Reviewer #3 (Public Review):

The authors characterized the effect of Zn2+ in potentiating OTOP1 and OTOP3 proton-activated H+ currents. They took advantage of a set of chimeras with swapped extracellular loops between OTOP3 (Zn2+-dependent potentiation) and OTOP2 (no potentiation) by neatly identifying an extracellular loop that is sufficient to confer Zn2+ potentiation. The results support the idea that within this loop resides at least part of the Zn2+ binding site, a hypothesis also confirmed by the role of a histidine residue. The authors suggested that Zn2+ potentiation of OTOP3 involves different structural elements than those required for inhibition, the conclusion that is supported by the data on the OTOP3-OTOP2 chimeras. These results shed light on a new aspect of the gating mechanism of these channels, adding an important piece to the puzzle to decipher their role in cells. This manuscript provides an important result for scientists whose research is focused on proton channels, and ion channel gating mechanisms.

Weaknesses: Although the identification of the extracellular loop represents an important result to define the structural element that confers Zn2+ potentiation to OTOP3, there are several aspects of the gating mechanism that would require a deeper analysis. The mutagenesis of the OTOP3 tm11-12 linker is very limited and does not include mutagenesis experiments in OTOP2 and OTOP1 that would further support the conclusion proposed by the authors and extend the importance of the tm11-12 linker to all the three OTOP channels (as stated in the manuscript title).<br /> Moreover, only one residue has been identified as important for Zn2+ binding. Given the three-dimensional structures of OTOP channels available to this date, particularly the chicken OTOP3 structure (PDB:6NF6), a structural analysis would certainly provide a set of putative partners for the histidine identified as the key residue for Zn2+ potentiation. Even if it is hard to understand what conformational state is represented in the structure, this analysis will provide a valid starting point to investigate the functional relevance of these residues.

Reviewer #3 (Public Review):

This work extends earlier findings from this group which showed in congenitally blind individuals preserved, presumably language-derived, representations of colour knowledge are present only in dATL. While the present study confirms the importance of language in representations in dATL, the specificity of dATL hinges on descriptive rather than inferential statistics, and future studies may be needed to demonstrate the primacy of dATL in language-based representation as well as the generalisability of effects across different flavours of conceptual knowledge.

Reviewer #3 (Public Review):<br /> <br /> In the current study, the authors present a novel and original approach (termed MINE) to analyze neuronal recordings in terms of task features. The method proposed combines the interpretability of regressor-based methods with the flexibility of convolutional neural networks and the aim is to provide an unbiased, "model-free" approach to this very important problem.

In my opinion, the authors succeed in most of these aspects. They use three datasets: an artificially-generated one that provides a ground-truth, a published dataset from wide-scale cortical mouse recordings and a novel one that studies thermosensation in larval zebrafish. MINE compares favorably in all three cases.

I believe that the paper would mostly benefit from an increased effort in clear exposition of the Taylor expansion approach, which is at the core of the method. The methods section describes the mathematics, but I wonder whether it would be possible to illustrate or schematize this in a main Figure, e.g. as an addition to Figure 1 or as a new figure. Around line 185, the manuscript reads: "We therefore perform local Taylor expansions of the network at different experimental timepoints. In other words, we differentiate the network's learned transfer function that transforms predictors into neural activity."

It would help to explicitly state with respect to what the derivative is being computed (i.e. time) and maybe a diagram (which I had to draw to understand the paper) in which a neuronal activity trace is shown and from time t onwards a prediction is computed using terms in the Taylor expansion would be very instructive (showing on an actual trace how disregarding certain terms changes the prediction and hence the conclusions about the actual dependence of the trace on the behavioral features). The formulation in terms of Jacobians and Hessians can then be restricted to the Methods section and the paper will be easier to read for a wider audience. The method is presented as a "model-free" approach (title and introduction). I think it would help to discuss this with some precision. The Taylor expansion approach does imply certain beliefs on the structure of the data (which are well founded in most cases). Do the authors agree that MINE would encapsulate any regression model where both linear and interaction terms are allowed to include an arbitrary non-linearity (in the case of the interaction terms, different non-linearities for both variables)? If this is the case, maybe an explicit statement would allow the reader to quickly identify the versatility of MINE.

I find the section relating to non-linearities interesting, but was slightly disappointed to find that the authors do not propose a single method. In Figure 3E, the authors show that a logistic regression model that combines the curvature and NLC apporaches outperforms either, but the model is not described in any sort of detail. I appreciate the attempt made by the authors to apply this to the zebrafish imaging dataset in Figure 7, but it was still unclear to me how non-linearities and complexity are related.

Reviewer #3 (Public Review):

Sarver et al., propose that TcMAC21 mice are hypermetabolic and that this is the cause of their reduced weight. Unfortunately, the developmental defects of TcMAC21 mice make this a challenging question to definitively answer. The authors claim that TcMAC21 mice are hypermetabolic due to a futile calcium cycling in skeletal muscle, which is caused by up-regulation of SLN. However, all of the data that would go into the energy balance equation (food intake, energy absorption, and energy expenditure) have been improperly analyzed. TcMAC21 pups are 8.5 g lighter than euploid littermates. The body weight data and images in Fig. 3A indicate that TcMAC21 mice runted. This difference is primarily a result of lower lean mass (FIG. 2B). This is important as it sets up many concerns that need to be addressed. Specific comments are noted below.

Specific comments:

1) It is incorrect to normalize EE to lean mass if this parameter is different between groups. Normalizing the EE data to lean mass makes it appear as though TcMAC21 mice exhibited increased EE when in fact this is a mathematical artefact. EE data should simply be plotted as ml/h (or kcal/h) per mouse. Alternatively, ANCOVA can be applied using lean mass as a covariate. Excellent reviews on this topic have been written (PMID: 20103710; PMID: 22205519).

2) It makes no sense to normalize food intake to weight, as it makes no sense to divide metabolic rate by weight as well (see above). If food intake is not normalized, this will clearly show that TcMAC21 mice eat much less than controls, and if plotted as cumulative food intake will show that TcMAC21 are smaller and gain less weight on a high-fat diet because they simply eat less. This further indicates that the major tenet of this paper is not correct.

3) The authors have tried to address the smaller weight of TcMAC21 mice by including weight-matched wild-type mice. However, they only focus on analyzing surface temperature, which is not an indicator of thermogenesis. Moreover, there is no information on whether these weight-matched wild-type mice are similar in age or body composition to the TcMAC21 mice. Nevertheless, the increased surface temperature can also indicate increased heat conservation, which is opposite to thermogenesis. It would make sense that TcMAC21 mice with massive reductions in lean mass would activate compensatory mechanisms of heat conservation to offset increased heat dissipation to the environment. This does seem to be the case, based on the data shown in Fig. 6D (see below).

4) A more optimal method of testing whether increased heat dissipation plays a role in the EE of TcMAC21 mice, is to measure EE at thermoneutrality, where energy dissipation to the environment will be minimized. Here the authors have attempted this in Fig. 6D. Unfortunately, the authors normalized EE to lean mass, artefactually elevating TcMAC21 EE. Despite this mistake, it now looks as though the large differences in EE that were seen at room temp have been attenuated, and only significantly limited to the dark phase. This indicates that in addition to the normalization artefact, higher heat dissipation from smaller TcMAC21 mice may also contribute to the elevated EE at 22C.

5) In Fig. 6D, why is the hourly plot not shown here (like 2D and 4C)? The data clearly are not as striking as the EE data at 22C?

6) GTT was similar between TcMAC21 and controls (Fig. 3I). However, the smaller insulin response could be due to the fact that glucose was normalized to body weight. It would be better to normalize to lean mass, since that is different as well, or simply give all mice the same amount of glucose that the control group receives since this is how it is done in humans.

7) The fecal energy in Fig. 4B only measures the concentration of energy per gram of feces. However, this analysis has failed to take into account total fecal excretion, which should be used to multiply the energy density of the feces. Thus, these data are incomplete and not sufficient to exclude absorption differences between the groups. And it is now curious why if all other metabolic measurements (even though wrong), such as food intake and EE are normalized to body weight, why have the authors not normalized to body weight for the feces data? Is this because if this was done this would show massive elevating in fecal energy in TcMAC21 mice and thus falsify their hypothesis?

8) I cannot find any indication of sample size in any of the EE experiments, aside from the bar graph in Fig. 6D. In any case, this experiment only an n=4 to 5 per group. This is an extremely small number for these types of experiments, so how can the authors be sure of reproducibility with such a low sample size? Are all of the other EE experiments also of similarly small sample sizes?

Reviewer #3 (Public Review):

Here, the authors aim to uncover the mechanism by which the K+ efflux channel TWIK2 contributes to activation of the canonical NLRP3 inflammasome, as a follow on from their 2018 publication identifying TWIK2 as an essential factor in ATP-induced inflammasome activation. They firstly use immunofluorescence to identify TWIK2 trafficking to the membrane following ATP challenge, and is found to colocalise with early and recycling endosomes during homeostasis. The strengths of the paper are the finding that TWIK2 localisation in cells may be altered by ATP. Biophysical investigation of membrane potential identifies extracellular Ca2+ as essential for NLRP3 activation, and the calcium-dependent small GTPase Rab11a was found to colocalise with the plasma membrane upon ATP treatment. Finally, mice harbouring Rab11a siRNA-treated macrophages were found to exhibit reduced inflammation in response to induction of sepsis, further reinforcing the potential of Rab11a targeting for novel therapeutics. However, mechanistic exploration do not provide direct evidence on TWIK2 trafficking or the involvement of Rab11a specifically with NLRP3 inflammasomes, and results with non-specific inhibitors needs to be supported by further experiments.

Reviewer #3 (Public Review):

This is a very interesting and sound work. It has been postulated that sensory neurons could optimize their information about future stimuli, but we still don't know how they can do that. This paper tackled this issue in depth with both phenomenological and mechanistic models, to understand which mechanisms could help optimize this predictive information, and show convincingly that several mechanisms can help for this.

The main limitation is that this is tested for motion at constant speed, and it would be interesting to know what happens in other cases. Also, the part about phenomenological modeling might need clarifications to understand better what really increases predictive information: it is clear the real system does it better than alternative, less realistic models, but in some cases it is not clear what is the key feature of the model.

Reviewer #3 (Public Review):

The manuscript by Hara and Kuraku addresses the question of whether some genes have a diverging gene fate (gene loss) due to underlying sequence or genomic properties. To approach this task, the authors introduce a gene loss detection pipeline that takes some previously raised technical concerns of overestimating gene loss (e.g. variations in assembly quality) into account. When applying their pipeline to >100 species, the authors report ~1,000 human genes whose orthologues were lost in multiple mammalian lineages (which they refer to as elusive genes). The study then focuses on integrating all functional evidence that can be obtained from large-scale databases for these elusive genes and test whether their genomic and evolutionary properties in the genomes of human and various other vertebrates (chimpanzee, mouse, chicken, turkey, green anole, central bearded dragon, western clawed frog, coelacanth, spotted gar, bamboo shark, whale shark) differs from the properties of the ~8,000 non-elusive genes (genes stably conserved across the compared species). In addition, the authors further analyse the human genome for the population-level variations, expression profiles and epigenetic features of elusive genes.

Overall, the study is descriptive and adds incremental evidence to an existing body of extensive gene loss literature. The topic is specialised and will be of interest to a niche audience. The text is highly redundant, repeating the same false positive issue in the introduction, methods, and discussion sections, while no clear conclusion or interpretation of their main findings are presented.

Major comments

- While some of the false discovery rate issues of gene loss detection were addressed in the presented pipeline, the authors fail to test one of the most severe cases of mis-annotating gene loss events: frameshift mutations which cause gene annotation pipelines to fail reporting these genes in the first place. Running a blastx or diamond blastx search of their elusive and non-elusive gene sets against all other genomes, should further enlighten the robustness of their gene loss detection approach

- Along this line, we noticed that when annotation files were pooled together via CD-Hit clustering, a 100% identity threshold was chosen (Methods). Since some of the pooled annotations were drawn from less high quality assemblies which yield higher likelihoods of mismatches between annotations, enforcing a 100% identity threshold will artificially remove genes due to this strict constraint. It will be paramount for this study to test the robustness of their findings when 90% and 95% identity thresholds were selected.

- While some statistical tests were applied (although we do recommend consulting a professional statistician, since some identical distributions tend to show significantly low p-values), the authors fail to discuss the fact that their elusive gene set comprises of ~5% of all human genes (assuming 21,000 genes), while their non-elusive set represents ~40% of all genes. In other words, the authors compare their sequence and genomic features against the genomic background rather than a biological signal (non-elusiveness). An analysis whereby 1,081 genes (same number as elusive set) are randomly sampled from the 21,000 gene pool is compared against the elusive and non-elusive distributions for all presented results will reveal whether the non-elusive set follows a background distribution (noise) or not.

- We also wondered whether the authors considered testing the links between recombination rate / LD and the genomic locations of their elusive genes (again compared against randomly sampled genes)?

- Given the evidence presented in Figure 6b, we do not agree with the statement (l.334-336): "These observations suggest that the elusive genes are unlikely to be regulated by distant regulatory elements". Here, a data population of ~1k genes is compared against a data population of ~8k genes and the presented difference between distributions could be a sample size artefact. We strongly recommend retesting this result with the ~1k randomly sampled genes from the total ~21,000 gene pool and then compare the distributions.

- Analogous random sampling analysis should be performed for Fig 6a,d

- We didn't see a clear pattern in Figure 7. Please quantify enrichments with statistical tests. Even if there are enriched regions, why did the authors choose a Shannon entropy cutoff configuration of <1 (low) and >1 (high)? What was the overall entropy value range? If the maximum entropy value was 10 or 100 or even more, then denoting <1 as low and >1 as high seems rather biased.

Reviewer #3 (Public Review):

In the present study by Boyle et al., the function of NPY expressing spinal neurons in pain and itch perception is studied. While the function of these neurons has been addressed previously, the difference to previous studies is the combinatorial use of AAV encoded effectors and cre transgenic mice whereas previous studies relied on cre transgenic mice and reporter mice encoding the effector or only viruses. Boyle at al. demonstrate that their strategy enabled them to restrict the analysis to only those neurons expressing NPY in the adult mouse compared to a more heterogenous population that had been studied before. By using a combination of morphology, electrophysiology and behavioral paradigms they convincingly show that NPY neurons impact pruritoception via inhibiting GRPR neurons. Furthermore, they indicate a role of NPY neurons also in nociception as activation attenuates not only responses to acute nociceptive stimuli but also blocks inflammation or nerve injury induced mechanical and heat hypersensitivity. Selectively activating NPY neurons in vivo may therefore be a promising strategy to treat neuropathic pain.

The result of this study extends and partially contrasts previous studies. The authors argue that contrasting results may be due to the different experimental strategies (e.g. only neurons expressing NPY adult in the present study versus a more heterogeneous population before).

Overall, the experiments are convincing, and the quality of the data/figures is exceptionally high.

Reviewer #3 (Public Review):

The authors study monolayers of MDCK cells on curved surfaces. These surfaces consist of hemicylindrical valleys and hills obtained through microfabrication involving glass rods and repeated molding steps. They find higher apoptotic extrusion rates in valleys compared to hills for patterns with 25 and 50 µm curvature radii, but not in valleys of 100 µm curvature radius. By using osmotic shocks and reflection interference contrast microscopy, they identify hydraulic stress to drive cell extrusion. 3D force microscopy reveals that cytoskeletal forces point towards the substrate on hills and away from the substrate in valleys. From these observations, the authors conclude that hydraulic stress-induced cell extrusion is assisted by cytoskeletal forces in the valleys and opposed on the hills. Finally, they link the hydraulic stress to the activity of focal adhesion kinase, which in turn affects cell survival through Akt signaling.

Strengths:

This work combines a new microfabrication method with state of the art 3d force microscopy that allows the authors to study curvature-dependent cell extrusion. The application of various osmotic shocks to the system clearly identifies the role of hydraulic stress in cell extrusion. The decoupling of the main driver of cell extrusion (hydraulic stress) from its curvature-dependent modulation through cytoskeletal forces, together with the mechanical activation of apoptosis is an important new finding that significantly advances our understanding of epithelial cell extrusion and could be important during developmental processes and for maintaining intact epithelia in adult organisms.

Weaknesses:

The main weakness of this work is a lack of quantification of the hydraulic stress. Furthermore, the authors do not present data on other cell types such that the phenomenon studied in this work might be specific to MDCK cells. Finally, The authors do not modify cytoskeleton contractility to check how this parameter affects the threshold curvature below which cell extrusion is no longer curvature dependent.

Reviewer #3 (Public Review):

This study shows for the first time changes in palladin expression under disease conditions and mRNA alterations in human samples. The authors have identified novel binding partners for the protein as a first step toward determining how palladin mediates its effects in the heart. Finally, through the use of mouse models to decrease palladin expression they identify a crucial role for palladin in the cardiac response to pathological stress, with some interesting findings that show the effects of palladin depend on when the protein is altered.

The novel findings of the study are supported by the data presented, but there are several instances where clarification is needed of the conclusions drawn from the data reach beyond what is presented in the Results section.

The focus on only male mice is a significant limitation of the paper, as it is well known that there are profound sex differences in the response to pathological stressors. While the ability to obtain sufficient heart samples from male and female patients may be a reasonable justification for focusing on males, the preclinical mouse model should have been examined in both sexes and the limitation of this choice should be clearly noted in the paper.

The changes in myopalladin expression were not measured in the disease model (TAC), which limits the ability to determine if myopalladin was altered in the disease state. This addition would strengthen the study.

Finally, the myofilament data are presented as evidence that changes in the contractile apparatus are contributors to the observed contractile dysfunction at the organ level. But these studies were conducted using levels of calcium that far exceed what is seen in vivo and, therefore, do not support the conclusion drawn.

