/IL-2R.

Reviewer #2 (Public Review):

Summary:

This manuscript from Liu et al. examines the role of Fat and Dachsous, two transmembrane proto-cadherins that function both in planar cell polarity and in tissue growth control mediated by the Hippo pathway. The authors developed a new method for measuring growth of the wing imaginal disc during late larval development and then used this approach to examine the effects of disruption of Fat/Dachsous function on disc growth. The authors show that during mid to late third instar the wing imaginal disc normally grows in a linear rather than exponential fashion and that this occurs due to slowing of the mitotic cell cycle as the disc grows during this period. Consistent with their known role in regulating Hippo pathway activity, this slowing of growth is disrupted by loss of Fat/Dachsous function. The authors also observed a previously unreported gradient of Fat protein across the wing blade. However, graded expression of Fat or Dachsous is not necessary for proper growth regulation in the late third instar because ectopic Dachsous expression, which affects gradients of both Dachsous and Fat, has no growth phenotype.

Strengths:

Although the role of the Hippo pathway in growth control has been extensively studied, our understanding of how the pathway controls growth during normal development remains relatively weak. This work addresses this question by examining normal growth of the wing imaginal disc during part of its development in the larva and characterizing the effects of Fat/Dachsous manipulation on that growth. The authors developed tools for measuring wing growth by measuring wing volume, an approach that could be useful in future studies of tissue growth.

Weaknesses:

1) Although the approach used to measure volume is new to this study, the basic finding that imaginal disc growth slows at the mid-third instar stage has been known for some time from studies that counted disc cell number during larval development (Fain and Stevens, 1982; Graves and Schubiger, 1982). Although these studies did not directly measure disc volume, because cell size in the disc is not known to change during larval development, cell number is an accurate measure of tissue volume. However, it is worth noting that the approach used here does potentially allow for differential growth of different regions of the disc.

2) Related to point 1, a main conclusion of this study, that cell cycle length scales with growth of the wing, is based on a developmentally limited analysis that is restricted to the mid-third instar larval stage and later (early third instar begins at 72 hr - the authors' analysis started at 84 hr). The previous studies cited above made measurements from the beginning of the 3rd instar and combined them with previous histological analyses of cell numbers starting at the beginning of the 2nd instar. Interestingly, both studies found that cell number increases exponentially from the start of the 2nd instar until mid-third instar, and only after that point does the cell cycle slow resulting in the linear growth reported here. The current study states that growth is linear due to scaling of cell cycle with disc size as though this is a general principle, but from the earlier studies, this is not the case earlier in disc development and instead applies only to the last day of larval life.

3) The analysis of the roles of Fat and Dachsous presented here has weaknesses that should be addressed. It is very curious that the authors found that depletion of Fat by RNAi in the wing blade had essentially no effect on growth while depletion of Dachsous did, given that the loss of function overgrowth phenotype of null mutations in fat is more severe than that of null mutations in dachsous (Matakatsu and Blair, 2006). An obvious possibility is that the Fat RNAi transgene employed in these experiments is not very efficient. The authors tried to address this by doubling the dose of the transgene, but it is not clear to me that this approach is known to be effective. The authors should test other RNAi transgenes and additionally include an analysis of growth of discs from animals homozygous for null alleles, which as they note survive to the late larval stages.

4) It is surprising that the authors detect a gradient of Fat expression that has not been seen previously given that this protein has been extensively studied. It is also surprising that they find that expression of Nubbin Gal4 is graded across the wing blade given that previous studies indicate that it is uniform (ie. Martín et al. 2004). These two surprising findings raise the possibility that the quantification of fluorescence could be inaccurate. The curvature of the wing blade makes it a challenging tissue to image, particularly for quantitative measurements.

5) Overall, in my view the impact of these findings is limited. The focus on growth solely at the end of larval development, when there are a number of potentially confounding variables (for example hormonal cues), makes the generality of the findings reported here difficult to judge. Additionally, the functional analysis of Fat/Dachsous function in this process is limited - for example does disruption of other Hippo pathway components have a similar effect?

Reviewer #1 (Public Review):

Summary and Strengths:

The manuscript presents novel results on the regulation of Drosophila wing growth by the protocadherins Ds and Fat. The manuscript performs a more careful analysis of disc volume, larval size, and the relationship between the two, in normal and mutant larvae, and after localized knockdown or overexpression of Fat and Ds. Not all of the results are equally surprising given the previous work on Fat, Ds, and their regulation of disc growth, pupariation, and the Hippo pathway, but the presentation and detail of the presented data is new. The most novel results concern the scaling of gradients of Fat and Ds protein during development, a largely unstudied gradient of Fat protein, and using overexpression of Ds to argue that changes in the Ds gradient do not underlie the slowing and halting of cell divisions during development.

Weaknesses:

Below I list questions and suggestions about the methodology, the presentation, and the interpretation of the data.

1) Pouch growth: division or recruitment? The study chooses to examine growth only in the prospective wing blade (the "pouch") rather than the wing disc as a whole. This can create biases, as fat and ds manipulations often cause stronger effects on growth, and on Hippo signaling targets, in the adjacent hinge regions of the disc. So I am curious about this choice.

The limitation to the wing region also creates some problems for the measurements themselves. The division between wing and pouch is not a strict lineage boundary, and thus cells can join or leave this region, creating two different reasons for changes in wing pouch size; growth of cells already in the region, or recruitment of cells into or out of the region. The authors do not discuss the second mechanism.

It is not at all clear that the markers for the pouch used by the authors are stable during development. One of these is Vg expression, or the Vg quadrant enhancer. But the Vg-expressing region is thought to increase by recruitment over late second and third instar through a feed-forward mechanism by which Vg-expressing cells induce Vg expression in adjacent cells. In fact, this process is thought to be driven in part by Fat and Ds (Zecca et al 2010). So when the authors manipulate Fat and Ds are they increasing growth or simply increasing Vg recruitment? I would prefer that this limitation be addressed.

The second pouch marker the authors use is epithelial folding, but this also has problems, as Fat and Ds manipulations change folding. Even in wild type, the folding patterns are complex. For instance, to make folding fit the Vg-QE pattern at late third the authors appear to be jumping in the dorsal pouch between two different sets of folds (Fig 1S2A). The authors also do not show how they use folding patterns in younger, less folded discs, nor provide evidence that the location of the folds are the same and do not shift relative to the cells. They also do not explain how they use folds and measure at later wpp and bpp stages, as the discs unfold and evert, exposing cells that were previously hidden in the folds.