Reviewer #3 (Public Review):

The ability of T cells to move through a variety of complex and disparate tissue environments is fundamental to their success in surveying and responding to infectious challenges. A better understanding of the molecular cues that regulate T cell motility in tissues is needed in order to inform therapeutic targeting of T cell migration. Contributions that are intrinsic and extrinsic to the T cells themselves have been shown to shape the pattern of T cell movement. This study uses advanced quantitative image analysis tools to dissect differences in T cell motility in different tissue locations, to better define how the tissue environment shapes the pattern of motility and scope of tissue explored. The combination of different quantitative measures of motion enables the extensive characterization of CD8 T cell motility in the lymph node, lung, and villi of the small intestine. However, there are too many variables with respect to the CD8 T cell populations used for analysis to be able to gain new insight into the impact of the tissue microenvironment itself.

The use of these advanced quantitative imaging analysis tools has the potential to significantly expand our analysis capabilities of T cell movement within and across tissues. The strength of the paper is the comprehensive analysis of multiple motility parameters designed with T cell function in mind. Specifically, with respect to the need for T cells to search a tissue area to identify antigen-bearing cells for T cell activation and identify cellular targets for the delivery of anti-microbial effector functions. The inclusion of an analysis of the "patrolled volume per time" is seen as a particularly useful advance to compare T cell behaviors across tissues.

However, with the current data sets, it is difficult to draw definitive conclusions on the impact of the tissue environment on how T cell move, given the considerable variability in the CD8 T cells themselves. Extended experimentation would be needed to fully support their key claims. In particular:

1) The authors have separated out naïve and activated CD8 T cells for their analysis, but this is a marked over-simplification. There are too many variables within these groups to be able to distinguish between differences in the T cell populations versus differences in the tissue environment. Variables include:<br /> a) T cells pre-activated in vitro before in vivo transfer (LPS-lung) versus transfer of naïve T cells for activation in vivo (Flu-lung, LCMV-villi)<br /> b) Polyclonal CD8 T cells (naïve, LPS-lung, Flu-lung) versus monoclonal (P14) CD8 T cells (LCMV-villi)<br /> c) Presence of cognate-antigen (Flu-lung, LCMV-villi) versus absence of antigen (LPS-lung)<br /> d) Cell numbers, 104 polyclonal naïve for Flu-lung versus 5 x 104 monoclonal (P14 T cells) for LCMV-villi)<br /> e) Intravital imaging (LCMV-villi) versus tissue explants (Flu-lung)

The authors do present data that suggest similarities of motility patterns within the same tissue occur despite variabilities in the CD8 T cell source, for example, the MSD is not significantly different in the two lung groups despite differences in the way the CD8 T cells were activated. However, these similarities are lost when other parameters are analyzed suggesting additional variability independent of the tissue itself.

2) Controlled experiments are needed, where the input CD8 T cell population is kept constant and the target tissue differs, to substantiate any of the current conclusions. This could be done by using a single source and/or specificity of CD8 T cells (e.g., P14 or OT-I TCR transgenics, or polyclonal in vitro activated CD8 T cells) transferred into mice where the tissue providing the antigen or inflammation source is varied (lung with pOVA-flu versus small intestine with pOVA-LCMV for example).

Alternatively, activated polyclonal CD8 T cells could be analyzed in the LPS-lung draining LN as well as in the LPS-lung to make a direct comparison between the tissues (LN versus lung) using CD8 T cells of the same activation status.

3) Differences in the micro-anatomical regions of the tissues studied may also contribute to tissue differences in movement patterns between the lung and the small intestine. The region of the small intestine imaged was specifically focused on the villi, close to the gut epithelium. Details of the location within the lung where images were taken are missing, therefore the motility differences between the lung and small intestine could reflect differences in the micro-anatomical position of the CD8 T cells within the tissue (proximal to epithelium versus parenchymal), rather than differences between the tissues themselves.

Overall, the authors have developed a quantitative multi-parameter approach to the study of T-cell motility in different tissues. Application of these analytical tools to the study of T-cell behavior in different tissue locations has the potential to reveal tissue and/or T-cell-specific patterns of movement that may help to identify molecular requirements for context-specific dynamic T-cell behavior. Their quantitative approach reveals small but statistically significant differences in particular motility parameters, the functional significance of which will require further study. The careful design of experiments to reduce as many variables as possible will be needed to increase the impact of the work and ensure new insights into this important aspect of T-cell function.

Reviewer #3 (Public Review):

In this work, the authors have built a framework for the annotation of interactions between species. The framework includes ontologies, methodologies, and an annotation tool called PHI-Canto. The framework makes use of multiple existing ontologies that are in wide use in the biocuration community. In addition, the authors have built their own project-specific controlled vocabularies and ontologies for the capture of pathogen-host interaction phenotypes (PHIPO), diseases (PHIDO), and environmental conditions (PHI-ECO). Their work builds on and extends methods that have been developed within the Gene Ontology Consortium and model organism databases. The tool PHI-Canto is an extension of the tool Canto developed by PomBase for curation. The authors used this framework to annotate pathogen-host interactions within the Pathogen-Host Interactions Database.

Strengths: The manuscript is well-written and includes significant detail regarding curation policies/methods and the use of the actual PHI-Canto tool. The appendices are very detailed and provide useful illustrations of the annotation practices and tool interface. The work has built upon and extended well-established standards and methods that have proven their utility over many years of use in the biocuration community. The authors have rigorously tested their framework with the curation of a variety of publications providing a diverse assortment of annotation challenges. The concept of a "metagenotype" is important and providing such a structured system for the capture of this information is useful. All of the materials produced by the work are completely freely available for use by the wider community.

Weaknesses: There are some areas of the manuscript and appendices which are a bit confusing and could be improved. The authors have developed their own set of disease terms (PHIDO) but do not comment on why existing disease terminologies (such as Mondo or DO) were not used or if the PHIDO terms relate to those other vocabularies. There is no discussion of the possible use of a graph representation for the capture of this complex information (which is being done in many settings including the Gene Ontology with GO Causal Activity Models (GO-CAMs)) or why such a structure was not used. Although the abstract talks about the use of the framework within the PHI database as a test case for broader use regarding interspecies interactions, there is no mention of extending the use of the tool to other species interaction communities beyond pathogen-host interactions.

Reviewer #3 (Public Review):

Eyraud and colleagues examine how fibrocytes and CD8 cells can interact with each other to promote COPD. The key findings include that CD8 cells and fibrocytes are found to exist in close proximity to each other in COPD lungs using histopathological analysis of patient samples. The authors leverage pre-existing transcriptomic data on CD8 cells to focus on chemokine release by CD8 cells as a potential pathogenic mechanism by which they could affect fibrocyte migration. In vitro studies using peripheral blood-derived CD8 cells and fibrocytes confirm increased fibrocyte migration in the presence of CD8 cells. as drivers of COPD progression. Conversely, in vitro studies show that fibrocytes exert a pro-proliferative effect on CD8 cells. The authors also use a computational model to assess how these interactions could promote the development of fibrocyte-CD8 clusters as COPD progresses over the course of 20 years.

The strengths of the study include:

1) The multi-faceted research approach that integrates histopathology from clinical COPD lung sections, in vitro co-culture studies, and computational modeling.

2) Applying computational modeling to determine how cell-cell interactions of migration and proliferation can result in distribution patterns within the lung that approximate what is found in actual clinical samples

3) Propose a feedback loop of CD8 cells and fibrocytes that could become a potential therapeutic target to interrupt a vicious cycle that promotes COPD.

However, there are also some weaknesses:

1) Specificity of the role of CD8 cells: While much of the focus is on the proximity of and interactions between CD8 cells and fibrocytes, it is not clear whether other cells similarly interact with fibrocytes. For example, CD4 cells, dendritic cells, or interstitial macrophages may similarly interact with fibrocytes as several of these also release chemokines. In the absence of a more comprehensive assessment, it becomes difficult to parse out how specific and relevant the fibrocyte-CD8 cell interactions are for COPD progression when compared to other putative interactions.

2) The transcriptomic analysis which in many ways sets the stage for the chemokine studies uses a pre-existing dataset of COPD and non-COPD samples with only n=2. The robustness of such a sample size is limited and the narrow focus on chemokines or adhesion receptors of CD8 cells in this limited sample size does not provide a more comprehensive analysis that would require larger samples sizes, studying the transcriptomes of other cell types and a broader analysis of which pathways are the most likely to be dysregulated in the cells that surround fibrocytes.

3) Specificity of the findings for COPD: The in vitro studies use circulating cells which are different from lung cells and this is appropriately acknowledged by the authors. However, it appears from the description that the cells are all from COPD patients. It is therefore not clear whether these interactions between fibrocytes and CD8 cells are unique to COPD, whether they also occur between control CD8 and fibrocytes, or only in cells obtained from patients with inflammatory/pulmonary diseases.

Reviewer #3 (Public Review):

Laure Olazcuaga et al. investigated the metabolomes of four fruit-based diets and corresponding individuals of Drosophila suzukii that reared on them using comparative metabolomics analysis. They observed that the four fruit-based diets are metabolically dissimilar. On the contrary, flies that fed on them are mostly similar in their metabolic response. From a quantitative point of view, they find that part of the fly metabolomes correlates well with that of the corresponding diet metabolomes, which is indicative of insect ingestive history. By further focusing on 71 metabolites derived from diet-specific fly ions and highly abundant fruit ions, the authors show that D. suzukii differentially accumulates diet metabolism in a compound-specific manner. The authors claim that the data support the metabolic generalism hypothesis while rejecting the multi-host metabolic specialism hypothesis. This study provides a valuable global chemical comparison of how diverse diet metabolites are processed by a generalist insect species.

Strengths:<br /> The rapid advances in high-resolution mass spectrometry have recently accelerated the discovery of many novel post-ingestive compounds through comparative metabolomics analysis of insect/frass and plant samples. Untargeted metabolomics is thus a very powerful approach for the systematic comparison of global chemical shifts when diverse plant-derived specialized metabolites are further modified or quantitatively metabolized after ingestion by insects. The technique can be readily extended to a larger micro- or macro-evolutionary context for both generalist and specialist insects to systematically investigate how plant chemical diversity contributes to dietary generalism and specialism.

Weaknesses:<br /> The authors claim that their data support the hypothesis of metabolic generalism, however, a total analysis of insect metabolism may not generate a clean dataset for direct comparison of fruit-derived metabolites with those metabolized by D. suzukii, given that much of these metabolites would be "diluted" proportionally by insect-derived metabolites. If the insect-derived metabolites predominate, then, as the authors observed, a tight clustering of D. suzukii metabolomes in the PCA plot would be expected. It is therefore very difficult to interpret these patterns.

The authors generated a qualitative dataset using the peak list produced by XCMS which contains quantitative peak areas, it is unclear how the threshold was selected to determine if a peak is present or absent in a given sample. The qualitative dataset would influence the output of their data analysis.

The authors reply on in-source fragmentation for peak annotation when authentic standards are not available. The accuracy of the annotation thus requires further validation.

Reviewer #3 (Public Review):

Gaze-stabilizing motor coordination and the resulting patterns of retinal image flow are computed from empirically recorded eye movement and motion capture data. These patterns are assessed in terms of the information that would be potentially useful for guiding locomotion that the retinal signals actually yield. (As opposed to the "ecological" information in the optic array, defined as independent of a particular sensor and sampling strategy).

While the question posed is fundamental, and the concept of the methodology shows promise, there are some methodological details to resolve. Also, some terminological ambiguities remain, which are the legacy of the field not having settled on a standardized meaning for several technical terms that would be consistent across laboratory setups and field experiments.

Technical limits and potential error sources should be discussed more. Additional ideas about how to extend/scale up the approach to tasks with more complex scenes, higher speed, or other additional task demands and what that might reveal beyond the present results could be discussed.

Reviewer #3 (Public Review):

In empirical data, the dependence of microbial diversity on environmental temperature can take multiple different functional forms, while the previous theory has not established a clear understanding of when the temperature-dependence of diversity should take a particular form, and why. The authors seek to understand what forms are possible, and when they will occur, via analysis of the feasibility (i.e. positivity) of Lotka-Volterra equation solutions. This is combined with an assumption for the way that species' growth rates depend on temperature, along with an assumption for the way species interaction rates depend on temperature. Together, this completely specifies the form of the Lotka-Volterra equations, and whether all species in the model can coexist indefinitely at a given temperature, or whether only a lower-diversity subset can persist.

The overall goal is valuable, and the overall approach of using this classic model of species interactions is justifiable. My main question marks relate to the way the conditions on feasibility (i.e. when all species will have positive equilibria), whether and when we need to consider the stability of these feasible solutions, and finally how general the way in which model parameters are specified to depend on temperature. I will expand on these three issues below. A more minor issue is that the authors set up this problem with extensive reference to the interaction of consumers and resources, referencing previous approaches that explicitly model these. Since resources are not explicitly present in the Lotka-Volterra formalism, it would be helpful to have a clearer justification for the authors' rationale in choosing this kind of model.

(1) Conditions on growth and interaction rates for feasibility and stability. The authors approach this using a mean field approximation, and it is important to note that there is no particular temperature dependence assumed here: as far as it goes, this analysis is completely general for arbitrary Lotka-Volterra interactions.

However, the starting point for the authors' mean field analysis is the statement that "it is not possible to meaningfully link the structure of species interactions to the exact closed-form analytical solution for [equilibria] 𝑥^*_𝑖 in the Lotka-Volterra model.

I may be misunderstanding, but I don't agree with this statement. The time-independent equilibrium solution with all species present (i.e. at non-zero abundances) takes the form

x^* = A^{-1}r

where A is the inverse of the community matrix, and r is the vector of growth rates. The exceptions to this would be when one or more species has abundance = 0, or A is not invertible. I don't think the authors intended to tackle either of these cases, but maybe I am misunderstanding that.

So to me, the difficulty here is not in writing a closed-form solution for the equilibrium x^*, it is in writing the inverse matrix as a nice function of the entries of the matrix A itself, which is where the authors want to get to. In this light, it looks to me like the condition for feasibility (i.e. that all x^* are positive, which is necessary for an ecologically-interpretable solution) is maybe an approximation for the inverse of A---perhaps valid when off-diagonal entries are small. A weakness then for me was in understanding the range of validity of this approximation, and whether it still holds when off-diagonal entries of A (i.e. inter-specific interactions) are arbitrarily large. I could not tell from the simulation runs whether this full range of off-diagonal values was tested.

As a secondary issue here, it would have been helpful to understand whether the authors' feasible solutions are always stable to small perturbations. In general, I would expect this to be an additional criterion needed to understand diversity, though as the authors point out there are certain broad classes of solutions where feasibility implies stability.

(2) I did not follow the precise rationale for selecting the temperature dependence of growth rate and interaction rates, or how the latter could be tested with empirical data, though I do think that in principle this could be a valuable way to understand the role of temperature dependence in the Lotka-Volterra equations.

First, as the authors note, "the temperature dependence of resource supply will undoubtedly be an important factor in microbial communities"

Even though resources aren't explicitly modeled here, this suggests to me that at some temperatures, resource supply will be sufficiently low for some species that their growth rates will become negative. For example, if temperature dependence is such that the limiting resource for a given species becomes too low to balance its maintenance costs (and hence mortality rate), it seems that the net growth rate will be negative. The alternative would be that temperature affects resource availability, but never such that a limiting resource leads to a negative growth rate when a taxon is rare.

On the other hand, the functional form for the distribution of growth rates (eq 3) seems to imply that growth rates are always positive. I could imagine that this is a good description of microbial populations in a setting where the resource supply rate is controlled independently of temperature, but it wasn't clear how generally this would hold.

Secondly, while I understand that the growth rate in the exponential phase for a single population can be measured to high precision in the lab as a function of temperature, the assumption for the form of the interaction rates' dependence on temperature seems very hard to test using empirical data. In the section starting L193, the authors seem to fit the model parameters using growth rate dependence on temperature, but then assume that it is reasonable to "use the same thermal response for growth rates and interactions". I did not follow this, and I think a weakness here is in not providing clear evidence that the functional form assumed in Equation (4) actually holds.

Reviewer #3 (Public Review):

The manuscript entitled "Osteoblast-intrinsic defect in glucose metabolism impairs bone formation in type II diabetic mice" by Song et al. showed that osteoblast activity was compromised due to impaired glucose metabolism using a youth-onset T2D mouse model. The investigators induced youth-onset T2D in 22-week-old C57BL/6J male mice by a high-fat diet (HFD) starting at 6 weeks of age and injection of low-dose streptozotocin three times at 12-week-old. Then they demonstrated that metformin promoted glycolysis and osteoblast differentiation in vitro and increased bone mass in the diabetic mice. It was also demonstrated that targeted overexpression of Hif1a or Pfkfb3, but not Glut1, in osteoblasts reduced bone loss in T2D mice. Overall, the investigators made a great effort to characterize the changes in metabolism in the bone of the B6/C57 mice by HFD and metformin with microCT, dynamic histomorphometry, C13 isotype labeling in vivo, scRNA-seq and metabolic assays with bone marrow mesenchymal cells in vitro.

Reviewer #3 (Public Review):

WDR62 is a spindle pole-associated scaffold protein. Recessive mutations in WDR62 account for the second most common cause of autosomal recessive primary microcephaly (MCPH). This paper investigates how a C-terminal truncating mutation D955AfsX112 in WDR62 causes MCPH using iPSCs from a patient. The authors generated neuroepithelial (NES) cells, cortical progenitors, and neurons from the patient-derived and isogenic retro-mutated iPSC lines. They found that: (1) the mutant WDR62 fails to localize to the spindle poles during mitosis; (2) patient-derived iPS-NES cells exhibit shorter primary cilia and significantly smaller spindle angles; (3) the mutation leads to differentiation defects in iPSC-derived cortical neurons; (4) during the interphase-to-mitosis transition, WDR62 translocates from the Golgi apparatus to the spindle poles in a microtubule-dependent manner; and (5) the mutation prevents WDR62 shuttling from the Golgi to the spindle poles. Using the isogenic retro-mutated iPSC lines as the control increased the rigor of the current study. In general, this is a very carefully designed study, the data support the authors' conclusions, and confirm previous findings of WDR62 functions.

Reviewer #3 (Public Review):

In "Lifelong regeneration of cerebellar Purkinje neurons after induced cell ablation in zebrafish" by Pose-Mendez and colleagues, the authors followed the regenerative properties that Purkinje cells have in larvae and adult Zebrafish. These properties common in teleostean and other animals are rare in mammals and, therefore, their study is of great interest to the neurodevelopmental community.