Finally, the authors limit their measurements to cells with exposed apical faces and thus a measurable area but apparently ignore the cells inside the folds. At late third, however, a substantial amount of the prospective wing blade is found within the folds, especially where they are deepest near the A/P compartment boundary. Using the third vein sensory organ precursors as markers, the L3-2 sensillum is found just distal to the fold, the L3-1 and the ACV sensilla are within the fold, and the GSR of the distal hinge is found just proximal to the fold. That puts the proximal half of the central wing blade in the fold, and apparently uncounted in their assays. These cells will however be exposed at wpp and especially bpp stages. How are the authors adjusting for this?

2) Stabilizing and destabilizing interactions between Fat and Ds- The authors describe a distal accumulation of Fat protein in the wing, and show that this is unlikely to be through Fat transcription. They further try to test whether the distal accumulation depends on destabilization of proximal Fat by proximal Ds by looking at Fat in ds mutant discs.

However, the authors do not describe how they take into account the stabilizing effects of heterophilic binding between the extracellular domains (ECDs) of Fat and Ds; without one, the junctional levels and stability of the other is reduced (Ma et al., 2003; Hale et al. 2015). So when they show that the A-P gradient of Fat is reduced in a ds mutant, is this because of the loss of a destabilizing effect of Ds on Fat, as they assume, or is it because all junctional Fat has been destabilized by loss of extracelluarlar binding to Ds? The description of the Fat gradient in Ds mutants is also confusing (see note 6 below), making this section difficult for the reader to follow.

The authors do not propose or test a mechanism for the proposed destabilization. Fat and Ds bind not only through their ECDs, but binding has now also been demonstrated through their ICDs (Fulford et al. 2023)

3) Ds gradient scales by volume, rather than cell number - This is an intriguing result, but the authors do not discuss possible mechanisms.

4) Autonomous effects on growth- Fat and Ds are already known to have autonomous effects on growth and Hippo signaling from clonal analyses and localized knockdowns. One novelty here is showing that localized knockdown does not delay pupariation in the way that whole animal knockdown does, although the mechanism is not investigated. Another novelty is that the authors find stronger wing pouch overgrowth after localized ds RNAi or whole disc loss of fat than after localized fat RNAi, the latter being only 11% larger. The fat RNAi result would have strengthened by testing different fat RNAi stocks, which vary in their strength and are commonly weaker than null mutations, or stronger drivers such as the ap-gal4 they used for some of their ds-RNAi experiments or use of UAS-dcr2. Another reason for caution is that Garoia (2005) found much stronger overgrowth in fat mutant clones, which were about 75% larger than control clones.

5) Flattening of Ds gradients does not slow growth. One model suggests that the flattening of the Ds gradient, and thus polarized Ds-Fat binding, account for slowed growth in older discs. The difficulty in the past has been that two ways of flattening the Ds gradient, either removing Ds or overexpressing Ds uniformly, give opposite results; the first increases growth, while the latter slows it. Both experiments have the problem of not just flattening the gradient, but also altering overall levels of Ds-Fat binding, which will likely alter growth independent of the gradients. Here, the authors instead use overexpression to create a strong Ds gradient (albeit a reversely oriented one) that does not flatten, and show that this does not prevent growth from slowing and arresting.

To make sure that this is not some effect caused by using a reverse gradient, one might instead induce a more permanent normally oriented Ds gradient and see if this also does not alter growth; there is a ds Trojan gal4 line available that might work for this, and several other proximal drivers.

Another possible problem is that, unlike previous studies, the authors have not blocked the Four-jointed gradient; Fj alters Fat-Ds binding and might regulate polarity independently of Ds expression. A definitive test would be to perform the tests above in four-joined mutant discs.

The Discussion of these data should be improved. The authors state in the Discussion "The significance of these dynamics is unclear, but the flattening of the Fat gradient is not a trigger for growth cessation." While the Discussion mentions the effects of Ds on Fat distribution in some detail, this is the only phrase that discusses growth, which is surprising given how often the gradient model of growth control is mentioned elsewhere. The reader would be helped if details are given about what experiment supports this conclusion, the effect on not only growth cessation but cell cycle time, and why the result differs from those of Rogjula 2008 and Willecke 2008 using Ds and Fj overexpression.

6) Discussion of Dpp. The authors spend much of the discussion speculating on the possibility that Fat and Ds control growth by changing the wing's sensitivity to the BMP Dpp. As the manuscript contains no new data on Dpp, this is somewhat surprising. The discussion also ignores Schwank (2011), who argues that Fat and Dpp are relatively independent. There have also been studies showing genetic interactions between Fat and signaling pathways such as Wg (Cho and Irvine 2004) and EGF (Garoia 2005).

Reviewer #1 (Public Review):

The manuscript by Geurrero and colleagues introduces two new metrics that extend the concept of "druggability"- loosely speaking, the potential suitability of a particular drug, target, or drug-target interaction for pharmacological intervention-to collections of drugs and genetic variants. The study draws on previously measured growth rates across a combinatoriality complete mutational landscape involving 4 variants of the TEM-50 (beta lactamase) enzyme, which confers resistance to commonly used beta-lactam antibiotics. To quantify how growth rate - in this case, a proxy for evolutionary fitness - is distributed across allelic variants and drugs, they introduce two concepts: "variant vulnerability" and "drug applicability".

Variant vulnerability is the mean vulnerability (1-normalized growth rate) of a particular variant to a library of drugs, while drug applicability measures the mean across the collection of genetic variants for a given drug. The authors rank the drugs and variants according to these metrics. They show that the variant vulnerability of a particular mutant is uncorrelated with the vulnerability of its one-step neighbors, and analyze how higher-order combinations of single variants (SNPs) contribute to changes in growth rate in different drug environments.

The work addresses an interesting topic and underscores the need for evolution-based metrics to identify candidate pharmacological interventions for treating infections. The authors are clear about the limitations of their approach - they are not looking for immediate clinical applicability - and provide simple new measures of druggability that incorporate an evolutionary perspective, an important complement to the orthodoxy of aggressive, kill-now design principles.

As I said in my initial review, I think the work could be improved with additional analysis that tie the new metrics to evolutionary outcomes. Without this evidence, or some other type of empirical or theoretical support for the utility of these metrics, I am not fully convinced that these concepts have substantial impact. The new metrics could indeed be useful--and they have intuitive appeal--but the current revisions stop short of demonstrating that these intuitive notions hold up under "realistic" conditions (whether in simulation, theory, or experiment).

Reviewer #2 (Public Review):

In the main text, the authors apply their metrics to a data set that was published by Mira et al. in 2015. The data consist of growth rate measurements for a combinatorially complete set of 16 genetic variants of the antibiotic resistance enzyme beta-lactamase across 10 drugs and drug combinations at 3 different drug concentrations, comprising a total of 30 different environmental conditions. In my previous report I had asked the authors to specify why they selected only 7 out of 30 environments for their analysis, with only one concentration for drug, but a clear explanation is still lacking. In the Data section of Material and Methods, the authors describe their criterion for data selection as follows: "we focus our analyses on drug treatments that had a significant negative effect on the growth of wildtype/TEM-1 strains". However, in Figure 2 it is seen that, even for the selected data sets, not all points are significant compared to wild type (grey points). So what criterion was actually applied?

In effect, for each chosen drug or drug combination, the authors choose the data set corresponding to the highest drug concentration. As a consequence, they cannot assess to what extent their metrics depend on drug concentration. This is a major concern, since Mira et al. concluded in their study that the differences between growth rate landscapes measured at different concentrations were comparable to the differences between drugs. I argued before that, if the new metrics display a significant dependence on drug concentration, this would considerably limit their usefulness. The authors challenge this, saying in their rebuttal that "no, that drug concentration would<br /> be a major actor in the value of the metrics does not limit the utility of the metric. It is simply another variable that one can consider when computing the metrics." While this is true in principle, I don't think any practicing scientist would disagree with the statement that the existence of additional confounding factors (in particular if they are unknown) reduces the usefulness<br /> of a quantitative metric.

As a consequence of the small number of variant-drug-combinations that are used, the conclusions that the authors draw from their analysis are mostly tentative. For example, on line 123 the authors write that the observation that<br /> the treatment of highest drug applicability is a combination of two drugs "fits intuition". In the Discussion this statement is partly retracted with reference to the piperacillin/tazobactam-combination which has low drug applicability. Being based on only a handful of data points, both observations are essentially anecdotal and it is unclear what the reader is supposed to learn.

To assess the environment-dependent epistasis among the genetic mutations comprising the variants under study, the authors decompose the data of Mira et al. into epistatic interactions of different orders. This part of the analysis is incomplete in two ways. First, in their study, Mira et al. pointed out that a fairly large fraction of the fitness differences between variants that they measured were not statistically significant. This information has been removed in the depiction of the Mira et al. fitness landscapes in Figure 1 of the present manuscript, and it does not seem to be reflected in the results of the interaction analysis in Figure 4. Second, the interpretation of the coefficients obtained from the epistatic decomposition depends strongly on the formalism that is being used. In a note added on page 15 of the revised manuscript, the authors write that they have used the LASSO regression for their analysis and refer the reader to a previous publication (Guerrero et al. 2019) which however (as far as I could see) also does not fully explain how the method works. To give an example of the difficulty of interpreting the data in Figure 4 without further information: The substitution C (G238S) is well known to have a strong positive effective in cefotaxime, but the corresponding coefficient is essentially zero. So whatever the LASSO regression does, it cannot simply measure the effect on growth.

Reviewer #3 (Public Review):

The authors introduce two new concepts for antimicrobial resistance borrowed from pharmacology, "variant vulnerability" (how susceptible a particular resistance gene variant is across a class of drugs) and "drug applicability" (how useful a particular drug is against multiple allelic variants). They group both terms under an umbrella term "drugability". They demonstrate these features for an important class of antibiotics, the beta-lactams, and allelic variants of TEM-1 beta-lactamase. In the revised version, they investigate a second drug class that targets dihydrofolate reductase in Plasmodium (the causative agent of malaria).

The strength of the result is in its conceptual advance and that the concepts seem to work for beta-lactam resistance and DHFR inhibitors in a protozoan. However, I do not necessarily see the advance of lumping both terms under "drugability", as this adds an extra layer of complicaton in my opinion.

I think that the utility of the terms will be more comprehensively demonstrated by using examples across a breadth of drug classes classes and/or resistance genes. For instance, another good bacterial model with published data might have been trimethoprim resistance, which arises through point mutations in the folA gene (although, clinical resistance tends to be instead conferred by a suite of horizontally acquired dihydrofolate reductase genes, which are not so closely related as the TEM variants explored here).

The impact of the work on the field depends on a more comprehensive demonstration of the applicability of these new concepts to other drugs. This would be demonstrated in future work.

Reviewer #1 (Public Review):

Summary:<br /> The study follows the role of yeast eIF2A protein as a potential translation initiation factor engaged in the non-canonical translation initiation under stress conditions and as a substitute for eIF2. Using ribosome profiling, RNA-Seq and reporter-based assays authors evaluated the role of eIF2A protein under regular or stress conditions (cells starved for branched amino acids). The authors found that yeast cells depleted of eIF2A protein do not change significantly their translation initiation, or translation in general. In contrast to previously reported data for human homolog, yeast eIF2A does not significantly contribute to the regulation of the uORFs, regardless of whether they start with canonical AUG or near cognate start codons. eIF2A is not involved in the repression of IRES element in the URE2 gene or has a role in purine biosynthesis. It appears that in yeast eIF2A contributes to the regulation of a very limited number of mRNAs (32 with significant changes in translation efficiency), where only 17 of such messages indeed are consistent with eIF2A deletion, and single mRNA (HKR1) could be validated in reporter assay.

Strengths:<br /> The main strength of the manuscript is a complete analysis and unbiased approach using genomic analysis methods (ribosome profiling and RNA-seq) as well as reporter validation studies. Additional strengths of the manuscript are scientific rigor and statistics associated with data analyses, clear data presentation, and discussion of the results in the context of the previous studies and results.

Weaknesses:<br /> No weaknesses were noted by this reviewer.

Reviewer #2 (Public Review):

Summary:<br /> Gaikwad et al. investigated the role of eIF2A in translational response to stress in yeast. For this purpose, the authors conducted ribosome profiling under SM treatment in an eIF2A-depleted strain. Data analysis revealed that eIF2A did not influence translation from mRNAs bearing uORFs or cellular IRESes, in the stress condition, broadly. The authors found that only a small number of mRNAs were supported by eIF2A. The data should be helpful for researchers in the field.

Major points:<br /> 1. The weakness of this work is the lack of clarification on the function of eIF2A in general. The novelty of this study was limited.