In this work, the authors use an already established animal model (PC-ATTACTM) to selectively ablate Purkinje cells in the larvae and adult Zebrafish, in a temporal control manner, that is by administering 4-OHT at defined stages. In doing so, the authors show that a full recovery of an ablated Purkinje cell population can be achieved when the ablation is induced in the larval stage, but this recovery is more modest when the ablation is induced in the adult stage, albeit very significant. The authors also show that regenerated Purkinje cells quickly elaborate their native electrical properties and integrate into functional circuits, which allow for the recuperation of motor behaviors produced by the loss of ablated Purkinje cells.

Overall, the work by Pose-Mendez and colleagues contributes to our understanding of neuronal regeneration in non-mammals. Technically, this study is well conducted and the provided data support most of the conclusions made by the authors.

Reviewer #3 (Public Review):<br /> <br /> Gonzalez and colleagues investigate dopamine signals in response to visual stimuli. This work builds on the longstanding notion that dopamine neurons respond to unexpected sensory stimuli, including visual cues. Using fiber photometry measurements of a fluorescent dopamine sensor, they find that in the lateral ventral striatum, dopamine signals reliably report salient transitions in illuminance. Dopamine signals scale with light intensity and the speed of illuminance changes. They further find that the frequency of illuminance transitions, rather than the number, dictates the extent that dopamine signals habituate. In a number of studies, they characterize dopamine signals to light of different wavelengths, durations, and intensities. These results shed new "light" on the role of dopamine in signaling salience, independent of reward or threat learning. This work is elegantly done and compelling. While the results are potentially specific to this region of the striatum, rather than a broad dopaminergic profile of visual stimulus encoding, this work offers valuable insight into dopamine function, as well as a practical guide and considerations for the implementation of visual stimuli in behavioral tasks that assay dopamine systems.

Reviewer #3 (Public Review):

This manuscript by Sano et al., presents cryo-EM structure of endothelin-1-bound endothelin B receptor (ETbR) in complex with heterotrimeric G-proteins. The structural snapshot provides important information about agonist-induced receptor activation and transducer-coupling. This manuscript also designs and present a successful case example for a variation of previously used NanoBiT-fusion-based strategy to stabilize GPCR-G-protein complexes. This strategy may be broadly applicable to other GPCR-G-protein complexes as well, and therefore, also provides an important methodological advance. Overall, the experimental design and interpretation of the structure are excellent, and the manuscript present an easy-to-follow coherent story. Considering the importance of ETbR signaling in multiple physiological and disease conditions, this structural snapshot, taken together with earlier structural studies by the same laboratory, advances the ETbR biology significantly with potential for novel ligand discovery. This manuscript is also available as a preprint in bioRxiv as well as another manuscript from Xu and Jiang group. Considering the structural information presented in these manuscripts, I would strongly suggest that even if the other manuscript is published somewhere before this one, it should not be viewed as a compromise on novelty, and rather considered as complementary information from independent studies that further strengthen the impact.

Reviewer #3 (Public Review):

The study focuses on a compelling question focusing on a largely indispensable mechanism, ribonucleotide reduction. The authors generate a unique specific bacterial strain where the ribonucleotide reducatase operon, entirely, is deleted. They grow the mutant strain in environments that have various amounts of the necessary deoxyribonucleoside levels, further, they perform evolution experiments to see whether and how the evolved lines would be able to adapt to the limited deoxyribonucleosides. Finally, researchers identify key mutations and generate key isogenic genetic constructs where target mutants are deleted. A summary postulation based on the evolutionary trajectory of ribonucleotide reduction by bacteria is presented. Overall, the study is well presented, well-justified, and builds on fairly classic genetic and evolution experiments. The select question and hypotheses and the overall framing of the story are fairly novel for the respective communities. The results should be interesting to evolutionary biology researchers, especially those interested in RNA>DNA directional evolution, as well as molecular microbiologists interested in the ribonucleotide reception dependence and selection by the environment. A discussion on the limitations of the laboratory study for the broader understanding of the host dependence during endosymbiosis and parasitism would be a good addition given the emphasis on this phenomenon as a part of the broader impacts of the study.

Reviewer #3 (Public Review):

Shen et al. attempt to reconcile two distinct features of neural responses in frontoparietal areas during perceptual and value-guided decision-making into a single biologically realistic circuit model. First, previous work has demonstrated that value coding in the parietal cortex is relative (dependent on the value of all available choice options) and that this feature can be explained by divisive normalization, implemented using adaptive gain control in a recurrently connected circuit model (Louie et al, 2011). Second, a wealth of previous studies on perceptual decision-making (Gold & Shadlen 2007) have provided strong evidence that competitive winner-take-all dynamics implemented through recurrent dynamics characterized by mutual inhibition (Wang 2008) can account for categorical choice coding. The authors propose a circuit model whose key feature is the flexible gating of 'disinhibition', which captures both types of computation - divisive normalization and winner-take-all competition. The model is qualitatively able to explain the 'early' transients in parietal neural responses, which show signatures of divisive normalization indicating a relative value code, persistent activity during delay periods, and 'late' accumulation-to-bound type categorical responses prior to the report of choice/action onset.

The attempt to integrate these two sets of findings by a unified circuit model is certainly interesting and would be useful to those who seek a tighter link between biologically realistic recurrent neural network models and neural recordings. I also appreciate the effort undertaken by the authors in using analytical tools to gain an understanding of the underlying dynamical mechanism of the proposed model. However, I have two major concerns. First, the manuscript in its current form lacks sufficient clarity, specifically in how some of the key parameters of the model are supposed to be interpreted (see point 1 below). Second, the authors overlook important previous work that is closely related to the ideas that are being presented in this paper (see point 2 below).

1) The behavior of the proposed model is critically dependent on a single parameter 'beta' whose value, the authors claim, controls the switch from value-coding to choice-coding. However, the precise definition/interpretation of 'beta' seems inconsistent in different parts of the text. I elaborate on this issue in sub-points (1a-b) below:

1a). For instance, in the equations of the main text (Equations 1-3), 'beta' is used to denote the coupling from the excitatory units (R) to the disinhibitory units (D) in Equations 1-3. However, in the main figures (Fig 2) and in the methods (Equation 5-8), 'beta' is instead used to refer to the coupling between the disinhibitory (D) and the inhibitory gain control units (G). Based on my reading of the text (and the predominant definition used by the authors themselves in the main figures and the methods), it seems that 'beta' should be the coupling between the D and G units.

1b). A more general and critical issue is the failure to clearly specify whether this coupling of D-G units (parameterized by 'beta') should be interpreted as a 'functional' one, or an 'anatomical' one. A straightforward interpretation of the model equations (Equations 5-8) suggests that 'beta' is the synaptic weight (anatomical coupling) between the D and G units/populations. However, significant portions of the text seem to indicate otherwise (i.e a 'functional' coupling). I elaborate on this in subpoints (i-iii) below:

(1b-i). One of the main claims of the paper is that the value of 'beta' is under 'external' top-down control (Figure 2 caption, lines 124-126). When 'beta' equals zero, the model is consistent with the previous DNM model (dynamic normalization, Louie et al 2011), but for moderate/large non-zero values of 'beta', the network exhibits WTA dynamics. If 'beta' is indeed the anatomical coupling between D and G (as suggested by the equations of the model), then, are we to interpret that the synaptic weight between D-G is changed by the top-down control signal within a trial? My understanding of the text suggests that this is not in fact the case. Instead, the authors seem to want to convey that top-down input "functionally" gates the activity of D units. When the top-down control signal is "off", the disinhibitory units (D) are "effectively absent" (i.e their activity is clamped at zero as in the schematic in Fig 2B), and therefore do not drive the G units. This would in-turn be equivalent to there being no "anatomical coupling" between D and G. However when the top-down signal is "on", D units have non-zero activity (schematic in Fig 2B), and therefore drive the G units, ultimately resulting in WTA-like dynamics.

(1b-ii). Therefore, it seems like when the authors say that beta equals zero during the value coding phase they are almost certainly referring to a functional coupling from D to G, or else it would be inconsistent with their other claim that the proposed model flexibly reconfigures dynamics only through a single top-down input but without a change to the circuit architecture (reiterated in lines 398-399, 442-444, 544-546, 557-558, 579-590). However, such a 'functional' definition of 'beta' would seem inconsistent with how it should actually be interpreted based on the model equations, and also somewhat misleading considering the claim that the proposed network is a biologically realistic circuit model.

(1b-iii). The only way to reconcile the results with an 'anatomical' interpretation of 'beta' is if there is a way to clamp the values of the 'D' units to zero when the top-down control signal is 'off'. Considering that the D units also integrate feed-forward inputs from the excitatory R units (Fig 2, Equations 1-3 or 5-8), this can be achieved either via a non-linearity, or if the top-down control input multiplicatively gates the synapse (consistent with the argument made in lines 115-116 and 585-586 that this top-down control signal is 'neuromodulatory' in nature). Neither of these two scenarios seems to be consistent with the basic definition of the model (Equations 1-3), which therefore confirms my suspicion that the interpretation of 'beta' being used in the text is more consistent with a 'functional' coupling from D to G.

2) The main contribution of the manuscript is to integrate the characteristics of the dynamic normalization model (Louie et al, 2011) and the winner-take-all behavior of recurrent circuit models that employ mutual inhibition (Wang, 2008), into a circuit motif that can flexibly switch between these two computations. The main ingredient for achieving this seems to be the dynamical 'gating' of the disinhibition, which produces a switch in the dynamics, from point-attractor-like 'stable' dynamics during value coding to saddle-point-like 'unstable' dynamics during categorical choice coding. While the specific use of disinhibition to switch between these two computations is new, the authors fail to cite previous work that has explored similar ideas that are closely related to the results being presented in their study. It would be very useful if the authors can elaborate on the relationship between their work and some of these previous studies. I elaborate on this point in (a-b) below:

2a) While the authors may be correct in claiming that RNM models based on mutual inhibition are incapable of relative value coding, it has already been shown previously that RNM models characterized by mutual inhibition can be flexibly reconfigured to produce dynamical regimes other than those that just support WTA competition (Machens, Romo & Brody, 2005). Similar to the behavior of the proposed model (Fig 9), the model by Machens and colleagues can flexibly switch between point-attractor dynamics (during stimulus encoding), line-attractor dynamics (during working memory), and saddle-point dynamics (during categorical choice) depending on the task epoch. It achieves this via a flexible reconfiguration of the external inputs to the RNM. Therefore, the authors should acknowledge that the mechanism they propose may just be one of many potential ways in which a single circuit motif is reconfigured to produce different task dynamics. This also brings into question their claim that the type of persistent activity produced by the model is "novel", which I don't believe it is (see Machens et al 2005 for the same line-attractor-based mechanism for working memory)

2b) The authors also fail to cite or describe their work in relation to previous work that has used disinhibition-based circuit motifs to achieve all 3 proposed functions of their model - (i) divisive normalization (Litwin-Kumar et al, 2016), (ii) flexible gating/decision making (Yang et al, 2016), and working memory maintenance (Kim & Sejnowski,2021)

Reviewer #3 (Public Review):

This work dives into the inner molecular workings of viruses such as yellow fever, Zika, and tick borne encephalitis. Due to their pathogenic nature, these are active targets for drug development, and motivated by this, the authors set out to search for so-called "cryptic" binding pockets, concealed from the protein surface and therefore often missed. Using atomistic computer simulations of viral rafts embedded in lipid membranes, the authors present new methodology to detect and characterise structural and electrostatic features of viral envelope proteins. By mixing in a small organic co-solvent (benzene) that acts as a drug proxy, structural fluctuations are enhanced, which reveal hitherto hidden binding pockets. The authors convincingly show that this perturbation has only a minute effect on protein secondary structure. The technique revealed a new cryptic binding pocket that is well conserved across multiple flaviviruses.

The cryptic site involves four potentially charged residues and to understand their interplay, constant pH molecular dynamics simulations are combined with a detailed structural and electrostatic analysis of the binding pocket.<br /> Due it's multi-dimensional nature, the response to a possible pH change is a complex process and the authors present a compelling analysis involving charge states, inter-residue distances (reduced using PCA), and structural features of the pocket. An important conclusion is that the role of histidine is less important than previously thought: the pH dependent behaviour is a collective property of the pocket.

This study is an important contribution to computer aided drug-design. In particular, using co-solutes to induce structural fluctuations seems very helpful for uncovering new binding sites. Of equal importance are methodology to analyse complex trajectories. This work is a good example of how multiple dimensions can be reduced and rationalised using e.g. solvent accessibly surface area (SASA), radius of gyration, net-charge, and principal component analysis. There are likely several other properties that could aid in this rationalising and the present work is a solid platform for exploring these.

Reviewer #3 (Public Review):

Rodriguez et al. develop a nonlinear ordinary differential equation model of hematopoiesis under normal and chronic myeloid leukaemia (CML) conditions, incorporating feedback control, lineage branching, and signaling between normal and CML cells. Design space analysis is used to identify viable models of cell-cell signalling interaction. Data from mouse models are used to refine the set of cell-cell interactions considered viable, resulting in a novel feedback-feedforward model. Through this framework, the response to tyrosine kinase inhibitor (TKI) therapy is analysed. Model behaviour is qualitatively consistent with experimental data from mouse models, and clinical data. In particular, the model demonstrates varying responses to tyrosine kinase inhibitor therapy across a range of parameter sets consistent with "normal" hematopoietic cell counts; and predicts that a relatively high proportion of leukemic hematopoietic stem cells is a contributor to (though does not guarantee) primary tyrosine kinase inhibitor resistance, consistent with experimental and clinical data.

Strengths:<br /> Mathematical modelling in the work is validated using both experimental and clinical data.

The approach to model selection and identification of reasonable parameter regions is interesting and appealing, particularly in the context of modelling processes such as CML which can exhibit significant heterogeneity between patients.

I expect that this work will be useful to the community, as the approach employed in this work could be readily adapted to study other similar problems (for example, different conditions or treatments), provided that suitable experimental and/or clinical data are collected or available.

The work is supported by extensive supplementary material, clearly documenting in detail the techniques involved and assumptions made.

Weaknesses:<br /> Clinical data from CML patients treated with TKI therapy is limited (n=21).

As acknowledged by the authors, there are some physiological aspects that may be important that are not modelled; including stem cell-niche interactions in the bone marrow microenvironment, and interactions with immune cells.

Reviewer #3 (Public Review):

In this study Cook and Ryan examine, at physiological temperatures, the sensitivity of neurotransmitter release to external calcium concentrations close to physiological ones. Using hippocampal neurons in culture, field potential-based stimulation, a spatially confined genetically encoded calcium indicator (GCaMP6f) as well as fluorescent reporters of exocytosis and extracellular glutamate, the authors show that as extracellular calcium concentrations are reduced from 2.0, to 1.2 and finally to 0.8 mM, a disproportional fraction of presynaptic terminals cease to respond, as evidenced by no elevations in intracellular calcium concentrations, no detectable exocytosis or changes in extracellular glutamate. The phenomenon is quantitively modulated by blocking particular types of calcium channels, but is qualitatively conserved across all tested conditions. Finally, the authors show that effects of lower extracellular calcium concentrations can be mimicked by applying Baclofen, an agonist of type B GABA receptors. The authors reveal the sensitivity of all-or none calcium influx and exocytosis near extracellular calcium physiological set points and highlight the potential importance of this sensitivity as an effective control point for neural circuit modulation.

The findings described in the manuscript are potentially important as they seem to uncover a new, yet undescribed, all-or none (binary) phenomenon in the field of synaptic neuroscience, that is, of individual presynaptic terminals moving between two 'states' - 'active' and 'silenced'- which are set somehow by levels of extracellular calcium concentrations. Moreover, this dependency is observed at extracellular calcium concentrations that are quite close to the physiological concentration set point. The use of multiple reporters (intracellular calcium concentrations, synaptic vesicle fusion and extracellular glutamate) strengthens the validity of the observations.

On the other hand, there are two major points that need to be addressed.

The first is that alternative explanations should be ruled out more convincingly, first and foremost the matter of membrane excitability. Two observations are relevant here: The qualitative preservation of the phenomenon when two types of voltage gated calcium channels are blocked separately, and the large heterogeneity of the % of silenced boutons among neurons at a given extracellular calcium concentrations, which is at least as great as the range of modulation of the % of silenced synapses by extracellular calcium concentrations at single neurons. One then wonders if the findings might be attributed to a) the fidelity of the field potential-based stimulation system, that is, the degree to which neurons track the stimuli trains; b) the heterogeneity of neurons in this regard, c) this fidelity at different extracellular calcium concentrations for different neurons, and d) the identity of presynaptic sites analyzed in one run (are they all part of the same axon?). Along these lines, there is an assumption that the field potential-based stimulation system is the sole driver of excitation in these networks, which is reasonable given that excitatory synaptic transmission is mostly blocked pharmacologically (by CNQX and APV). Inhibitory transmission, however, was not blocked and thus, there is no guarantee that the inhibitory input neurons receive and its modulation by extracellular calcium does affect the degree to which neurons fire precisely and reliably at 20 Hz at all conditions. If it could be shown, at least for a substantial subset of the data, that all terminals analyzed for a particular neuron are part of an unambiguously identified axon stretch, with no branches (potential conduction failure points) and still demonstrate the claimed heterogeneity, this potential confound would be less of an issue.

The second issue relates to the ties made to neuromodulation. In spite of the title, introduction and discussion, not a single neuromodulator (such as dopamine, acetylcholine, noradrenaline, serotonin) was tested, only baclofen, which as a derivative of GABA, activates GABAB receptors, not receptors of canonical neuromodulators. The title of this manuscript is therefore not appropriate.

Reviewer #3 (Public Review):

The authors describe a machine learning method for classifying the geographic origin of a Salmonella enterica isolate based on its whole-genome sequencing data. This is done at a continent, region, and country level, and the method is shown to be robust to phylogenetic diversity, temporal trends, and possibly some amount of mislabelling (but please see the first concern below). The authors demonstrate that their pipeline produces results in 5 minutes or less, which makes it applicable to many public health microbiology settings.