2. Related to this, it would be worth investigating common features in mRNAs selectively regulated (surveyed in Figure 3A). Also, it would be worth analyzing the effect of eIF2A deletion on elongation (ribosome occupancy on each codon and/or global ribosome footprint distribution along CDS) and termination/recycling (footprint reads on stop codon and on 3′ UTR).

3. Regarding Figure 3D, the reporters were designed to include promoter and 5′ UTR of the target genes. Thus, it should be worth noting that reporter design was based on the assumption that eIF2A-dependency in translation regulation was not dependent on 3′ UTR or CDS region. The reason why the effects on ribosome profiling-supported mRNAs could not be recapitulated in reporter assay may originate from this design. This should be also discussed.

4. Related to the point above, the authors claimed that eIF2A affects "possibly only one" (HKR1) mRNA. However, this was due to the reporter assay which is technically variable and could not allow some of the constructs to pass the authors' threshold. Alternative wording for this point should be considered.

5. For Figure 3D, it would be worth considering testing the #-marked genes (in Figure 3C) in this set up.

6. In box plots, the authors should provide the statistical tests, at least where the authors explained in the main text.

Reviewer #3 (Public Review):

Summary:<br /> The authors have undertaken a study to rigorously characterize the possible role of eIF2A in regulating translation in yeast. The authors test for the role of eIF2A in the absence or presence of cellular stress and conclude that eIF2A does not play any significant role in regulating translation initiation in yeast.

Strengths:<br /> The authors have used rigorous experimental approaches, including genome-wide ribosome profiling analysis in the absence or presence of stress, to show that eIF2A does not function in translation initiation on most mRNAs in yeast. Interestingly, the authors do identify a small number of mRNAs that possess some eIF2A dependency, so they constructed reporters to rigorously test them. One mRNA, HKR1, appears to possess a degree of eIF2A-dependent translation regulation.

Weaknesses:<br /> While no role of eIF2A in translation initiation is apparent, the authors do not determine what function eIF2A does play in yeast. Whether it plays a role in regulating translation in a different stress response is not determined.

Reviewer #1 (Public Review):

Summary and Strengths:

Zhang et al. conducted a study in which they isolated and characterized a Marburg virus (MARV) glycoprotein-specific antibody, AF-03. The antibody was obtained from a phage-display library. The study shows that AF-03 competes with the previously characterized MARV-neutralizing antibody MR78, which binds to the virus's receptor binding site. The authors also performed GP mutagenesis experiments to confirm that AF-03 binds near the receptor binding site. In addition, the study confirmed that AF-03, like MR78, can neutralize Ebola viruses with cleaved glycoproteins. Finally, the authors demonstrated that NPC2-fused AF-03 was effective in neutralizing several filovirus species.

Weaknesses:

1. The main premise of this study is unclear. Flyak et al. in 2015 described the isolation and characterization of a large panel of neutralizing antibodies from a Marburg survivor (Flyak et al., Cell, 2015). Based on biochemical and structural characterization, Flyak proposed that the Marburg neutralizing antibodies bind to the NPC1 receptor binding side. In the same study, it has been shown that several MARV-neutralizing antibodies can bind to cleaved Ebola glycoproteins that were enzymatically treated to remove the mucin-like domain and glycan cap. In the following study, it has been shown that the bispecific-antibody strategy can be used to deliver Marburg-specific antibodies into the endosome, where they can neutralize Ebola viruses (Wec et al., Science 2016). Finally, the use of lysosome-resident protein NPC2 to deliver antibody cargos to late endosomes has been previously described (Wirchnianski et al., Front. Immunol, 2021)

The above-mentioned studies are not referenced in the introduction. The authors state that "there is no licensed treatment or vaccine for Marburg [virus] infection." While this is true, there are human antibodies that recognize neutralizing epitopes - that information can't be excluded while providing the rationale for the study. Furthermore, the authors use the word "novel" to describe the AF-03 antibody. How novel is AF-03 if multiple Marburg-neutralizing antibodies were previously characterized in multiple studies? Since AF-03 competes with previously characterized MR78, it binds to the same antigenic region as MR78. AF-03 also has comparable neutralization potency as MR78.

2. Without the AF-03-MARV GP crystal structure, it's unclear how van der Waals interactions, H-bonds, and polar and electrostatic interactions can be evaluated. While authors use computer-guided homology modeling, this technique can't be used to determine critical interactions. Furthermore, Flyak et al. reported that binding to the NPC1 receptor binding site is the main mechanism of Marburg virus neutralization by human monoclonal antibodies. Since both AF-03 (this study) and MR78 (Flyak study) competed with each other, that information alone was sufficient for GP mutagenesis experiments that identified the NPC1 receptor binding site as the main region for mutagenesis.

3. The AF-03-GP affinity measurements were performed using bivalent IgG molecules and trimeric GP molecules. This format does not allow accurate measurements of affinity due to the avidity effect. The reported KD value is abnormally low due to avidity effects. The authors need to repeat the affinity experiments by immobilizing trimeric GPs and then adding monovalent AF-03 Fab.

Reviewer #2 (Public Review):

Summary:

The authors describe the discovery of a filovirus neutralizing antibody, AF03, by phage display, and its subsequent improvements to include NPC2 that resulted in a greater breadth of neutralization. Overall, the manuscript would benefit from considerable grammatical review, which would improve the communication of each point to the reader. The authors do not convincingly map the AF03 epitope, nor do they provide any strong support for their assumption that AF03 targets the NPC1 binding site. However, the authors do show that AF03 competes for MR78 binding to its epitope, and provides good support for the internalization of AF03-NL as the mechanism for improved breadth over the original AF03 antibody.

Strengths:

This study shows convincing binding to Marburgvirus GP and neutralization of Marburg viruses by AF03, as well as convincing neutralization of Ebolaviruses by AF03-NL. While there are no distinct populations of PE-stained cells shown by FACS in Figure 5A, the cell staining data in Figure 5C are compelling to a non-expert in endosomal staining like me. The control experiments in Figure 7 are compelling showing neutralization by AF03-NL but not AF03 or NPC2 alone or in combination. Altogether these data support the internalisation and stabilisation mechanism that is proposed for the gain in neutralization breadth observed for Ebolaviruses by AF03-NL over AF03 alone.