Some clear strengths of the paper include:<br /> - the use of a hierarchical classification method, which ensures that only those samples that can be unambiguously classified as belonging to a specific region can get assigned to a sub-region within that region (e.g. continent to country)<br /> - leveraging the UKHSA dataset going back nearly a decade, and containing a comprehensive record of all clinically detected Salmonella enterica infections, which mitigates potential biases and ensures a maximal geographic coverage<br /> - making all the data (microreact) and the source code (GitHub) public, which facilitates replication as well as enables other researchers and public health microbiologists to use the trained models directly on their own data<br /> - the use of unitigs as the basis for prediction, which are more informative than K-mers yet more straightforward to identify than SNPs or gene alleles.

There are several methodological concerns that should ideally be addressed:<br /> - in addition to the more complex situation of a tourist visiting country A and consuming food from country B, it would be good to rule out a simpler one of the tourist visiting both countries on the same trip (including via a stopover at an airport); the authors should elaborate on the plausibility of missing data on such multi-country trips and their frequency based on the available travel data<br /> - similarly, there appears to be an underlying assumption that the UK is never at the origin of a Salmonella enterica infection in the dataset selected; the authors should explain why that is a reasonable assumption for this dataset<br /> - the increase of infection incidence during the summer months might be at least partly attributable to a greater number of trips abroad during that period - if the authors have corrected their data for this, they should explicitly say so<br /> - lastly, in discussing the outbreak due to Polish eggs, it should be possible to check explicitly what fraction of the training data may have originated from this outbreak to see if this is sufficient to explain the observed poor prediction

Overall, this is a paper representing a substantial body of work and combining algorithmic advances with practical utility given the rapid turnaround time. It is likely to be generalisable to other pathogens of public health importance and to become integrated into standard protocols for outbreak origin tracing.

Reviewer #3 (Public Review):

Using viral tracing and single-cell transcriptome profiling the authors investigated the electrophysiologic, morphologic, and physiologic roles for subsets of cardiac-specific neurons and found evidence that three adrenergic stellate ganglionic neuron subtypes innervate the heart.

The presented findings provide relevant insights into the properties of neurons modulating cardiac sympathetic control. The findings might open up new avenues to targeted modulation of cardiac sympathetic control. Additional insights from various models addressing for example ischemic and non-ischemic cardiomyopathy might allow to development of targeted therapies for various patient populations in the future.

Reviewer #3 (Public Review):

The study aimed at the identification of functional micro-peptides encoded by transcripts previously annotated as long noncoding RNAs (lncRNAs). The authors pre-selected 10 candidates out of the ~500 zebrafish lncRNA data set based on their engagement with the ribosome (by ribosome profiling data) and their expression in the embryonic brain. By performing an F0 CRISPR/Cas9 screen coupled with embryonic behavioral assays, two transcripts encoding sequence-related micro-peptides were identified. Using a set of stable mutant alleles, the authors showed that mutations specifically affecting the open reading frame (ORF) of the putative micro-peptides cause changes in embryonic behavior when compared to wild-type embryos or embryos with mutations in the non-coding regions of the tested transcripts. The locomotor hyperactivity phenotype was even stronger in double homozygous mutants suggesting a redundant function of both micro-peptides. The authors demonstrated that the behavioral phenotype of one of the mutants was rescued by the transgene expression of the coding sequence (CDS). Sequence analyses of both peptides revealed their conservation and homology to the human non-histone chromosomal proteins (HMGN1 proteins). The authors demonstrated that the micro-peptide mutants exhibit changes in chromatin accessibility for transcription factors modifying neural activation, dysregulation of gene expression programs, and changes in oligodendrocyte and cerebellar cell states during development.

The study presents an important discovery of two sequence-related micro-peptides with important and potentially conserved functions during development. While it is still unclear how the micro-peptides act in the cell, it is evident that they are key regulators of cellular states. Whereas the study is well done, the data presentation should be improved as several important details were omitted.

Reviewer #3 (Public Review):

K. Vandelannoote and collaborators report on using spatially-localized possum feces investigated for Mycobacterium ulcerans, as a proxy for cases of Buruli ulcer, South Australia. The report is a contributive, enforcing survey of animal excreta and is based on strong pieces of evidence.

Reviewer #3 (Public Review):<br /> <br /> The manuscript by Francou et al investigated cellular mechanisms of epiblast ingression during mouse gastrulation. The authors wanted to know whether/how epiblast cell-cell junctional dynamics correlate with apical constriction and subsequent ingression. Because mouse gastrula adopts an inverted-cup morphology (as a result of differential invasive behavior of polar and mural trophoblast cells), epiblast cells are located in the innermost position and are difficult to image. This is more so when one wants to perform live imaging of epiblast cells' apical surface. The authors tackled such problems/limitations by using a combination of ZO-1 GFP line, confocal time-lapse microscopy, fixed embryo immunostaining, and Crumbs2 mutant embryos. The authors observed that apical constriction was associated with cell ingression, that this constriction occurred in a pulsed fashion (i.e., 2-4 cycles with phases of contraction and expansion, eventually leading to reduction of apical surface and ingression), that this constriction took place asynchronously (i.e., neighboring epiblast cells did not exhibit coordinated behavior) and that junctional shrinkage during apical constriction also occurred in a pulsed and asynchronous manner. The authors also investigated localization/co-localization of several apical proteins (Crumbs2, Myosin2B, pMLC, ppMLC, Rock1, F-actin, PatJ, and aPKC) in fixed samples, uncovering somewhat reciprocal distribution of two groups of proteins (represented by Myosin2B in one group, and Crumbs2 in the other). Finally, the authors showed that Crumbs2 -/- embryos had disturbed actomyosin distribution/levels without affecting junctional integrity (partially explaining the ingression defect reported in Crumbs2 -/- mutant embryos). Overall, this manuscript offers high-quality live imaging data on the dynamic remodeling of epiblast apical junctions during mouse gastrulation. It would be interesting to see whether phenomena reported in this manuscript can be extended to the entire primitive streak (or are they specific only to a subset of mesoderm precursors) and to the entire period of mesendoderm formation. More importantly, it would be interesting to see whether the ingression behavior seen here is representative of all eutherian mammals regardless of their gastrular topography.

Reviewer #3 (Public Review):

In this manuscript, a cytosolic extract of porcine oocytes is prepared. To this end, the authors have aspirated follicles from ovaries obtained from by first maturing oocytes to meiose 2 metaphase stage (one polar body) from the slaughterhouse. Cumulus cells (hyaluronidase treatment) and the zona pellucida (pronase treatment) were removed and the resulting naked mature oocytes (1000 per portion) were extracted in a buffer containing divalent cation chelator, beta-mercaptoethanol, protease inhibitors, and a creatine kinase phosphocreatine cocktail for energy regeneration which was subsequently triple frozen/thawed in liquid nitrogen and crushed by 16 kG centrifugation. The supernatant (1.5 mL) was harvested and 10 microliters of it (used for interaction with 10,000 permeabilized boar sperm per 10 microliter extract (which thus represents the cytosol fraction of 6.67 oocytes).

The sperm were in this assay treated with DTT and lysoPC to prime the sperm's mitochondrial sheath.

After incubation and washing these preps were used for Western blot (see point 2) for Fluorescence microscopy and for proteomic identification of proteins.

Points for consideration:

1) The treatment of sperm cells with DTT and lysoPC will permeabilize sperm cells but will also cause the liberation of soluble proteins as well as proteins that may interact with sperm structures via oxidized cysteine groups (disulfide bridges between proteins that will be reduced by DTT).

2) Figure 3: Did the authors really make Western blots with the amount of sperm cells and oocyte extracts as the description in the figures is not clear? This point relates to point 1. The proteins should also be detected in the following preparations (1) for the oocyte extract only (done) (2) for unextracted nude oocytes to see what is lost by the extraction procedure in proteins that may be relevant (not done) (3) for the permeabilized (LPC and DTT treated and washed) sperm only (not done) (4) For sperm that were intact (done) (5) After the assay was 10,000 permeabilized sperm and the equivalent of 6.67 oocyte extracts were incubated and were washed 3 times (or higher amounts after this incubation; not done). Note that the amount of sperm from one assay (10,000) likely will give insufficient protein for proper Western blotting and or Coomassie staining. In the materials and methods, I cannot find how after incubation material was subjected to western blotting the permeabilized sperm. I only see how 50 oocyte extracts and 100 million sperm were processed separately for Western blot.

3) Figures 4, 5, 6, 7, and 8 see point 2. I do miss beyond these conditions also condition 1 despite the fact that the imaged ooplasm does show positive staining.

4) These points 1-3 are all required for understanding what is lost in the sperm and oocyte treatments prior to the incubation step as well as the putative origin of proteins that were shown to interact with the mitochondrial sheath of the oocyte extract incubated permeabilized sperm cells after triple washing. Is the origin from sperm only (Figs 5-8) or also from the oocyte? Is the sperm treatment prior to incubation losing factors of interest (denaturation by DTT or dissolving of interacting proteins pre-incubation Figs 3-8)?

5) Mass spectrometry of the permeabilized sperm incubated with oocyte extracts and subsequent washing has been chosen to identify proteins involved in the autophagy (or cofactors thereof). The interaction of a number of such factors with the mitochondrial sheath of sperm has been shown in some cases from sperm and others for an oocyte origin. Therefore, it is surprising that the authors have not sub-fractionated the sperm after this incubation to work with a mitochondrial-enriched subfraction.

I am very positive about the porcine cell-free assay approach and the results presented here. However, I feel that the shortcomings of the assay are not well discussed (see points 1-5) and some of these points could easily be experimentally implemented in a revised version of this manuscript while others should at least be discussed.

Reviewer #3 (Public Review):

The authors tried to study the role of the cylicin gene in sperm formation and male fertility. They used the Crispr/cas 9 to knockout two mouse cylicin genes, cylicin 1 and cylicin 2. They used comprehensive methods to phenotype the mouse models and discovered that the two genes, particularly cylicin 2 are essential for sperm calyx formation. They further compared the evolution of the two genes. Finally, they identified mutations of the genes in a patient. The major strengths are the high quality of data presented, and the conclusion is supported by their findings from the animal models and patients. The major weakness is that the study is descriptive: no molecular mechanism studies were conducted or proposed, limiting its impact on the field.

Reviewer #3 (Public Review):

In this manuscript, the authors characterize antigen binding sites, mechanism of action, and in vivo efficacy of neutralizing monoclonal antibodies (mAbs) previously isolated from New World hantavirus survivors. Both hantavirus species-specific mAbs and broadly neutralizing hantavirus mAbs are analyzed.

The strengths of the manuscript are the presentation of both in vitro and in vivo data for mAbs that have different antigen binding sites and mechanisms of neutralization. Weaknesses include a lack of authentic virus experiments for the in vitro data.

The impact of the work on the field is the identification of different neutralizing sites on hantavirus glycoproteins in species-specific and broadly reactive mAbs. There are also interesting data on loss of broadly neutralizing activity of mAbs after reversion to the germline sequence.

Reviewer #3 (Public Review):

Head-fixed preparations should always be conceived more as a necessity (for example, to avoid damaging expensive lab equipment) than as a final path towards which the entire field of neuroscience must go. The ideal will always be to move towards a more naturalistic and ecological approach to understanding behavior. Said that. The Davis Rig seems to be a thing of the past, welcome the Open-Source Head-fixed Rodent Behavioral Experimental Training System (OHRBETS). OHRBETS represents a significant advantage over the Davis Rig equipment to measure oromotor palatability responses in a brief access test, to perform positive and negative reinforcement, and even real-time place preference in a head-fixed preparation.

This is a well-written manuscript; the work and results are impressive. The manuscript is quite relevant to the Neuroscience field and will be of general interest. The experiments were carefully done. It is expected that OHRBETS will be widely used in multiple Neuroscience labs.

Reviewer #3 (Public Review):

In this manuscript, Guinet and colleagues explore the impact of endoparasitoid lifestyle in Hymenopterans on endogenization and domestication of viruses. Using a well-structured bioinformatic pipeline, they show that an endoparasitoid lifestyle promotes viral endogenization and domestication, particularly for dsDNA viruses. In their discussion, they provide multiple discussion points to hypothesize why this could be the case. It is, to my knowledge, one of the first to link life history traits of insects to particular bias in the genomic endogenization of viruses, which has implications for virology and host-parasite interaction at large.

The manuscript is well-written and structured. The amount of data generated and analyzed is impressive, and the authors have carefully set up their analysis. I have no reasons to doubt any of the analyses the authors have conducted on the output of the screening pipeline set up to discover and characterize endogenous viral elements. I would, however, have appreciated a more thorough investigation on the impact of the scoring system for EVE detection (Scaffold endogenization score), which strongly shapes the dataset used for the analysis, and thus might introduce biases. While I completely understand the need for a scoring system and agree that the parameters used seem reasonable, these are new for the field, and their impact has not been properly explored here. The authors have chosen to focus on a conservative threshold of EVEs scored above D (see Table S2): I wonder what the picture would be if they included all potential EVEs, even poorly scored. How dependent are the results of this unvalidated scoring system? I know several proven EVEs in mosquitoes (confirmed in vivo) that would have been poorly scored and excluded here. By being sure to exclude false positives, the authors may have biased their dataset in ways that influence the results.

Reviewer #3 (Public Review):

Initially, Salas-Lucia et al examined the effect of deiodinase polymorphism on thyroid hormone-medicated transcription using a transgenic animal model and found that the hippocampus may be the region responsible for altered behavior. Then, by changing to topic completely, they examined T3 transport through the axon using a compartmentalized microfluid device. By using various techniques including an electron microscope, they identified that T3 is uptaken into clathrin-dependent, endosomal/non-degradative lysosomes (NDLs), transported in the axon to reach the nucleus and activate thyroid hormone receptor-mediated transcription.

Although both topics are interesting, it may not be appropriate to deal with two completely different topics in one paper. By deleting the topic shown in Table 1, Figure 1, and Figure 2, the scope of the manuscript can be more clear.

Their finding showing that triiodothyronine is retrogradely transported through axon without degradation by type 3 deiodinase provides a novel pathway of thyroid hormone transport to the cell nucleus and thus can contribute greatly to increasing our understanding of the mechanisms of thyroid hormone action in the brain.

Reviewer #3 (Public Review):

This paper addresses the impact of non-linear protein degradation on the precision of morphogen gradients. Since the predominant model for the formation of morphogen gradients is a production/diffusion/degradation model understanding the contribution of degradation is an important question. This paper investigates the properties of the simplest and most general mathematical model for gradient formation. As such, this work is of interest. The main conclusion of the paper is that non-linear protein degradation has little impact on the precision of the morphogen gradient near the source of production of the morphogen and it reduces precision far away from the source. These conclusions are supported by the mathematical analysis presented. The paper is a difficult read for people unfamiliar with the current literature.

Reviewer #3 (Public Review):

The manuscript by Chen et al shows solid evidence that canine origin influenza viruses are evolving towards a more mammalian adapted phenotype. The data also show that humans may lack proper protection against these viruses if they were to evolve more prone to cross to humans. There are some aspects of the ms that need to be addressed: 1) The investigators should run neuraminidase inhibition assays to established the level of cross reactivity of human sera to the canine origin NA (one of reasons proposed as to the lower impact of the H3N2 pandemic was the presence of anti0N2 antibodies in the human population), 2) please tone down the significance of ferret-to-ferret transmission as a predictor of human-to-human transmission. Although flu viruses that transmit among humans do show the same capacity in ferrets, the opposite is NOT always true.

Reviewer #3 (Public Review):

The manuscript adequately demonstrates that genomic instability is maintained in HGSOC tumourspheres. The use of 3-dimensional HGSOC models to more greatly resemble the in vivo environment has been used for more than a decade, but this is the first demonstration using a variety of genomic assessment tools to show genomic instability in the HGSOC tumoursphere model. It is clearly demonstrated that these HGSOC tumourspheres represent copy number variations similar to information in public datasets (TCGA, PAWG, BriTROC-1) and that cellular heterogeneity is present in these tumourspheres. The simple steps outlined to establish and passage tumourspheres will benefit the field to further study mechanisms of genomic instability in HGSOC.

A weakness of the manuscript is the lack of operational definitions for what constitutes an organoid and an appropriate definition to distinguish genomic instability from chromosomal instability (a distinct type of genomic instability). Line 147 states "As PDOs consist of 100% tumour cells...", although this does not appear to have been established by any assessment. This limited characterization of the 3D model is a weakness since no data is provided on whether the tumourspheres constitute only a single cell type (as indicated on line 147) or multiple cell types (e.g., HGSOC cell, mesothelial cells) using markers beyond p53 expression. Based on this information, this model cannot be called a PDO, rather it should be referred to as a tumoursphere.

Chromosome instability (CIN) is a type of genomic instability that is broadly defined as an increased rate of chromosome gains or losses and is best identified through analysis of single cells (e.g., karyotype analysis), something that bulk whole genome sequencing cannot determine since it is a reflection of cell populations and not individual cells. While the data demonstrate genomic instability is retained in the tumourspheres, and chromosome losses or copy-number amplifications were observed using single-cell whole genome sequencing, evaluation of samples from the same patient over time was not evaluated. While there is evidence to support CIN in these samples, in agreement with other published work that has demonstrated CIN in >95% of HGSOC samples analyzed at the single-cell level, this work is not conclusive. The title of the manuscript should be modified to more accurately represent what the evidence supports.

An additional weakness is missing information (e.g., Figure 1d, Supplementary Figure 3b, and Supplementary Table 4 were not included in the manuscript; the 13 anticancer compounds used to test drug sensitivity are not indicated) making an assessment of the data impossible, and assessment of some conclusions difficult.

Reviewer #3 (Public Review):

This manuscript by Geisler and colleagues used suppressor genetics to identify suppressors of the sma-5(n678) allele, which results in a defective gut endotube (an IF layer just under the microvillar structure), small body size, slow development, and short life span. The authors identified an internal deletion allele in ifb-2, which stunningly rescues all of the phenotypes listed above (despite the apparent absence of an endotube). This suppression is also observed with a previously characterized knockout allele. Conversely, this allele also suppresses analogous defects that result from mutations in the ifo-1 gene and bbln-1.