Weaknesses:

Overall, this reviewer is of the opinion that this paper is constructed haphazardly. For instance, the neutralization of mutant pseudoviruses is shown in Figure 2 before the concept of pseudovirus neutralization by AF03 is introduced in Figure 3. Similarly, the control experiments for AF03+NPC2 are described in Figure 7 after the data for breadth of neutralization are shown in Figure 6. GP quality controls are shown in Figure 2 after GP ELISAs / BLI experiments are done in Figure 1. This is disorienting for the reader.

Figure 1: The visualisation of AF03 modelling and docking endeavours is extremely difficult to interpret. Firstly, there is no effort to orient the non-specialist reader with respect to the Marburgvirus GP model. Secondly, from the figures presented it is impossible to tell if the Fv docks perfectly onto the GP surface, or if there are violent clashes between the deeply penetrating AF03 CDRs and GP. This information would be better presented on a white background, perhaps showing GP in surface view from multiple angles and slices. The authors attempt to label potential interactions, but these are impossible to read, and labels should be added separately to appropriately oriented zoomed-in views.

Figure 2: The neutralization of mutant pseudoviruses cannot be properly assessed using bar graphs. These data should be plotted as neutralization curves as they were done for the wild-type neutralization data in Figure 3. The authors conclude that Q128 & N129 are contact residues, but the neutralization data for this mutant appear odd as the lowest two concentrations of AF03 show higher neutralization than the second highest AF03 concentration. Neutralization of T204/Q205/T206 (green), Y218 (orange), K222 (blue), or C226 (purple) appears to be better than neutralization of the wild-type MARV. The authors do not discuss this oddity. What are the IC50's? The omission of antibody concentrations on the x-axis and missing IC50 values give a sense of obscuring the data, and the manuscript would benefit from greater transparency, and be much easier to interpret if these were included. I am intrigued that the Q128S/N129S mutant is reported as having little effect on the neutralization of MR78. The bar graph appears to show some effect (difficult to interpret without neutralization curves and IC50 data), and indeed PDB:5UQY seems to suggest that these amino acids form a central component of the MR78 epitope (Q128 forms potential hydrogen bonds with CDRH1 Y35 and CDRL3 Y91, while N129 packs against the MR78 CDRH3 and potentially makes additional polar contact with the backbone). Lastly, since neutralization was tested in both HEK293T cells and Huh7 cells in Figure 3, the authors should clarify which cells were used for neutralization in Figure 2.

Figure 3: The first two images in Figure 3C showing bioluminescent intensity from pseudovirus-injected mice pretreated with either 10mg/kg or 3mg/kg AF03 are identical images. This is apparent from the location, shape, and intensity of the bioluminescence, as well as the identical foot placement of each mouse in these two panels. Currently, this figure is incomplete and should be corrected to show the different mice treated with either 10mg/kg or 3mg/kg of AF03.

Figure 4 would benefit from a control experiment without antibodies comparing infection with GP-cleaved and GP-uncleaved pseudoviruses. The paragraph describing these data was also difficult to read and would benefit from additional grammatical review.

Figure 5: The authors should clarify in the methods section that the "mock" experiment included the PE anti-human IgG Fc antibody. Without this clarification, the lack of a distinct negative population in the FACS data could be interpreted as non-specific staining with PE. If the PE antibody was added at an equivalent concentration to all panels, what does the directionality of the arrowheads in Figure 5A (labelled PE) and 5B (labelled pHrodo Red) indicate?

Figure 6B: These data would benefit from the inclusion of IC50, transparency of antibody concentrations used, and consistency in the direction of antibody concentrations (increasing to the right or left of the x-axis) when compared to Figure 2.

Reviewer #1 (Public Review):

Summary:

Mandal et al build upon their earlier work in CD 4 T cells to address the role of WASP in cytotoxic T cell mechanosensing. As shown previously by this group and others, the authors present evidence that tumour cell lysis is stiffness dependent and requires CTL WASP expression. They proceed to show that CTLs engaging targets form actin-rich foci, that the formation of these structures is dependent upon tumour cell stiffness and WASP dependent actin nucleation. Traction force measurements show that WASP is involved in force generation, and evidence that WASP plays a role in mechanosensing comes from studies showing that stiffness dependent phosphorylation of early TCR signalling intermediates (but not the later stages of T cell activation) is WASP dependent, as is phosphorylation of the tension sensor CasL. Finally, the authors provide in vivo data that WASP-deficient T cells kill tumours inefficiently.

Strengths:

The paper is well-written and brings together a range of well-established techniques for measuring T cell stiffness responses, force production, signalling, and effector function. Although some of the findings are necessarily correlative, the authors have largely achieved their aims. One particularly interesting observation is that stiffness dependent phosphorylation of ZAP70 requires WASP expression. Evidence that ZAP70 phosphorylation is WASP dependent is important, as it suggests that forces exerted by WASP are needed for some of the earliest stages of TCR signalling, perhaps TCR deformation itself. This observation, made in CD8 T cells, is particularly interesting given that previous work from this group [Kumari et al eLife 2015] showed that ZAP70 phosphorylation was intact in WASP-/- CD4 T cell blasts. In that study, the first clear differences in TCR signaling were seen at the level of PLCγ phosphorylation. This could represent an interesting difference between CD4 and CD8 T cells, but supplemental data from Figure S2 also show WASP dependence for CD3ζ and ZAP70 phosphorylation in naïve CD4 T cells. Unfortunately, this interesting issue was not discussed or pursued experimentally.

Weaknesses:

While the study is well executed, it is rather limited in scope, and many of the observations have been reported previously in other systems. These weaknesses limit the impact of the study. In particular, the authors have previously shown in CD4 T cells that the nucleation promoting activity of WASP is responsible for the formation of actin foci, for early TCR signalling events associated with T cell activation, for traction force generation and for CasL phosphorylation [Kumari et al eLife 2015, Kumari et al EMBO J 2020]. It could be argued that this paper extends findings made originally in CD4 cells to include CD8 T cells. But the authors did not make this clear, and the advance is rather incremental. Moreover, similar studies have been done in CD8 T cells by other labs. Most notably, the Huse group has conducted highly relevant work investigating the mechanobiology of CTL function in vitro and in vivo [Basu et al Cell 2016, Wang et al Nat Comms 2022, Tamzalit et al Sci Immunol 2019, Tello-Lafoz et al Immunity 2021, de Jesus et al bioRxiv Preprint 2023]. Indeed, one study showed that WASP depletion impairs the formation of protrusions that deform the target cell surface and promote target lysis [Tamzalit et al Sci Immunol 2019]. Mandal et al cite this work and argue that what they show differs from the mechanopotentiation shown in Tamzalit et al, but they don't explore the issue further. They also fail to cite work from Tello-Lafoz et al showing that regulated changes in target cell stiffness contribute to CTL vulnerability. Finally, Mandal et al. fail to deal with evidence that WASP participates in many phases of the CTL response, including adhesion, migration, granule release, and serial killing. All of these are likely contributors to the in vivo phenotypes shown in Figure 4.

Reviewer #2 (Public Review):

Summary:

Mandal et al. use WASP-deficient T cells to study the role of WASP in T cell signaling and activation and tying WASP to mechanosensing in T cells. Using both CD8 and CD4 T cells from WASP-deficient animals, the authors show defects in T cell signaling and function as well as defects in mechanosensing in activated CD8 T cells.

Strengths:

Confirming findings from many previous studies, Mandal et al. demonstrate that WASP-deficiency in T cells leads to defective T cell function (Figs 1, 2, 3, and 4). Fig 3 shows direct effects of mechanical stress on CD8 T cell signaling in the absence of WASP.

Weaknesses:

The title does not reflect the data presented as the only data demonstrating a role for WASP in mechanosensing in this manuscript doesn't directly connect WASP mechanosensing with tumors (Fig 3). The results shown in Fig 1 using an actin inhibitor doesn't directly connect WASP with mechanosensing. Fig 4 uses WASP-deficient animals in a tumor model, but doesn't demonstrate any role for mechanosensing in the WASP-deficient animals. The title should reflect the lack of data connecting WASP in mechanosensing to a tumor context.

One major oversight is the absence of discussion of a previous publication demonstrating a direct role of WASP in mechanosensing to the actin cytoskeleton in dendritic cells and naive CD4 and CD8 T cells (Gaertner et al. Dev Cell 2022). There should be a discussion of how the findings in Gaertner et al. shed light on the results from this manuscript.

The use of Myca to disrupt the actin cytoskeleton as a "modulator of stiffness" is problematic. While one of the potential effects of disrupting the actin cytoskeleton is changing stiffness, as shown in Figure 1, many other functions are simultaneously disturbed also. The use of B16 tumor cells is simply for antigen presentation, and not in a tumor context, so generalized statements about "stiffness" or "softness" and "tumor cells" in reference to Figure 1 should be changed to account for these alternative explanations.

Fig S2 shows Myca treatment of BMDCs leads to decreased functionality of OTII CD4s. Interpretation in the manuscript claims "This indicates that leaching of Myca from treated cells does not cause inhibition of bystander cells". This would not be my interpretation of the data. An alternative interpretation is that if Myca is remaining in the media, then effects on APCS (either BMDCs or B16s) could lead to decreased CD4 or CD8 T cell activation and thus be responsible for effects seen in Fig 1. This possibility should be considered.

Fig 4 claims that high rigidity leads to downstream effects of WASP-/- T cell function. But there is no demonstration of the role of mechanosensing in Figure 4. To make this claim, the authors would need to compare high and low rigidity conditions.

Fig 4 also shows that WASP-/- showed higher tumor growth in an implanted tumor model. For 4F, since WASP is deficient in all hematopoietic cells, the finding in 4G may not be due to T cells. In 4H-J, because implantation of tumors occurs within 1 day of lymphodepletion and assessing tumor growth prior to reconstitution of the hematopoietic compartment, there should be control experiments shown to demonstrate that other hematopoietic cell types that remain are not function and thus do not participate in the differences seen in tumor growth. Also, statistical tests need to be done to show the significance of the differences between groups in Fig 4I and 4J (also 4G).

Reviewer #3 (Public Review):

The manuscript from Mandal et al. aims to show that the actin cytoskeleton is the key mechanosensitive element in cytotoxic T lymphocytes, enabling them to discriminate between target cells of different cortical stiffness. They further examine whether WASP activation is sensitive to substrate stiffness, and thus modulates actin polymerization and early T cell signaling in a mechanosensitive manner. Overall, the mechanosensitivity of CTLs has attracted a lot of attention in the last few years and this study explores new and interesting facets. The manuscript asks an important question regarding the mechanisms underlying the stiffness dependent response observed in T cells. The authors have used a variety of techniques ranging from mouse models and in vivo studies, cell biological manipulations and biophysical measurements which is commendable. Their work suggests that the actin cytoskeleton regulated by WASP plays a key role in mechanosensitivity - which is an intriguing finding.

While this manuscript has wide-ranging experiments and interesting results, a number of points need to be carefully addressed to support the central claims.

The first major issue is that the irreversible actin inhibitor myca can have a number of non-specific effects on CTL activation. It is not clear that the effects observed are due to the change in stiffness alone. Since Myca depolymerizes actin, the B16 target cells would have altered MHC mobility or impaired receptor-ligand engagement - which might affect actin foci formation and signaling. There is also no gain of function experiment, wherein the stiffness of the target cell is enhanced. Moreover, there are two populations in both the control and myca-treated Young's modulus histograms for B16 cells. Are these sub-populations fundamentally different in their cytoskeletal organization? This can also confound or introduce variability in results on stiffness-dependence of CTL function, given the second sub-population of Myca-treated cells overlaps with the first sub-population of control cells. The authors need to provide a justification for these.

Secondly, the WASP knockout still shows mechanosensitivity but at reduced force levels (Fig. 3B). Similarly, other measures (Fig. 3) still show increases with stiffness. Thus, it is not clear whether WASP is necessary for mechanosensing but simply for maintaining force levels and (expectedly) lower actin levels and foci in the WASP knockout. In fact, Fig 3 implies WASP is required for signaling and not for mechanosensing, undermining the main claim of the paper. At the very least, ANOVA or factor analysis (stiffness x WASP) needs to be done to demonstrate the requirement of WASP for CTL mechanosensitivity.

Third, there are some concerns regarding the traction force microscopy. The authors do not present key details in the manuscript about the methods used. Secondly, the traction values are entirely too high compared to reported values in the literature for CTLs. A back-of-the-envelope calculation of the total force yields ~30 nN for wild-type cells) on 10 kPa gels, which is about an order of magnitude higher than reported values (Tamzalit et al. 2020, Hui et al. 2017, Bashour et al. 2014, Pathni et al. 2022). The authors should clearly demonstrate and justify that their measured values are reasonable and accurate. The lack of representative movies and displacement maps used for the traction force measurements make it hard to evaluate the results. Typical bead displacements for CTLs on softer gels are on the order of 1 micron (Mustapha et al. 2022), which should decrease to 0.1 micron or less on 50 kPa gels. These would make the tractions hard to estimate accurately. The authors should evaluate and show the displacements underneath the cell and outside the cell boundaries to give estimates of the noise floor for tractions. Finally, there is no discussion of how the tractions were calculated from the displacements - was Fourier Transform or Finite element method used? What is the noise level of the measurements and how were the traction estimates regularized?