This is an exceptionally rigorous set of experiments, beautifully described in a clear manuscript illustrated by nicely constructed figures. The overall finding, that some IF mutations result in toxic aggregates that can be eliminated by the loss of a single IF protein is interesting both from a fundamental understanding of IF networks and its clinical implications. With one minor exception, the conclusions are well supported by the data presented.

Reviewer #3 (Public Review):

In this manuscript, Chan and collaborators investigate the role of CDPK1 in regulating microneme trafficking and exocytosis in Toxoplasma gondii. Micronemes are apicomplexan-specific organelles localized at the apical end of the parasite and depending on cortical microtubules. Micronemes contain proteins that are exocytosed in a Ca²+-dependent manner and are required for T. gondii egress, motility, and host-cell invasion. In Apicomplexa, Ca²+ signaling is dependent on Ca²+-dependent protein kinases (CDPKs). CDPK1 has been demonstrated to be essential for Ca²+-stimulated micronemes exocytosis allowing parasite egress, gliding motility, and invasion. It is also known that intracellular calcium storages are mobilized following a cyclic nucleotide-mediated activation of protein kinase G. This step, occurs upstream of CDPK1 functions. However, the exact signaling pathway regulated by CDPK1 remains unknown. In this paper, the authors used phosphoproteomic analysis to identify new proteins phosphorylated by CDPK1. They demonstrated that CDPK1 activity is required for calcium-stimulated trafficking of micronemes to the apical end, depending on a complex of proteins that include HOOK and FTS, which are known to link cargo to the dynein machinery for trafficking along microtubules. Overall, the authors identified evidence for a new protein complex involved in microneme trafficking through the exocytosis process for which circumstantial evidence of its functionality is demonstrated here.

Reviewer #3 (Public Review):

Acetylcholine and Norepinephrine are two of the most powerful neuromodulators in the CNS. Recently developments of new methods allow monitoring of the dynamic changes in the activity of these agents in the brain in vivo. Here the authors explore the relationship between the dynamic changes in behavioral states and those of ACh and NE in the cortex. Since neuromodulatory systems cover most of the cortical tissue, it is essential to be able to monitor the activity of these systems in many cortical areas simultaneously. This is a daunting task because the axons releasing NE and ACh are very thin. To my knowledge, this study is the first to use mesoscopic imaging over a wide range of the cortex at the single axon resolution in awake animals. They find that almost any observable change in behavioral state is accompanied by a transient change in the activity of cortical ACh and NE axonal segments. Whisking is significantly correlated with ACh and NE. The authors also explore the spatial pattern of activity of ACh and NE axons over the dorsal cortex and find that most of the dynamics is synchronous over a wide spatial scale. They look for deviation from this pattern (which I will discuss later). Lastly, the authors monitor the activity of cortical interneurons capable of releasing ACh.

Comments:<br /> 1. On a broad overview, I find the discussion of behavioral states, brain states, and neuromodulation states quite confusing. To begin with, I am not convinced by the statement that "brain states or behavioral states change on a moment-to-moment basis." I find that the division of brain activity into microstates (e.g., microarousal) is counterproductive. After all, at the extreme, going along this path, we might eventually have an extremely high dimensional space of all neuronal activity, and any change in any neuron would define a new brain state. Similarly, mice can walk without whisking, can whisk without walking, can walk and whisk, are all these different behavioral states? And if so, are they all associated with different brain states? Most importantly, in the context of this manuscript, one would expect that different states (brain, behavior) would be associated with at least four potential states of the ACh x NE system (high ACh and High NE, High ACh and Low NE, etc.). However, the reported findings indicate that the two systems are highly synchronized (or at least correlated), and both transiently go on with any change from a passive state to an active state. Therefore, the manuscript describes a rather confined relationship of the neuromodulation systems with the rather rich potential of brain and behavioral states. Of course, this is only my viewpoint, and the authors are not obliged to accept it, but they should recognize that the viewpoint they take for granted is not shared by all and consider acknowledging it in the manuscript.<br /> 2. Most of the manuscript (bar one case) reports nearly identical dynamics of ACh and NE. Is that a principle? What makes these systems behave so similarly? Why have two systems that act nearly the same? Still, if there is a difference, it is the time scale of the ACh compared to the NE. Can the authors explain this difference or speculate what drives it?<br /> 3. Whisker activity explains most strongly the neuromodulators dynamics, but pupil dilation almost does not (in contrast to many previous reports including reports of the same authors). If I am not mistaken, this was nearly ignored in the presentation of the results and the discussion section. Could the author elaborate more on what is the reason for this discrepancy?<br /> 4. I find the question of homogenous vs. heterogenous signaling of both the ACh and NE systems quite important. It is one thing if the two systems just broadcast "one bit" information to the whole brain or if there are neuromodulation signals that are confined in space and are uncorrelated with the global signal. However, the way the analysis of this question is presented in the manuscript is very difficult to follow, and eventually, the take-home message is unclear. The discussion section indicates that the results support that beyond a global synchronized signal, there is a significant amount of heterogeneous activity. I think this question could benefit from further analysis. I suggest trying to demonstrate more specific examples of axonal ROIs where their activity is decorrelated with the global signal, test how consistent this property is (for those ROIs), and find a behavioral parameter that it predicts. Also, in the discussion part, I am missing a discussion of the potential mechanism that allows this heterogeneity. On the one hand, an area may receive NE/ACh innervation from different BF/LC neurons, which are not completely synchronized. But those neurons also innervate other areas, so what is the expected eventual pattern? Also, do the results support neuromodulation control by local interneuron circuits targeting the axons (as is the case with dopaminergic axons in the Basal Ganglia)?<br /> 5. The axonal signal seems to be very similar across the cortex. I am not sure this is technically possible, but given that NE axons are thin and non-myelinated and taking advantage of the mesoscopic scale, could the author find any clue for the propagation of the signal on the rostral to caudal axis?<br /> 6. While the section about local VCIN is consistent with the story, it is somehow a sidetrack and ends the manuscript on the wrong note. I leave it to the authors to decide but recommend them to reconsider if and where to include it. Unfortunately, the figure attached was on a very poor resolution, and I could not look into the details, so I am afraid that I could not review this section properly.

Reviewer #3 (Public Review):

This manuscript describes McSC states and McSC function during regeneration in zebrafish using both a scRNAseq timecourse and classic zebrafish experimentation, including lineage tracing and mutant lines. Altogether this study provides a more holistic look at pigment regeneration following injury and helps to validate the role of signaling pathways implicated in McSC biology by previous studies. The major question addressed by this manuscript is whether McSC heterogeneity can explain the highly regenerative nature of the zebrafish pigmentary system. The observations reported in this manuscript confirm this view, eloquently using a time course of single-cell transcriptomics for predictive purposes followed up by mechanistic studies to confirm the fate of different McSC subclusters. This study very nicely complements and extends our current understanding of how McSCs function during regeneration and provides novel datasets for further interrogation. Perhaps the most exciting aspect of the data is the identification of a novel marker (aox5) to identify self-renewing McSCs; this tool could be employed to identify these cells and address their potential in the context of expanding these cells for therapeutic purposes or address their contribution as melanoma stem cells. This study will be of general interest to researchers interested in pigment regeneration, stem cell-based therapeutics for pigment disorders, and the basic biology of stem cells and their heterogeneity.

While this paper certainly extends previous observations of McSCs, the idea of McSC heterogeneity is not necessarily novel. In mouse, KIT-dependent and KIT-independent McSC populations have been identified (Ueno 2015) as well as other McSC subpopulations with different potentials (CD34+/-, Joshi 2019). While this manuscript does a much more comprehensive job of describing this heterogeneity, which is fantastic, some of the previous literature on the topic could be better acknowledged and integrated. Despite this criticism, this manuscript provides the most comprehensive look to date at McSC dynamics across the regenerative period and provides ample datasets for secondary analyses to generate/confirm additional hypotheses.

Reviewer #3 (Public Review):

In this study, the authors set out to study the requirement of the TATA binding protein (TBP) in transcription initiation in mESCs. To this end they used an auxin inducible degradation (AID) system. They report that by using the AID-TBP system after auxin degradation, 10-20% of TBP protein is remaining in mESCs. The authors claim that as, the observed 80-90% decrease of TBP levels are not accompanied by global changes in RNA polymerase II (Pol II) chromatin occupancy or nascent mRNA levels, TBP is not required for Pol II transcription. In contrast, they find that under similar TBP-depletion conditions tRNA transcription and Pol III chromatin occupancy were impaired. The authors also asked whether the mouse TBP paralogue, TBPL1 (also called TRF2) could functionally replace TBP, but they find that it does not. From these and additional experiments the authors conclude that redundant mechanisms may exist in which TBP-independent TFIID like complexes may function in Pol II transcription.

The major strengths of this manuscript are the numerous genome-wide investigations, such as many different CUT&Tag experiments, and NET-seq experiments under control and +auxin conditions and their analyses. Weaknesses lie in some experimental setups (i.e. overexpression of Halo-tagged TAFs), mainly in the overinterpretation (or misinterpretation) of the data and in the lack of a fair discussion of the obtained data in comparison to observations described in the literature. As a result, very often the interpretation of data does not fully support the conclusions.<br /> Nevertheless, the findings that 80-90% decrease in cellular TBP levels do not have a major effect on Pol II transcription are interesting, but the manuscript needs some tuning down of many of the authors' very strong conclusions, correcting several weaker points and with a more careful and eventually more interesting Discussion.

Reviewer #3 (Public Review):

In this manuscript, Wang et al. assess the role of wall shear stress and hydrostatic pressure during valve morphogenesis at stages where the valve elongates and takes shape. The authors elegantly demonstrate that shear and pressure have different effects on cell proliferation by modulating YAP signaling. The authors use a combination of in vitro and in vivo approaches to show that YAP signaling is activated by hydrostatic pressure changes and inhibited by wall shear stress.

There are a few elements that would require clarification:

1) The impact of YAP on valve stiffness was unclear to me. How is YAP signaling affecting stiffness? is it through cell proliferation changes? I was unclear about the model put forward:<br /> - Is it cell proliferation (cell proliferation fluidity tissue while non-proliferating tissue is stiffer?)<br /> - Is it through differential gene expression?<br /> This needs clarification.

2) The model proposes an early asymmetric growth of the cushion leading to different shear forces (oscillatory vs unidirectional shear stress). What triggers the initial asymmetry of the cushion shape? is YAP involved?

3) The differential expression of YAP and its correlation to cell proliferation is a little hard to see in the data presented. Drawings highlighting the main areas would help the reader to visualise the results better.

4) The origin of osmotic/hydrostatic pressure in vivo. While shear is clearly dependent upon blood flow, it is less clear that hydrostatic pressure is solely dependent upon blood flow. For example, it has been proposed that ECM accumulation such as hyaluronic acid could modify osmotic pressure (see for example Vignes et al.PMID: 35245444). Could the authors clarify the following questions:<br /> - How blood flow affects osmotic pressure in vivo?<br /> - Is ECM a factor that could affect osmotic pressure in this system?

Reviewer #3 (Public Review):

Farahani et al. developed a novel biosensor, pYtag, to monitor receptor tyrosine kinase activity using live cell fluorescence microscopy. The approach to the sensor design relies on adding a tyrosine activation motif to a receptor tyrosine kinase of interest which when phosphorylated recruits a fluorescently-tagged SH2 domain protein. The sensor was used to monitor EGFR and ErbB2 activity and characterize their activity in the presence of different ligands, allowing for the kinetics of receptor activity to be determined in live cells with high temporal resolution.

The design, characterization, and verification of the sensor with controls were rigorously done and the sensor appears to be a good approach to monitoring receptor tyrosine kinases. In addition to this, the biological characterization of RTK signaling kinetics allowed for mathematical modeling to determine the dimerization affinity of ligand-bound receptors is the rate-limiting step of receptor tyrosine kinase signaling dynamics. Proving these sensors can be used to monitor biological activities in live cells.

Initial proof of principles of pYtag was demonstrated in cell lines where the tags were expressed, the authors went beyond this and showed the tagging system could be gene edited to endogenous proteins allowing for the function of receptor tyrosine kinase to be measured under physiological concentrations.

Reviewer #3 (Public Review):

Over the past decade, Cryo-EM analysis of assembling ribosomes has mapped the major intermediates of the pathway. Our understanding of the mechanisms by which ATPases drive the transitions between states has been slower to develop because of the transient nature of these events. Here, the authors use cryo-EM and biochemical and molecular genetic approaches to examine the function of the DEAD-box ATPase Spb4 and the AAA-ATPase Rea1 in RNP remodeling. Spb4 works on the pre-60S in an early nucleolar state. The authors find that Spb4 acts to remodel the three-way junction of H62/H63/H63a at the base of expansion segment ES27. Interestingly, Spb4 appears to interact stably with a folding intermediate in the ADP rather than ATP-bound form. This work represents one of the few cases in which an RNA helicase of ribosome biogenesis has been captured and engaged with its substrate. The authors then show that the addition of the AAA-ATPase Rea1 to Spb4-purified particles results in the release of Ytm1, a known target of Rea1. However, they did not observe an efficient release of Ytm1 when particles were affinity purified via Ytm1, suggesting that the recruitment of Spb4 is important for this step. Cryo-EM analysis of Spb4-particles treated with Rea1 revealed the previously characterized state NE particles but no additional intermediates. Consequently, this analysis of Rea1 is less informative about its function than is their work on Spb4 helicase activity. In general, the data support the authors' conclusions and the data are well presented.

Major points<br /> 1. The Erzberger group has recently published work regarding the function of Spb4. They similarly found that Spb4 is necessary for remodeling the 3-way junction at the base of ES27. Although it was posted to Biorxiv in Feb 2022, it was not formally published until Dec 2022. The authors should cite this work and include a brief discussion comparing conclusions.<br /> 2. L311. The heading "Coupled pre-60S dissociation of the Ytm1-Erb1 complex and RNA helicase Has1" should be changed. Coupling implies a mechanistic interplay. Although the release of Ytm1 and Has1 both depend on Rea1, the data do not support the conclusion of mechanistic coupling. In fact, the authors write in lines 328-329 "Thus, the Rea1-dependent pre-60S release of the Ytm1-Erb1 complex occurs before and independently of Has1..." Independently cannot also imply coupling.<br /> 3. L339-342 Combining data sets for uniform processing was a great idea! This approach should be used more often in cryo-EM analyses of in vitro maturation reactions.<br /> 4. L428 The authors need to amend their comment that this is the first structure of Spb4-bound to the substrate as this has recently been published by the Erzberger group and was first posted as a preprint in early 2022.

Reviewer #3 (Public Review):

The function of the nervous system relies on precisely connected neuronal networks. A previous study from the Luo lab reported an important pair of molecular interaction between an adhesion GPCR, latrophilin-2, and teneurin-3 in specifying the connections between CA1 neurons in the hippocampus and the subiculum. This new study continues to investigate the signaling mechanisms, particularly whether the trimeric G proteins are involved. Adhesion GPCRs are in general still under studied, esp in nervous system. This study also used a clever misexpression approach, which provide signaling studies in the in vivo context. The data are of high quality and convincing.

Reviewer #3 (Public Review):

In this manuscript, the authors address the mechanism of concentration of HIV-1 particles following interaction with Siglec-1 and define important differences in this process between immature DCs and mature DCs. The methods are largely derived from imaging that is followed by quantitation of nanoclustering of Siglec-1, distance from the center of the cell, and the effects of inhibitors of actin and RhoA pathways. The quantitative imaging approach is a strength and appears quite carefully done. Another strength is the new findings regarding the role of the formin-dependent actin cytoskeletal rearrangements and RhoA activation on clustering and polarization leading to the formation of the virus-containing compartment (VCC). The results are convincing that mature DCs demonstrate more nanoclustering and that formins and RhoA are important in the clustering that occurs of viruses or virus-like particles following capture by Siglec-1. This information should be valuable to the field.

The weaknesses are not in the methods and major conclusions themselves, but there are a number of aspects of the study that could be strengthened. The definition of a VCC here is simply a spot of Siglec-1 that has coalesced with VLPs. A more complete study would include typical VCC markers such as CD81, CD9, and others and would extend the findings to prove that the mechanism invoked actually elicits VCC formation, as opposed to clustering of Siglec-1 and VLPs along the surface of the cell. This study does not establish the mechanism of membrane invagination or tubule formation that occurs with VCC formation, so perhaps it is really describing the initial, surface-related steps of VCC formation but not subsequent internalization events required to form the deeper, vacuole-like VCC.

Nevertheless, this study provides new insights into the initial steps of VCC formation and is provocative regarding how this can be achieved by Siglec-1 in the absence of the need for a cytoplasmic tail. The formin-dependence of VCC formation will be of interest in future studies of HIV uptake and trans-infection events mediated by dendritic cells and macrophages. Some of the findings can be directly translated to the biological context of how VCCs form in HIV-infected macrophages. These will all likely be of substantial interest to those working on HIV and other viruses that are captured by Siglec-1.

Reviewer #3 (Public Review):

The authors perform an elegant study where they show that intravitreal injection of human monocytes from patients with AMD cause reduced ERG B-wave amplitudes and photoceptor cell loss compared to controls in the photic retinal injury model. Differentiation of human monocytes from patients with AMD into M2a macrophages caused increased photoreceptor cell loss compared to M1 macrophages. Next, the authors show that after co-culturing retinal explants with M1 and M2a human macrophages followed by TUNEL staining, M2 human macrophages had significantly more apoptotic photoreceptor cells than M1 human macrophages. The authors show that human M2a macrophages have significantly more ROS compared to M0 and M1 human macrophages; however, injection of human M2a macrophages did not cause increased oxidative damage compared to control conditions. Using a multiplex cytokine assay of 120 cytokines between human M1 and M2a macrophages-conditioned medium, the authors found increased levels of 9 cytokines, including three HCC-1, MCP-4, and MPIF-1, which are ligands of the C-C chemokine receptor CCR1. Co-staining showed CCR1 expression in Muller cells following photic injury. In the rd10 mouse model of retinal degeneration as well as aged BALB/c mice CCR1 is upregulated in Muller cells. Injection of mice with the CCR1-specific inhibitor BX471 caused increased photoreceptor numbers and B-wave amplitudes in the photic-injury model. Overall the experiments are well performed and of interest to the field.

Reviewer #3 (Public Review):

The authors attempted to dissect the intercellular mechanisms implicated in the development of diabetic cardiomyopathy. They used one time point to determine the expressional changes in the STZ-high caloric diet model vs non-diabetic. They also attempted to interfere with fibrosis using a PFGFRa antagonist and silencing of Itgb1. Finally, they looked at some variants of the Itgb1 in patients with diabetes to determine a possible association.

Strengths: This is one of the first transcriptomics study a single cell level of the mouse diabetic heart. The study is technically sound.

Weakness: The study is mainly associative. A cause relationship effect is difficult to be extracted. A major problem is that they studied only a single time point at an advanced stage of the disease, therefore it is difficult to determine if the observed changes are epiphenomena. They also use only one diabetic model where STZ was superimposed on the high caloric diet. STZ can cause unspecific effects and more models are generally requested. They also used male mice only while diabetic cardiomyopathy is more prevalent in females. No functional data are provided to study the capacity of treatment to rescue cardiac contractility and diastolic function, which is certainly affected by fibrosis.<br /> The methodological part can help further studies provided the limits indicated above are considered.

Reviewer #3 (Public Review):

The manuscript by Han et al characterizes a pathway from AgRP(LepR) neurons to DMH(MC4R) neurons that is involved in energy balance control. They use a conditional knockout strategy to show that AgRP(LepR) knockout increases body weight and this effect was reversible by blocking GABA signaling. They also showed that activation of AgRP-DMH projection increases food intake, and highlighted a role for alpha3-GABAA receptor signaling in the DMH for regulating feeding behavior. While these data highlight a potential circuit that modulates feeding, there are concerns about the paper in its current form that diminish enthusiasm. The lack of proper controls in many of the experiments raises doubts about the findings.

Strengths: The authors use new tools to characterize a new circuit for leptin-mediated energy balance control. The conditional knockout has several advantages over previous techniques that are described within the manuscript. Further, the authors use combinations of different techniques (gene knockout, optogenetic manipulation, in vivo activity monitoring) to make observations at multiple levels of analysis.

Weaknesses: Several experiments within the paper have worrisome caveats or lack proper controls, raising concerns about the overall conclusions made.

Reviewer #3 (Public Review):

The paper by Sugatha et al. examines the role of SNX32 in membrane trafficking. They found SNX32 interacts with SNX4, SNX32 binds the TfR and CIMPR and is required for their intracellular trafficking, and the intracellular location of SNX32 to endosomes was through lipid binding to PI(3)P or PI(4)P. This study further demonstrated that SNX32 plays a role in BSG trafficking to the cell surface. And lastly, they demonstrated SNX32 plays a role in neuronal differentiation likely through its regulation of BSG trafficking.

Reviewer #3 (Public Review):

The manuscript by Ishii et al describes the structural characteristics of the Ostreococcus tauri photosystem I (PSI) light-harvesting complexes, mostly under low light conditions. The bulk of the work comes from cryo-EM studies that show changes in the supercomplex structure at low light, and suggest a model where additional light harvesting complexes are recruited to the supercomplex to increase light capturing. Interestingly, the evidence presented suggests that this mechanism is distinct from the classical antenna state transitions seen in other organisms studied thus far.

The structural studies are quite interesting and overall suggest an interesting mechanism for adjusting light harvesting by PSI in this heretofore understudied species. These are exciting findings and a great example of how new structural approaches can lead to new functional discoveries.

The manuscript is weaker when it comes to connecting these new structures to functions, and definitive cause-effect relationships are not yet provided, nor are any extensive studies on the effects of redox regulation, physiological state, etc. of the putative state transition reported, preventing a more definitive assessment of the mechanisms and physiological importance of the observed changes.

Nevertheless, the results indicate that a different (previously unknown) mode of regulation, or at least alteration, of light capture, is likely to occur in this species, adding substantially to our knowledge of the diversity of photosynthetic responses, and setting up the field to investigate the underlying mechanisms.

Reviewer #3 (Public Review):

This paper from Gao et al., uses single nuclei RNA sequencing to identify cell types and their putative gene markers for the paraventricular thalamus, a small midline brain region important for arousal and motivation. The dataset, collected from male mice, contains ~13,000 single nuclei transcriptomes from the PVT and surrounding regions. Overall, the collected data itself is generally of high quality, and the authors describe some gene markers and putative cell types in the PVT. The authors then go on to characterize PVT cell types from ~4,000 nuclei they identified from the first round of clustering as cell originating from the PVT. They go onto to use fluorescence in situ hybridization to show the spatial patterning of 5 putative marker genes they identified and provide summary disk plot data for the expression of genes for neuromodulator receptors, ion channel subunits, calcium binding proteins, and neuromodulators. The authors then integrate the data with a published 'thalamoseq' dataset of an additional ~2K neurons to show there may be some overlap with cell types identified in previous thalamic sequencing attempts and the current data. Overall, this is a nice start for understanding cell types in the PVT. While the data collected so far is of high quality, and will likely be of interest to the field, the total number of putative PVT cells are quite low (4K or so), which may be impacting the ability to accurately identify cell types. Consistent with this, it is unclear whether the data is best explained by 5 unique PVT neuronal cell types as they describe, or whether the clustering resolution is set too high, which is forcing cells into somewhat arbitrary clusters. By eye, the clusters in Figure 2 do not seem well separated in Umap space. This would likely be improved by additional cells added to the dataset or by demonstrating by other means that the current clustering resolution is appropriate. Alternatively, repeated data integration steps used to try and correct for batch effects may also be causing this.

Reviewer #3 (Public Review):

In previous studies, Harvey and colleagues described several genetically-influenced biometric parameters correlated with the patent foramen ovale (PFO) cardiac defect (Biben et al., 2000) and identified 13 quantitative trait loci (QTL) that affect these traits using a murine F2 intercross design with mouse strains demonstrating extreme septal phenotypes (Kirk et al., 2006). In the submitted manuscript, Marjaneh et al. follow up and refine these studies with a more in-depth QTL analysis utilizing an advanced intercross design (F14), combined with genome and transcriptome sequencing data supporting a role for the identified QTL in atrial septation. The paper is mostly genetic analysis with follow-up informatics and one example of a validated variant. The results are important, and implicate dozens of loci and hundreds of genes (including those in the BMP pathway, and others known to be essential for cardiac morphogenesis) in atrial septum formation, highlighting the complexity of the processes involved. This paper will be an important resource for the field and sets the stage for a follow-up to validate the many candidates identified that may impact cardiac morphogenesis and atrial septation, specifically. The manuscript is well-written and straightforward and does not suffer from major errors in logic or interpretation. The identification of implicated genetic variants will benefit the field of cardiac development and may inform the advancement of future therapeutics for human patients with PFO (for identified coding variants, in particular).

Reviewer #3 (Public Review):

The authors set out to explore how neurons in the rodent parahippocampal area code for environmental and behavioral variables in a complex goal-directed task. The task required animals to learn the association between a cue and a spatial response and to use this information to guide behavior flexibly on a trial-by-trial basis. The authors then used a series of sophisticated analytical techniques to examine how neurons in this area encode spatial location, task-relevant cues, and correct vs. incorrect responding. While these questions have been addressed in studies of hippocampal place cells, these questions have not been addressed in these upstream parahippocampal areas.

Strengths:

1) The study presents data from ensembles of simultaneously recorded neurons in the parahippocampal region. The authors use a sophisticated method for ensuring they are not recording from the same neurons in multiple sessions and yet still report impressive sample sizes.

2) The use of the complex behavioral task guards against stereotyped behavior as rats need to continually pay attention to the relevant cue to guide behavior. The task is also quite difficult ensuring rats do not reach a ceiling level of performance which allows the authors to examine correct and incorrect trials and how spatial representations differ between them.

3) The authors take the unusual approach of not pre-processing the data to group neurons into categories based on the type of spatial information that they represent. This guards against preconceived assumptions as to how certain populations of neurons encode information.

4) The sophisticated analytical tools used throughout the manuscript allow the authors to examine spatial representations relative to a series of models of information processing.

5) The most interesting finding is that neurons in this region respond to situations where rewards are not received by increasing their firing rates. This error or mismatch signal is most commonly associated with regions of the basal ganglia and so this finding will be of particular interest to the field.

Weaknesses:

1) The histological verification of electrode position is poor and while this is acknowledged by the authors it does limit the ability to interpret these data. Recent advances have enabled researchers to look at very specific classes of neurons within traditionally defined anatomical regions and examine their interactions with well-defined targets in other parts of the brain. The lack of specificity here means that the authors have had to group MEC, PaS, and PrS into a functional group; the parahippocampus. Their primary aim is then to examine these neurons as a functional group. Given that we know that neurons in these areas differ in significant ways, there is not a strong argument for doing this.

2) The analytical/statistical tools used are very impressive but beyond the understanding of many readers. This limits the reader's ability to understand these data in reference to the rest of the literature. There are lots of places where this applies but I will describe one specific example. As noted above the authors use a complex method to examine whether neurons are recorded on multiple consecutive occasions. This is commendable as many studies in the field do not address this issue at all and it can have a major impact as analyses of multiple samples of the same neurons are often treated as if they were independent. However, there is no illustration of the outputs of this method. It would be good to see some examples of recordings that this method classifies as clearly different across days and those which are not. Some reference to previously used methods would also help the reader understand how this new method relates to those used previously.

3) The effects reported are often subtle, especially at the level of the single neuron. Examples in the figures do not support the interpretations from the population-level analysis very convincingly.

The authors largely achieve their aims with an interesting behavioral task that rats perform well but not too well. This allows them to examine memory on a trial-by-trial basis and have sufficient numbers of error trials to examine how spatial representations support memory-guided behavior. They report ensemble recordings from the parahippocampus which allows them to make conclusions about information processing within this region. This aim is relatively weak though given that this collection of areas would not usually be grouped together and treated as a single unitary area. They largely achieve their aim of examining the mechanisms underlying how these neurons code task-relevant factors such as spatial location, cue, and presence of reward. The mismatch or error-induced rate remapping will be a particularly interesting target for future research. It is also likely that the analytical tools used in this study could be used in future studies.

Reviewer #3 (Public Review):

This paper investigates how the epigenetic landscape is set up during early frog embryogenesis focusing on the role of the histone deacetylase, HDAC1, in the regulation of histone acetylation around the period of Zygotic gene activation. The authors document the progressive binding of HDAC1 to the embryonic genome around the time of ZGA and on genomic sites harbouring binding motifs for maternally provided transcription factors. The authors classify HDAC1 binding sites based on their association with different epigenetic markings on H3K27 (acetylation and/or methylation) in embryonic chromatin. They infer from the observed co-occurrence of "incompatible" acetylation and methylation marks on H3K27 residue on a subset of HDAC1 binding sites, that these H3K27 modifications occur in different parts of the embryos. Subsequently, they inhibit histone deacetylase activity by TSA and document its impact on the genomic distribution of acetylated histones as well as transcriptional deregulation in explant from different parts of the embryos. By cross comparing these data to the different classes of HDAC1-associated genomic regions, they conclude that HDAC1 is involved in the spatial regulation of embryonic gene expression. Altogether this work reveals how maternally provided transcription factors could direct chromatin modifiers to shape the epigenome of the developing embryos. The work however relies mostly on indirect evidence and it would be important in particular to confirm (i) that maternal factors are indeed required for HDAC1 targeting to chromatin and (ii) that the documented effect of TSA treatment is mediated through its inhibition of HDAC1.

Reviewer #3 (Public Review):

P2X channels are homomeric or heteromeric, non-selective cation channels that are gated by extracellular ATP. They are found in many tissues and are implicated in bodily functions including digestion and urination, and other processes such as pain and immune response. Recent atomic resolution structures of P2X3 and P2X7 have captured the principal gating states likely conserved within this channel family. Among novel structural features that were identified was a cytoplasmic cap that appears to stabilize the intracellular region of the pore in the open state. This cap is not present in the closed and inactivated states. From these data, it has been proposed that the intracellular side of a conductive P2X pore is formed by a cytoplasmic-exposed portion of a larger, membrane-embedded fenestration, a somewhat unusual characteristic for ion channels. In this manuscript, the authors delineated the region of the fenestration that is likely exposed to the cytoplasm and identify a residue that is negatively charged in P2X1-4 and P2X7 but positively charged in P2X5-6. They suggest that not only could this residue line the ion pore, but also it may contribute to differences in cation-to-anion permeability previously observed between these P2X subfamilies. They demonstrate by electrophysiology that E17 lines the ion pore through a series of classical MTS blocking experiments. They further demonstrate that the charge of this residue confers partial or strong cation to anion permeability in rP2X2 and mP2X5, respectively. This is an elegant investigation of the internal pore of P2X channels and the experiments presented in this work are of high quality.

Reviewer #3 (Public Review):

In this manuscript, the authors examine microelectrode and macroelectrode recordings from the human STN, as well as electrocorticography from the sensorimotor cortex in order to examine the neurophysiological biomarkers underlying tremor and bradykinesia. This is an important and timely topic, as the detection of such biomarkers can have implications for developing effective closed-loop DBS devices. Currently, there is some uncertainty as to which biomarkers may be relevant for which particular symptoms. Here the authors examine signals recorded from multiple depths within the STN and regress those signals onto behavioral measures of tremor and slowness as captured using a novel behavioral paradigm in which patients track movements on a screen in the intraoperative setting. This group has published on this paradigm previously, and here they now use support vector regressions to examine how the physiological data relates to these behavioral measures. In brief, they find that tremors and bradykinesia (slowness) correlate with different neural signatures from different locations. Overall, the results seem well supported, and the methods and statistical tests are sound.

Reviewer #3 (Public Review):<br /> <br /> In this study, Wong et al, generate tools to genetically follow many of the Drosophila olfactory projection neurons. The antennal lobe, where 50 projection neurons need to form a stereotypic map where information from 50 types of olfactory receptor neurons is relayed to higher brain regions, is an exquisite system to study principles of neural circuit wiring. As such, the Luo lab has led the field in uncovering the mechanisms also generating tools that are needed to describe the system in unparalleled temporal and cell-type resolution. Here, they use cutting-edge genetic tools and imaging techniques to provide us with a better-than-ever understanding of the early phases of dendrite targeting and patterning of projection neurons.

Using these refined genetic tools, often allowing them to visualize two types of projection neurons at a time, they uncovered several important principles of dendrite targeting. They found that dendrite targeting is divided into two major steps - first, projection neurons target their dendrites to a few distinct locations, thereby forming a proto-map. This initial targeting is dictated by the combination of their birth time and lineage. As a second step, neurons pattern their dendrites into the adult-specific location by a dynamic process in which net growth is dictated by a balance between stabilization and retraction of dendritic processes. Finally, they found that the embryonic-born projection-neurons, which undergo developmental remodeling that include pruning of their connections to the larval antennal lobe (as it undergoes degeneration) and regrowth into the adult antennal lobe. Surprisingly, and in contrast to other remodeling neurons in Drosophila, pruning and regrowth occur simultaneously.

While the strong part of the paper is the cutting-edge tools, coupled with exceptional imaging strategies, its main weakness stems from the decision to remain in the descriptive realm.

Reviewer #3 (Public Review):

Ubiquilin 2 (UBQLN2) encoded by a familial predisposition gene for Amyotrophic Lateral Sclerosis (ALS) is a proteosome shuttle protein shown to associate with Cxx2 and mammalian Ty3/gypsy-like retrotransposon PEG10 in previous work by this author. Other work has shown that PEG10 is expressed from an imprinted gene required for placental development and in adrenal and brain tissues. Increases in PEG10 expression are also implicated in some cancers. Building on previous work by the senior authors (Whitely et al., 2021) which showed that PEG10 interacts with components of the UBQLN machiner and is elevated in UBQUILN TKO human and mouse cells, this work focuses on the interaction of UBQLN proteins and PEG10 target. Using a HEK human kidney cell line, authors show first that targeting of PEG10 depends upon a proline-rich repeat at the carboxy terminus of Gag-Pol unique to eutherian animals; second, that the aspartyl protease previously implicated in gag-pol processing can release the gag carboxyl-terminal CHCC zinc knuckle nucleocapsid to concentrate in the nucleus and correlates with changes in expression of genes related to neuronal development. Finally, they show that PEG10 is elevated in human spinal cord neuron cell lines.

Strengths:

The primary strengths of this manuscript lie in the multiple experiments linking UBQLN2 activity to the target PEG10 PPR motif and in potentially linking Gag-Pol and NC production to changes in cellular gene expression. The authors knock out multiple UBQLN genes in various species and demonstrate the phylogenetic correspondence between UBQLN2 PEG10 levels.

Weaknesses:

Although this manuscript links elevated PEG10 protein levels to fALS mutated UBQLN2 and changes in neuronal gene expression, it does not as the title suggests demonstrate that UBQLN2 control of PEG10 is required for "neuronal health in ALS". This is an awkward title and the link between neuronal health and the ability to turnover PEG10 is not clearly established since most of the experiments were conducted in non-neuronal human cell lines.

Authors could more completely set the context for their work including their own work (Whiteley et al., 2021) and findings in Angelman (UBE3A, Pandya et al., 2021) and Parkinsons (Sakharkar et al., 2019) which, rather than detracting from their work, would confer greater interest. In addition, they mention in passing that in the absence of familial predisposition mutations, in ALS UBQLN2 can be inactivated by trapping in aggregates. This undermines their comparison of fALS and sALS cells.

The multiple western blots while consistent with authors conclusions, do not show greater than two-fold differences in PEG10 protein levels in the absence of UBQLN2 proteins so that there are likely other factors besides UBQLN2 influencing PEG10 levels. For example, the authors do not comment on PEG10 extracellular VLP production which occurs in some cells or that other proteins previously implicated as targets of PEG10 could be influencing the neuronal phenotypes of fALS. In addition, clarification of the different phenotypes of fALS mutations in the UBQLN2 hotspot would have addressed concerns that more than UBQLN2 is involved in the phenotype.