Fourth, many of the plots in the manuscripts are not accompanied by representative images to show how these aspects (distribution of actin and signaling markers for example) change qualitatively under different conditions (e.g. stiffness). Details of analysis and quantification need to be provided for a clearer understanding of the results and interpretations. All figures and captions should include information about the number of cells and experiments. Along these lines, there is very little detail in the methods, statistical power, calculations are not mentioned, there is little description of the pmel-1 knockout mouse, all of which make it hard to evaluate the soundness of the results.

Finally, the study as presented, doesn't conclusively show that WASP is required for mechanosensitive CTL function. The results presented show that WASP is required for early and longer-term signaling events and cytolytic activity, and that knocking out WASP reduces early TCR signaling, actin foci formation in response to substrate stiffness. To make the claim of WASP-mediated regulation of CTL mechanosensitivity stronger, it would be helpful to see how WASP knockout affects CTL killing in response to softened and (possibly) stiffened B16 targets.

Reviewer #1 (Public Review):

The authors investigate the function of the PTB domain containing adaptor protein Numb in skeletal muscle structure and function. In particular, the effects of reduced Numb expression in aging muscle is proposed as a mechanism for reduced contractile function associated with sarcopenia. Using ex-vivo analysis of conditional Numb and Numblike knockout muscle the authors demonstrate that loss of Numb but not the related Numblike gene expression perturbs muscle force generation. In order to explore the molecular mechanisms involved, Numb interacting proteins were identified in C2C12 cell cultured myotubes by immunoprecipitation and LC-MS/MS. The authors identify Septin 7 as well as Septin 2, 9 and 10 as a Numb binding proteins and demonstrate that loss of Numb/Numblike in myofibers causes changes in Septin 7 subcellular localization. Of note, whether additional septins form a complex or are also disrupted by Numb/Numblike loss remains an interesting area for further investigation. Additional investigation of the specificity and mapping of the Numb-Septin 7 (or another Septin) interaction would be of interest and provide an approach for future studies to demonstrate the biological relevance and specificity of the Numb-Septin 7 interaction in skeletal muscle

Reviewer #2 (Public Review):

Summary:

The main purpose of this investigation was to 1) compare the effects of a single knockout (sKO) of Numb or a double knockout (dKO) of Numb and NumbL on ex-vivo physiological properties of the extensor digitorium longus (EDL) muscle in C57BL/6NCrl mice; and 2) analyze protein complexes isolated from C2C12 myotubes via immunoprecipitation and LC/MS/MS for potential Numb binding partners. The main findings are 1) the muscles from sKO and dKO were significantly weaker with little difference between the sKO and dKO lines, indicating the reduced force is mainly due to the inactivation of the Numb gene; and 2) there were 11 potential Numb binding proteins that were identified and cytoskeletal specific proteins including Septin 7.

Strengths:

Straight-forward yet elegant design to help determine the important role the Numb has in skeletal muscle.

Weaknesses:

There were a limited number of samples (3-6) that were used for the physiological experiments; however, there was a very large effect size in terms of differences in muscle tension development between the induced KO models and the controls.

Reviewer #1 (Public Review):

Summary:

This manuscript presents the development of a new microscope method termed "open-top two-photon light sheet microscopy (OT-TP-LSM)". While the key aspects of the new approach (open-top LSM and Two-photon microscopy) have been demonstrated separately, this is the first system of integrating the two. The integration provides better imaging depth than a single-photon excitation OT-LSM.

Strengths:

- The use of liquid prism to minimize the aberration induced by index mismatching is interesting and potentially helpful to other researchers in the field.<br /> - The use of propidium iodide (PI) provided a deeper imaging depth.

Weaknesses:

- Details are lacking on imaging time, data size, the processing time to generate large-area en face images, and inference time to generate pseudo H&E images. This makes it difficult to assess how applicable the new microscope approach might be in various pathology applications.

Reviewer #2 (Public Review):

Summary:

In this manuscript, the authors developed an open-top two-photon light sheet microscopy (OT-TP-LSM) that enables high-throughput and high-depth investigation of 3D cell structures. The data presented here shows that OT-T-LSM could be a complementary technique to traditional imaging workflows of human cancer cells.

Strengths:

High-speed and high-depth imaging of human cells in an open-top configuration is the main strength of the presented study. An extended depth of field of 180 µm in 0.9 µm thickness was achieved together with an acquisition of 0.24 mm2/s. This was confirmed by 3D visualization of human cancer cells in the skin, pancreas, and prostate.

Weaknesses:

The complementary aspect of the presented technique in human pathological samples is not convincingly presented. The traditional hematoxylin and eosin (H&E) staining is a well-established and widely used technique to detect human cancer cells. What would be the benefit of 3D cell visualization in an OT-TP-LSM microscope for cancer detection in addition to H&E staining?

Joint Public Review:

In countries endemic for P vivax the need to administer a primaquine (PQ) course adequate to prevent relapse in G6PD deficient persons poses a real dilemma. On one hand PQ will cause haemolysis; on the other hand, without PQ the chance of relapse is very high. As a result, out of fear of severe haemolysis, PQ has been under-used.

In view of the above, the authors have investigated in well-informed volunteers, who were kept under close medical supervision in hospital throughout the study, two different schedules of PQ administration: (1) escalating doses (to a total of 5-7 mg/kg); (2) single 45 mg dose (0.75 mg/kg).

It is shown convincingly that regimen (1) can be used successfully to deliver within 3 weeks, under hospital conditions, the dose of PQ required to prevent P vivax relapse.

As expected, with both regimens acute haemolytic anaemia (AHA) developed in all cases. With regimen (2), not surprisingly, the fall in Hb was less, although it was abrupt. With regimen (1) the average fall in Hb was about 4 G. Only in one subject the fall in Hb mandated termination of the study.

Since the data from the Chicago group some sixty years ago, there has been no paper reporting a systematic daily analysis of AHA in so many closely monitored subjects with G6PD deficiency. The individual patient data in the Supplementary material are most informative and more than precious.

Comments on the revised version:

In my view this important paper is further improved in this revised version (R2), particularly with respect to clarity in the discussion. All the points I had previously raised have been tackled.