Reviewer #3 (Public Review):

Jigo, Tavdy & Carrasco used visual psychophysics to measure contrast sensitivity functions across the visual field, varying not only the distance from fixation (eccentricity) but also the angular position (meridian). Both parameters have been shown to affect visual sensitivity: spatial visual acuities generally fall off with eccentricity, it is now widely accepted that it is superior along the horizontal than the vertical meridian, and there may also be differences between the upper and lower visual field, although this anisotropy is typically less pronounced. The eccentricity-dependent decrease in performance is thought to be due to reduced cortical magnification in peripheral compared to central vision; that is, the amount of brain tissue devoted to mapping a fixed amount of visual space. The authors, therefore, include a crucial experimental condition in which they scale the size of their stimuli to account for reduced cortical magnification. They find that while this corrects for reduced performance related to stimulus eccentricity, it does not fully explain the variation in performance at different visual field meridians. They argue that this suggests other neural mechanisms than cortical magnification alone underlie this intra-individual variability in visual perception.

The experiments are done to an extremely high technical standard, the analysis is sound, and the writing is very clear. The main weakness is that as it stands the argument against cortical magnification as the factor driving this meridional variability in visual performance is not entirely convincing. The scaling of stimulus size is based on estimates in previous studies. There are two issues with this: First, these studies are all quite old and therefore used methods that cannot be considered state-of-the-art anymore. In turn, the estimates of cortical magnification may be a poor approximation of actual differences in cortical magnification between meridians. Second, we now know that this intra-individual variability is rather idiosyncratic (and there could be a wider discussion of previous literature on this topic). Since these meridional differences, especially between upper and lower hemifields, are relatively weak compared to the variance, a scaling factor based on previous data may simply not adequately correct these differences. In fact, the difference in scaling used for the upper and lower vertical meridian is minute, 7.7 vs 7.68 degrees of visual angle, respectively. This raises the question of whether such a small difference could really have affected performance.

That said, there have been reports of meridional differences in the spatial selectivity of the human visual cortex (Moutsiana et al., 2016; Silva et al., 2017) that may not correspond one-to-one with cortical magnification. This could be a neural substrate for the differences reported here. This possibility could also be tested with their already existing neurophysiological data. Or perhaps, there could be as-yet undiscovered differences in the visual system, e.g., in terms of the distribution of cells between the ventral and dorsal retina. As such, the data shown here are undoubtedly significant and these possibilities are worth considering. If the authors can address this critique either by additional experiments, analyses, or by an explanation of why this cannot account for their results, this would strengthen their current claims; alternatively, the findings would underline the importance of these idiosyncrasies in the visual cortex.

Reviewer #3 (Public Review):

The authors have been challenged to figure out the neural processing of delay discounting during waiting for upcoming reward outcomes after behavioral controls in the subthalamic nucleus, where unique brain regions as a part of the basal ganglia for cognitive and motor functions. They described the activity property of STN neurons for the delay gratification at the single neuron level and population level, using both conventional and recently developing approaches. The finding is novel, but the details of the analysis are sometimes inaccurate and needed to be improved. Their claims are now partially supported. If their analyses are improved, their findings have a significant impact on understanding the neural basis of delay discounting, which is one of the predominant behavioral characteristics among organisms.

Reviewer #3 (Public Review):

The biochemical identity and the crystal structure of the snake venom phosphodiesterase (svPDE) were determined using protein purified from the crude venom of a snake (Naja atra) captured in Taiwan. The crystal structure was determined with and without AMP bound. The quality of the structure is excellent and the coordination of the bound AMP makes sense based on the coordination by side-chain residues and the known coordination of bound AMP to structural homologues (ENPP3). Naturally, it's interesting that snake venom produces a soluble variant of the membrane-anchored PDE found in humans.

Although the structure and the catalytic site seem overall similar, it is unclear what the role of the snake enzyme is in the host infection. Furthermore, there are a number of human ENPP enzymes and they have different substrate preferences and physiological roles. More detailed biochemistry would help to put the role of the svPDE into a physiological context.

Reviewer #3 (Public Review):

The authors studied the interaction between Arl15 and CNNMs using various biochemical and biophysical approaches. Significantly, they solved the crystal structure of Arl15 and the CBS-pair domain of CNNM2 and demonstrated that PRLs and Arl15 could compete for binding to CNNMs. The study should advance our understanding of how cellular divalent ions are regulated via Arl15, CNNMs, and TRPM7, although some issues regarding the guanine nucleotide-binding of Arl15 need to be addressed.

Reviewer #3 (Public Review):

The role of maternal sleep apnea on neurological and physiological function in the offspring is of substantial interest and the investigators have contributed significantly to this emerging field via prior publications. Recent work has evidenced that recurrent bouts of gestational intermittent hypoxia (GIH) result in life-long changes in cardiovascular, cognitive, and metabolic function in the offspring. Recently, investigators have shown that GIH reprograms the neuroinflammatory response of neonates, such that the newborn offspring's normal immune response is attenuated following a Lipopolysaccharides (LPS) exposure and respiratory rhythm generation is considerably altered (Johnson et al. Respir Physiol Neurobiol. 2018). The present study by Mickelson et al. substantially extends these previous findings by showing that GIH results in region and sex-specific changes in the microglial activation of adult rats. In male rats, these changes are indicative of an increased pro-inflammatory profile and contribute to the blunted ability to elicit respiratory neuroplasticity following apneic challenge-induced breathing instability. While a robust attenuation of key inflammation-related genes was observed in spinal and brainstem regions of GIH-exposed female rats, these results were not pursued further and present another exciting area of investigation. Nonetheless, the primary goal of these studies was to elucidate the potential role of spinal microglial activation in decreasing respiratory neuroplasticity in adult rats, which has been investigated in-depth using clever and appropriate experimental approaches.

The respiratory motor system employs homeostatic neuroplastic mechanisms at the spinal level to increase phrenic motor output in response to reduced neural activation of respiratory pathways (also called inactivity-induced inspiratory motor facilitation (iMF)). Under carefully controlled conditions, lowering inspired CO2 levels causes cessation of phrenic inspiratory output (central apnea). The authors have previously utilized a protocol of recurrent central apneas to elicit iMF in phrenic motor output. In the present study, authors utilize this neurophysiological outcome to test the impact of GIH on altering the neuroplastic capacity of adult rats. A key finding of this study is that GIH attenuates iMF in male rats. This attenuation is not observed in female rats. To test the role of inflammation (in particular microglia-driven inflammation), the authors employ two approaches to inactivate spinal inflammatory pathways or deplete microglia in adult male rats. Building upon the 29 out of 12982 differentially expressed genes in cervical spinal cord microglia in GIH vs GNX (control exposure rats), the authors targeted the NF-κB pathway using intrathecally delivered TPCA-1 (NF-κB inhibitory subunit (IκB) inhibitor). Indeed, spinal TPCA-1 application restored iMF in GIH-exposed male rats. The second approach employed global microglial depletion using an orally delivered CSF1R inhibitor Pexidartinib (PLX3397) to show that iMF could be provoked in GIH-exposed male rats. It is important to note that although the authors do not report changes in microglial expression in GIH vs. GNX rats, they conclude that there are alterations in microglial activation that contribute to the GIH-induced attenuation of the neuroplastic capacity of respiratory motor networks.

A few questions emerge from this study. In the previous study by the group investigating changes in the inflammatory profile of newborns exposed to GIH, Cox-2 mRNA expression was shown to be elevated in the spinal cords of male rats. This is an interesting finding that has not been tested in GIH-exposed adult male rats in this study and it would be interesting to follow up on whether these changes in microglial profiles are conserved from newborn to adult stages. Indeed, the authors identify additional changes in hypoxia-responsive signaling pathways of GIH rats whose role in impaired respiratory plasticity would be an exciting follow-up to the current study.

The authors emphasize that the reduction in iMF capacity is due to changes in local spinal microglia activation. They do also report that 4 genes were upregulated in the brainstem region of GIH rats as compared to GNX rats. Without an appropriate anatomical control (such as hypoglossal motor output), it would not be appropriate to conclude that microglial activation resulting from GIH has no impact on respiratory networks. Further, the inclusion of bursting frequency data could provide some insight into neural drive originating in brainstem regions.

In summary, this study by Mickelson et al. provides a valuable framework for mechanisms imposing long-lasting changes in respiratory motor control following gestational exposure to episodes of sleep apnea. Furthermore, the work completed here may very well be relevant to other motor systems in which spinal microglia modulate the capacity to elicit homeostatic plastic changes. These changes are particularly important in the context of disease and injury and may impair the capacity of GIH-exposed individuals to elicit neuroplastic changes at the motor neuron level.

Reviewer #3 (Public Review):

This is a clearly written, straightforward, resource paper describing the creation of several new cell lines that may prove useful to the Drosophila community. They are to be distributed through the Drosophila Genomics Resource Center and might be put to use at the Drosophila RNAi screening center.

Reviewer #3 (Public Review):

The manuscript by Kleynhans et al analyzes data from household contacts of SARS-CoV-2 cases at two sites in South Africa. Proximity sensors were distributed to household members following diagnosis of the "index case" and measured the frequency and duration of close contacts (defined as being face-to-face within 1.5 meters for at least 20 seconds). The authors then examined the association between the duration, frequency, and average duration of contacts and the risk of a diagnosis of SARS-CoV-2 among household members in the subsequent two weeks, for both contact with the index case and all cases within the household. The risk of infection among household members was high (~60%), but was not significantly associated with the contact metrics examined. The findings may indicate that aerosols may be the predominant mode of SARS-CoV-2 transmission within households; however, there are also a number of limitations associated with the design and analysis of the study, which the authors acknowledge and which may limit the interpretability of the conclusions of this study.

One important study limitation has to do with the design of the study: Sensors were not distributed to household members until a day or two after the diagnosis of the index case. Since individuals are most infectious with SARS-CoV-2 just prior to symptom onset, contact patterns were measured only after most transmission from the index case likely occurred. Furthermore, household members may have limited their contact with the index case, particularly if the index case attempted to isolate following their diagnosis, so the contact patterns measured are unlikely to be representative of typical mixing within the household.

Another important limitation has to do with the analytical approach: The logistic regression model assumes that the first person in the household to test positive for SARS-CoV-2 (i.e. the index case) infected all subsequent cases within the household. However, this approach does not account for chains of transmission within the household or transmission from outside the household (possibly from the same source that infected the index case). While this concern is partially addressed by also assessing the association between the risk of infection and contact with all infected household members, more sophisticated methods could be used to infer the most likely infector of each case. The possibility of multiple introductions of the virus from outside the household is also only partially addressed by excluding households in which more than one variant was detected. While these limitations (and others) are appropriately acknowledged by the authors in the Discussion, nevertheless they limit the conclusions that can be drawn from the study results.

It is also worth noting that the contact metrics as defined and analyzed in the model may not be the measures that are most relevant to transmission. The authors examined three different contact measures: the median daily duration of contact, the median daily frequency of contact, and the median daily average duration of contact (i.e. the ratio of the two previous measures). They chose to examine the median daily values because contact duration was heavily skewed and the number of days of follow-up varied after data cleaning, but it may be that longer-duration contacts important to transmission are not appropriately captured by these metrics. Indeed, the median daily duration of the contact is quite short (only ~18 minutes on average). It would be useful to also evaluate a measure such as the total cumulative duration of contact and frequency of contacts divided by the number of days of follow-up, which differs from the measures they calculate and would take into account more prolonged and frequent contacts.

Lastly, the measures of association reported in the manuscript are the odds ratios (ORs) associated with one additional second of contact per day. This is not a very biologically meaningful unit of measure, and when rounded to two significant digits, the ORs are not surprisingly 1.0 with 95% confidence intervals that also round to 1.0. It would be more interpretable to report the ORs associated with a 1-minute (rather than 1-second) increase in the duration of contact, and the biological interpretation of the ORs should be described in the text.

Reviewer #3 (Public Review):

Gene regulation at the single cell level can appear in two fundamentally different modes: a digital mode, in which a certain gene is either ON or OFF, and an analog mode, where a gene can gradually modulate its expression in a range of values. Yet, it is unclear how such two modes might operate together. In the work by Antoniou-Kourounioti et al, the authors argue that the Arabidopsis floral repressor FLOWERING LOCUS C (FLC) exhibits such two regulatory modes in the Arabidopsis root before cold exposure, with analog preceding digital.

This work has the strength of performing an elegant combination of experimental and modelling approach to solve a non-trivial and fundamental question on gene regulation. At the experimental level, the authors are able to quantify the number of FLC transcripts as well as their protein levels at the single cell level in the studied Arabidopsis lines, and they elegantly recapitulate some of their experimental results with an in silico root model.

Although this work has a very high potential, I find there are several important aspects that require some attention.

I think further explanations and clarity are needed to help the readership understand the differences between digital and analog regulation, beyond the explanations illustrated by Fig 1. In my understanding, digital regulation will involve observing some kind of bimodality when quantifying expression levels at the single cell level (see Bintu et al 2016), but from the definitions of ON and OFF cells the authors did in this work (see below), and the modelling they propose, it seems not to be the case. Given the authors derive very strong conclusions from their quantifications on what is digital and what is analog, I think it is important to be clearer in this regard. Also, to clarify the possible scenarios of interplay between analog and digital, I believe it would help to emphasize and better connect the modelling part to the experimental part.

Another major concern to me is whether the extracted conclusions rely too much on certain choices the authors made when doing the quantifications from the experimental data. In particular,

1) The way the authors define ON and OFF cells sounds a bit arbitrary to me and, in my understanding, can affect a lot the outcomes and derived conclusions. The authors define ON cells to those cells having more than one transcript, or when they are above the value of 0.5 of the Venus intensity measure - what would it happen if the thresholds are slightly above these levels? And why such thresholds should be the same for the studied lines Ler, fca-3 and fca-1? By looking at the distributions of mRNAs and Venus intensities in Ler and fca-3 plants, one could argue that all cells are in an OFF, 'silent' state, and that what is measured is some 'leakage', noise or simply cell heterogeneity in the expression levels. If there is a digital regulation, I would expect to see this bimodality more clearly at some point, as it was captured in Berry et al (2015) - perhaps cells in fca-1 show at a certain level of bimodality? When seeing bimodality, one could separate ON and OFF states by unmixing gaussians, or something in these lines that makes the definition less arbitrary and more robust.

2) The authors use means in all their plots for histograms and data, and perform tests that rely on these means. However, many of these plots are skewed right distributions, meaning that mean is not a good measure of center. I think using median would be more appropriate, and statistical tests should be rather done on medians instead of means. If tests using medians were performed, I believe that some of the pointed results will be less significant, and this will affect the conclusions of this work.

3) Some data might require more repeats, together with its quantification. For instance, the expression levels for fca-1 in Fig 2E and Fig 3D at 7 days after sowing look qualitatively different to me - not just the mean looks different, but also the distribution; fca-1 in Fig 3D looks more monomodal, while in Fig 2E it looks it shows more a bimodal distribution. Having these two different behaviours in these two repeats indicates that, more ideally, three repeats might be needed, together with their quantification. Fig. 2C would also need some repeats. In Fig 1S1 C and D, it would be good to clarify in which cases there are 2 or more repeats -3 repeats might be needed for those cases in Fig 1S1 C-D that have large error bars.

Also, when doing the time courses, I find it would be very beneficial to capture an earlier time point for all the lines, to see whether it is easier to capture the digital nature of the regulation. Note that the authors have already pointed that 7 days after sowing might be too late for Ler line to capture the switch.

If the above comments are addressed and the authors manage to clarify how the digital and analog regulation are integrated in the chosen system, I believe this work would have a strong impact on a very wide scientific community, given it tackles a very fundamental question in gene regulation.

Reviewer #3 (Public Review):

This article aims at investigating the genetic and developmental basis underlying colour pattern polymorphism in the wood tiger moth. It combines GWAS and QTL data pointing at a candidate gene from the yellow gene family. The pattern of gene expression during wing disk development is then consistent with a potential role of this gene in the control of colour pattern variation but functional validation is lacking. The pigment analyses reveal the presence of pheomelanin on the wings, whose synthesis is known to be controlled by a pathway regulated by genes from the yellow family. The identification of these pigments suggests that variations in the colours of the wings in this species could indeed be caused by the regulation of the yellow pathway. Although functional validation establishing the exact role of the valkea gene is lacking, the data provided are in line with a pleiotropic effect of controlled by a small region of the genome enabling the series of phenotypic variations associated with the white coloration. The duplication event restricted to a single haplotype also provides a convincing mechanism for the restriction of recombination in this genomic region. However, the fact that the valkea gene is truncated questions its functionality. It remains possible that the developmental switch could be rather caused by the variations detected in the non-coding part of the duplicated region, causing differential patterns of expression in different genes, including yellow-e. Some deeper discussion is needed on the putative role of the valkea gene vs. of the regulatory regions in controlling the developmental switch between yellow and white morphs.

Altogether, this interesting study provides original and important results on the genetic architecture underlying balanced polymorphism in the wild.

Reviewer #3 (Public Review):

In order to address their study question of a potential shared genetic predisposition to both smoking and DNA methylation level, they indicate that a MZ discordant pair analysis would be very powerful.

The authors draw on the well-characterized and very large prospective study of twins and family members from the Netherlands, the Netherlands Twin Register (NTR). Over 3000 cohort members have DNA methylation assessed by arrays (450k and Epic). Monozygotic twin pairs discordant and concordant for smoking are included in epigenome-wide analyses, and followed-up using enrichment and gene expression studies.

The results demonstrate that the strongest associations that have been seen in unrelated individuals (such as for AHRR) are seen in the discordant pairs but do not have the statistical power to confirm or reject weaker (yet consistently seen) associations

Some mention of the effect of second-hand smoke (SHS) could be made as it is an exposure to smoke not due to one's own active smoking. As twin pairs often reside together or are in frequent contact/visiting - MZs more than DZ and females more than males, SHS may be attenuating differences between current and non-current smokers in discordant pairs rather than shared genetics. Likewise twin pairs often have the same or related occupation, and if smoking is common at their typical workplace (even if they work at different companies/employers), the non-smoking twin may be exposed to more tobacco than an unrelated never-smoker.

The study sample should be better described, especially with regard to how smoking behavior was assessed, and whether the twins in pairs discordant for smoking differ in characteristics that can affect DNA methylation. These details would be essential for understanding to what degree the observed findings are attributable to smoking.