Reviewer #1 (Public Review):

Amyotrophic lateral sclerosis (ALS) is a neurodegenerative disorder leading to the loss of innervation of skeletal muscles, caused by the dysfunction and eventual death of lower motor neurons. A variety of approaches have been taken to treat this disease. With the exception of three drugs that modestly slow progression, most therapeutics have failed to provide benefit. Replacing lost motor neurons in the spinal cord with healthy cells is plagued by a number of challenges, including the toxic environment, inhibitory cues that prevent axon outgrowth to the periphery, and proper targeting of the axons to the correct muscle groups. These challenges seem to be well beyond our current technological approaches. Avoiding these challenges altogether, Bryson et al. seek to transplant the replacement motor neurons into the peripheral nerves, closer to their targets. The current manuscript addresses some of the challenges that will need to be overcome, such as immune rejection of the allograft and optimizing maturation of the neuromuscular junction.

Reviewer #2 (Public Review):

The authors provide convincing evidence that optogenetic stimulation of ChR2-expressing motor neurons implanted in muscles effectively restore innervation of severely affected skeletal muscles in the aggressive SOD1 mouse model of ALS, and concluded that this method can be applied to selectively control the function of implicated muscles, which was supported by convincing data presented in the paper.

Reviewer #1 (Public Review):

Summary:

The authors have implemented the Optimal Transport algorithm in GromovMatcher for comparing LC/MS features from different datasets. This paper gains significance in the proteomics field for performing meta-analysis of LC/MS data.

Strengths:

The main strength is that GromovMatcher achieves significant performance metrics compared to other existing methods. The authors have done extensive comparisons to claim that GromovMatcher performs well.

Weaknesses:

There are two weaknesses.

1. When the number of features is reduced the precision drops to ~0.8.<br /> 2. How applicable is the method for other non-human datasets?

Reviewer #2 (Public Review):

Summary:

The goal of untargeted metabolomics is to identify differences between metabolomes of different biological samples. Untargeted metabolomics identifies features with specific mass-to-charge ratio (m/z) and retention time (RT). Matching those to specific metabolites based on the model compounds from databases is laborious and not always possible, which is why methods for comparing samples on the level of unmatched features are crucial.

The main purpose of the GromovMatcher method presented here is to merge and compare untargeted metabolomes from different experiments. These larger datasets could then be used to advance biological analyses, for example, for the identification of metabolic disease markers. The main problem that complicates merging different experiments is m/z and RT vary slightly for the same feature (metabolite).

The main idea behind the GromovMatcher is built on the assumption that if two features match between two datasets (that feature i from dataset 1 matches feature j from dataset 2, and feature k from dataset 1 matches feature l from dataset 2), then the correlations or distances between the two features within each of the datasets (i and k, and j and l) will be similar. The authors then use the Gromov-Wasserstein method to find the best matches matrix from these data.

The variation in m/z between the same features in different experiments is a user-defined value and it is initially set to 0.01 ppm. There is no clear limit for RT deviations, so the method estimates a non-linear deviation (drift) of RT between two studies. GromovMatcher estimates the drift between the two studies and then discards the matching pairs where the drift would deviate significantly from the estimate. It learns the drift from a weighted spline regression.

The authors validate the performance of their GromovMatcher method by a validation experiment using a dataset of cord blood. They use 20 different splits and compare the GromovMatcher (both its GM and GMT iterations, whereby the GMT version uses the deviation from estimated RT drift to filter the matching matrix) with two other matching methods: M2S and metabCombiner.

The second validation was done using a (scaled and centered) dataset of metabolics from cancer datasets from the EPIC cohort that was manually matched by an expert. This dataset was also used to show that using automatic methods can identify more features that are associated with a particular group of samples than what was found by manual matching. Specifically, the authors identify additional features connected to alcohol consumption.

Strengths:

I see the main strength of this work in its combination of all levels of information (m/z, RT, and higher-order information on correlations between features) and using each of the types of information in a way that is appropriate for the measure. The most innovative aspect is using the Gromov-Wasserstein method to match the features based on distance matrices.

The authors of the paper identify two main shortcomings with previously established methods that attempt to match features from different experiments: a) all other methods require fine-tuning of user-defined parameters, and, more importantly, b) do not consider correlations between features. The main strength of the GromovMatcher is that it incorporates the information on distances between the features (in addition to also using m/z and RT).

Weaknesses:

The first, minor, weakness I could identify is that there seem not to be plenty of manually curated datasets that could be used for validation. The second is also emphasized by the authors in the discussion. Namely, the method as it is set up now can be directly used only to compare two datasets.

Reviewer #1 (Public Review):

Summary:

Liang et. al., uses a previously devised full isotope labeling of peptidoglycan followed by mass spec to study the kinetics of Lpp tethering to PG and the hydrolysis of this bond by YafK.

Strengths:

-The labeling and mass spec analysis technique works very well to discern differentially labelled Tri-KR muropeptide containing new and old Lpp and PG.

Weaknesses:

-Only one line of experimentation using mass spec based analysis of labeled PG-Lpp is used to make all conclusions in the paper. The evidence is also not enough to fully deleanate the role of YafK.<br /> -Only one mutant (YafK) is used to make the conclusion.<br /> -The paper makes a lot of 'implications' with minimal proof to support their hypothesis. Other lines of experimentations must be added to fully delineate their claims.<br /> -Time points to analyse Tri-KR isotopologues in Wt (0,10,20,40,60 min) and yafK mutant (0,15, 25, 40, 60 min) are not the same.<br /> -Experiments to define physiological role of YafK are also missing.

Reviewer #2 (Public Review):

Summary:

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

Strengths:

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

Weaknesses:

However, the authors make a few other conclusions from their data which are harder to understand the logic of, or to feel confident in based on the existing data. They claim that their 5-time point kinetic data indicates that new lpp is not substantially added to lipidII before it is added to the peptidoglycan, and that instead lpp is attached primarily to old peptidoglycan. I believe that this conclusion comes from the comparison of Fig.s 3A and 3C, where it appears that new lpp is added to old peptidoglycan a few minutes before new lpp is added to new peptidoglycan. However, the very small difference in the timing of this result, the minimal number of time points and the complete lack of any presentation of calculated error in any of the data make this conclusion very tenuous. In addition, the authors conclude that lpp is not significantly attached to septal peptidoglycan. The logic behind this conclusion appears to be based on the same data, but the authors do not provide a quantitative model to support this idea.

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