The study provides important information on the smoking methylation relationship and supports the generally held view that smoking has a direct effect on methylation. Hence, methylation changes are a useful biomarker of current and past smoking. The current results indicate that confounding due to shared genetics is unlikely to be a major factor but some role cannot be excluded.

Reviewer #3 (Public Review):

The manuscript entitled "Hippo signaling impairs alveolar epithelial regeneration in pulmonary fibrosis" is a rigorous and timely report detailing the significance of Hippo signaling, Taz and Yap in AT2/AT1 differentiation and the subsequent impact on the progression of lung fibrosis versus repair/ regeneration. The authors experimental design and results support their conclusions. The identification of the distinct effects of Taz and Yap in these processes highlight the pathway and specific molecules as potential therapeutic targets.

The major strengths of these studies lie in the rigor of the elegant transgenic developmental/adult injury-repair mouse models combined with spatial transcriptomics and analyses. The weaknesses include a lack of detail presented in the methods, some legends and discussion.

Reviewer #3 (Public Review):

This is an interesting manuscript with an important subject pertaining to the impact of COVID-19 pandemic on various delayed schedules of population-based cancer screening, leading to the reduction of screen-detected cancers and the possible upstaging cancers. The results were assessed by simulation model (Policy I modelling) with the demonstration of Australia scenarios including three major cancers, including breast cancer, colorectal cancer, and cervical cancer.

Assess the impacts of COVID-19 disruption to population cancer screening for three major cancers on short-term and long-term outcomes for policy analysis.

The merit of this study is to provide a series of simulated results under disruption scenarios but the weakness are several-fold including lacking of mortality estimates, inadequate assessments and inaccurate reports on missed cancers (interval cancers) and upstaging.

Policy analysis based on disruption scenario through the simulation model would be very informative to guide policy-makers for designing a salvage program to minimize the impacts of COVID-19 disruptions.

Direct reporting data on the empirical disruption scenario instead of relying on the sensitivity analysis of disruption scenario is more transparent and convincing for the public.

Reviewer #3 (Public Review):

Here, Buglak and coauthors describe the effect of Sun1 deficiency on endothelial junctions. Sun1 is a component of the LINC complex, connecting the inner nuclear membrane with the cytoskeleton. The authors show that in the absence of Sun1, the morphology of the endothelial adherens junction protein VE-cadherin is altered, indicative of increased internalization of VE-cadherin. The change in VE-cadherin dynamics correlates with decreased angiogenic sprouting as shown using in vivo and in vitro models. The study would benefit from a stricter presentation of the data and needs additional controls in certain analyses.

1. The authors implicate the changes in VE-cadherin morphology to be of consequence for "barrier function" and mention barrier function frequently throughout the text, for example in the heading on page 12: "SUN1 stabilizes endothelial cell-cell junctions and regulates barrier function". The concept of "barrier" implies the ability of endothelial cells to restrict the passage of molecules and cells across the vessel wall. This is tested only marginally (Suppl Fig 1F) and these data are not quantified. Increased leakage of 10kDa dextran in a P6-7 Sun1-deficient retina as shown here probably reflects the increased immaturity of the Sun1-deficient retinal vasculature. From these data, the authors cannot state that Sun1 regulates the barrier or barrier function (unclear what exactly the authors refer to when they make a distinction between the barrier as such on the one hand and barrier function on the other). The authors can, if they do more experiments, state that loss of Sun1 leads to increased leakage in the early postnatal stages in the retina. However, if they wish to characterize the vascular barrier, there is a wide range of other tissue that should be tested, in the presence and absence of disease. Moreover, a regulatory role for Sun1 would imply that Sun1 normally, possibly through changes in its expression levels, would modulate the barrier properties to allow more or less leakage in different circumstances. However, no such data are shown. The authors would need to go through their paper and remove statements regarding the regulation of the barrier and barrier function since these are conclusions that lack foundation.<br /> 2. In Fig 6g, the authors show that "depletion of GEF-H1 in endothelial cells that were also depleted for SUN1 rescued the destabilized cell-cell junctions observed with SUN1 KD alone". However, it is quite clear that Sun1 depletion also affects cell shape and cell alignment and this is not rescued by GEF-H1 depletion (Fig 6g). This should be described and commented on. Moreover please show the effects of GEF-H1 alone.<br /> 3. In Fig. 6a, the authors show rescue of junction morphology in Sun1-depleted cells by deletion of Nesprin1. The effect of Nesprin1 KD alone is missing.

Reviewer #3 (Public Review):

Genomic imprinting is a striking example of epigenetic inheritance in mammals with profound influence on growth and development. A powerful experimental approach to the study of imprinting involves reciprocal mouse F1 crosses; it allows direct assessment of the parent-of-origin effects in a genetically uniform setting that is also an order of magnitude richer in polymorphism than human samples. Use of RNA sequencing is a natural fit to systematic quantitative analysis of allele-specific expression; however, multiple RNA-seq studies of imprinting in F1 mouse tissues wildly disagree in the estimated numbers of novel imprinted genes and in the extent of allelic bias in these genes. In their study, Edwards et al. start with an observation that existing studies varied in their experimental design and data analysis procedures. To assess to what extent disagreements between findings are due to different data processing, they re-analyzed several published datasets using a single pipeline. Furthermore, they performed experimental validation of a number of the novel candidate imprinted genes using primer extension on RT-PCR products (pyrosequencing), to estimate the number of false positives.

Between re-analysis of RNA-seq datasets and the validation experiments, this study presents convincing evidence that most candidate novel imprinted genes are artefactual. The discordant predictions between studies remain even after processing all the data following ISoLDE protocol. Importantly, validated candidate genes tended to be on the periphery of known imprinted domains, suggesting that their boundaries are yet to be finalized.

This work brings into focus an important issue of reproducible analysis and interpretation of RNA sequencing data, especially the analysis of allele-specific expression, including in the specific case of imprinted genes. With novel molecular mechanisms described recently (such as H3K27me3-related parent-of origin gene regulation) and greater accuracy of measuring subtle allelic bias afforded by deep sequencing, the authors' suggested classification (canonical, weak canonical, non-canonical, and weakly biased) is a useful pragmatic step in dealing with the confusing terminology in different studies.

The authors make a strong case that the data analysis methods used in the analyzed studies are prone to false positives. However, the approaches they use are more of an invitation to further dialogue than a definitive recipe to follow. For example, the authors mention that combining the results of several analytical approaches should increase accuracy. However, if those approaches are erroneous, this could lead to two types of error: (1) tools might be erroneous in a similar way, then consistency of results might be taken as confirmation of correctness, (2) averaging results from tools with opposite biases would lead to loss of signal. In the long run, there is no substitute to developing statistically accurate tools and validating that they correctly deal with noise in the data. On the experimental side, Pyrosequencing also involves PCR. This does not change the main conclusions of this study but going forward, it is worth focusing on the methods less affected by amplification (such as allele-specific FISH, ddPCR, or direct RNA sequencing).

Reviewer #3 (Public Review):

In this manuscript, the authors studied the erythropoiesis and hematopoietic stem/progenitor cell (HSPC) phenotypes in a ribosome gene Rps12 mutant mouse model. They found that RpS12 is required for both steady and stress hematopoiesis. Mechanistically, RpS12+/- HSCs/MPPs exhibited increased cycling, loss of quiescence, protein translation rate, and apoptosis rates, which may be attributed to ERK and Akt/mTOR hyperactivation. Overall, this is a new mouse model that sheds light into our understanding of Rps gene function in murine hematopoiesis. The phenotypic and functional analysis of the mice are largely properly controlled, robust, and analyzed.

A major weakness of this work is its descriptive nature, without a clear mechanism that explains the phenotypes observed in RpS12+/- mice. It is possible that the counterintuitive activation of ERK/mTOR pathway and increased protein synthesis rate is a compensatory negative feedback. Direct mechanism of Rps12 loss could be studied by ths acute loss of Rps12, which is doable using their floxed mice. At the minimum, this can be done in mammalian hematopoietic cell lines.

Below are some specific concerns need to be addressed.

1. Line 226. The authors conclude that "Together, these results suggest that RpS12 plays an essential role in HSC function, including self-renewal and differentiation." The reviewer has three concerns regarding this conclusion and corresponding Figure3. 1) The data shows that RpS12+/- mice have decreased number of both total BM cells and multiple subpopulations of HSPCs. The frequency of HSPC subpopulations should also be shown to clarify if the decreased HSPC numbers arises from decreased total BM cellularity or proportionally decrease in frequency. 2) This figure characterizes phenotypic HSPC in BM by flow and lineage cells in PB by CBC. HSC function and differentiation are not really examined in this figure, except for the colony assay in Figure 3K. BMT data in Figure4 is actually for HSC function and differentiation. So the conclusion here should be rephrased. 3) Since all LT-, ST-HSCs, as well as all MPPs are decreased in number, how can the authors conclude that Rps12 is important for HSC differentiation? No experiments presented here were specifically designed to address HSC differentiation.

2. Figure 3A and 5E. The flow cytometry gating of HSC/MPP is not well performed or presented, especially HSC plot. Populations are not well separated by phenotypic markers. This concerns the validity of the quantification data.

3. It is very difficult to read bone marrow cytospin images in Fig 6F without annotation of cell types shown in the figure. It appears that WT and +/- looked remarkably different in terms of cell size and cell types. This mouse may have other profound phenotypes that need detailed examination, such as lineage cells in the BM and spleen, and colony assays for different types of progenitors, etc.

4. For all the intracellular phospho-flow shown in Fig7, both a negative control of a fluorescent 2nd antibody only and a positive stimulus should be included. It is very concerning that no significant changes of pAKT and pERK signaling (MFI) after SCF stimulation from the histogram in WT LSKs. There are no distinct peaks that indicate non-phospho-proteins and phospho-proteins. This casts doubt on the validity of results. It is possible though that Rsp12+/- have very high basal level of activation of pAKT/mTOR and pERK pathway. This again may point to a negative feedback mechanism of Rps12 haploinsufficiency.

5. The authors performed in vitro OP-Puro assay to assess the global protein translation in different HSPC subpopulations. 1) Can the authors provide more information about the incubation media, any cytokine or serum included? The incubation media with supplements may boost the overall translation status, although cells from WT and RpS12+/- are cultured side by side. Based on this, in vivo OP-Puro assay should be performed in both genotypes. 2) Polysome profiling assay should be performed in primary HSPCs, or at least in hematopoietic cell lines. It is plausible that RpS12 haploinsufficiency may affect the content of translational polysome fractions.

Reviewer #3 (Public Review):

Cumplido-Mayoral and colleagues' study focused on the brain-age paradigm in the context of Alzheimer's disease risk. The goal was to valid brain-age 'deltas' by assessing how they relate to Alzheimer's biomarkers and related neurodegenerative measures. They did this by training a new brain-age model on FreeSurfer phenotypes (cortical and subcortical) using the UK Biobank dataset. They then tested multiple datasets including ALFA, ADNI, OASIS, and EPAD, focusing on cognitively unimpaired people and people with mild cognitive impairment. Using brain-age deltas calculated in the test sets, the authors then tested associations with a range of dementia-related measures, including the presence of MCI, APOE e4, amyloid and tau positivity, white matter hyperintensity volume and NfL levels from plasma or CSF.

Strengths include using multiple independent datasets from different sources. This provides large sample sizes and access to different data types. Another strength is the efforts to understand drivers of brain age prediction, by using the SHAP technique. The authors include a newly trained brain-age prediction model, which appears to work as well as existing alternative methods.

A weakness is the number of tests conducted and the absence of multiple comparison corrections. A problem with the SHAP analysis is that it does not account for the correlated nature of the input features.

Overall, the study met the stated aims, and I anticipate the results to make a positive contribution to the research field. The results tended to support the conclusions, particularly regarding the relationship between brain-age delta and the markers of neurodegeneration, AD risk, and cerebrovascular health. The only concern around this is whether the number of tests conducted has inflated the type I error rate and resulted in some false positives. This could have been explored further. The conclusions are sex differences are less well supported by the evidence. While some delta-by-sex interactions were significant, others were not (e.g., Figure 3), however, the interpretation focuses only on the significant ones to support blanket statements about the differences between males and females with regard to neurodegeneration. Given the issues about multiple comparisons, this seems premature and somewhat uneven.

Reviewer #3 (Public Review):

The period that is examined is in the range (21 to 37GW) and uses tractography to delineate five distinct thalamocortical pathways. The paper generates anatomically constrained whole-brain connectomes for each gestational week. The authors parcellate the thalamus according to to streamline connectivity that has been published about two decades ago. The authors delineate the developing thalamocortical pathways and parcellate the fetal thalamus according to its cortical connectivity using diffusion tractography. The study included the primary motor cortex, primary sensory cortex, posterior parietal cortex, dorsolateral prefrontal cortex, and primary visual cortex. With the limitations of the method, the authors delineated five major thalamocortical pathways in each gestational week.

The study finds consistent and distinct origins of different tracts, resembling the adult topology of thalamic nuclei as early as 23W gestation. The study monitors the transient compartment of the subplate and intermediate zone, internal capsule, and establishes references to complement histological knowledge.

The paper's hypothesis is straightforward: "the biological processes occurring in different fetal compartments leads to predictable changes in diffusion metrics along tracts, reflecting the appearance and resolution of these transient zones." Study transient structures, such as subcortical plate or subplate. The authors predict that as subplate neurons disappear the tissue fraction is becoming relatively higher in the deep grey matter and the cortical plate and lower in the subplate. The authors investigate this by characterising the entire trajectory of tissue composition changes between the thalamus and the cortex, to explore the role of transient fetal brain developmental structures on white matter maturational trajectories. The authors demonstrate that along-tract sampling of diffusion metrics can capture temporal and compartmental differences in the second to the third trimester, reflecting the maturing neurobiology of the fetal brain described in histology studies.

Reviewer #3 (Public Review):

The manuscript approaches an important problem associated with mannose challenge and subsequent changes in metabolism and DNA replication. The researchers employed MPI-KO human cancer cells to explore the key mechanism behind the anti-cancer activity of mannose, and demonstrated that the large influx of mannose exceeding the capacity to metabolize it, that is, the onset of 'honeybee syndrome', induced dramatic metabolic remodeling that led to dNTP loss.

• They established MPI-KO human cancer cells using the CRISPR-Cas9 system, and exploited the mannose auxotrophy and sensitivity observed in MPI-KO mouse embryonic fibroblasts (MPI- KO MEFs) (DeRossi et al., 2006). The addition of a physiological concentration of mannose (50 μM, unchallenged) to culture medium supported the proliferation of MPI-KO MEFs. However, mannose challenge increased the sensitivity of MPI-KO HT1080 cells to DNA replication inhibitors (i.e., cisplatin and doxorubicin) when the cells had been preconditioned with excess 5 mannose prior to the drug treatment.<br /> • Thus, induction of honeybee syndrome suppresses cell proliferation and increases chemosensitivity in MPI-KO human cancer cell models.<br /> • These results suggest that mannose challenge severely impairs the entry of the cells into S phase and its progression to mitotic phase. Strikingly, however, switching of the mannose-challenge medium to the mannose-unchallenged medium after long-term mannose challenge (6 days) resulted in robust cell proliferation.<br /> • The researchers observed downregulation of proteins related to the cell cycle and DNA replication in mannose-challenged cells (Fig. 3A), which were enriched with the mini-chromosome maintenance 2-7 (MCM2-7) complex.<br /> • Together, these results indicate that mannose challenge disengages dormant origins from DNA synthesis during replication stress, thus exacerbating DNA damage.<br /> • Our finding that DNA synthesis from dormant origins during replication stress is highly sensitive to the dNTP pool size is in good agreement with the therapeutic advantages of RNR inhibition in enhancing the efficacy of radiochemotherapy (Kunos and Ivy, 2018).<br /> The work is of potentially great importance in understanding the action of mannose on cancer cells and the resulting sensitization to anti-cancer agents.

Reviewer #3 (Public Review):

The authors report on an interesting study that addresses the effects of a physical and dietary intervention on accelerated/decelerated brain ageing in obese individuals. More specifically, the authors examined potential associations between reductions in Body-Mass-Index (BMI) and a decrease in relative brain-predicted age after an 18-months period in N = 102 individuals. Brain age models were based on resting-state functional connectivity data. In addition to change in BMI, the authors also tested for associations between change in relative brain age and change in waist circumference, six liver markers, three glycemic markers, four lipid markers, and four MRI fat deposition measures. Moreover, change in self-reported consumption of food, stratified by categories such as 'processed food' and 'sweets and beverages', was tested for an association with change in relative brain age. Their analysis revealed no evidence for a general reduction in relative brain age in the tested sample. However, changes in BMI, as well as changes in several liver, glycemic, lipid, and fat-deposition markers showed significant covariation with changes in relative brain age. Three markers remained significant after additionally controlling for BMI, indicating an incremental contribution of these markers to change in relative brain age. Further associations were found for variables of subjective food consumption. The authors conclude that lifestyle interventions may have beneficial effects on brain aging.

Overall, the writing is concise and straightforward, and the langue and style are appropriate. A strength of the study is the longitudinal design that allows for addressing individual accelerations or decelerations in brain aging. Research on biological aging parameters has often been limited to cross-sectional analyses so inferences about intra-individual variation have frequently been drawn from inter-individual variation. The presented study allows, in fact, investigating within-person differences. Moreover, I very much appreciate that the authors seek to publish their code and materials online, although the respective GitHub project page did not appear to be set to 'public' at the time (error 404). Another strength of the study is that brain age models have been trained and validated in external samples. One further strength of this study is that it is based on a registered trial, which allows for the evaluation of the aims and motivation of the investigators and provides further insights into the primary and secondary outcomes measures (see the clinical trial identification code).

One weakness of the study is that no comparison between the active control group and the two experimental groups has been carried out, which would have enabled causal inferences on the potential effects of different types of interventions on changes in relative brain age. In this regard, it should also be noted that all groups underwent a lifestyle intervention. Hence, from an experimenter's perspective, it is problematic to conclude that lifestyle interventions may modulate brain age, given the lack of a control group without lifestyle intervention. This issue is fueled by the study title, which suggests a strong focus on the effects of lifestyle intervention. Technically, however, this study rather constitutes an investigation of the effects of successful weight loss/body fat reduction on brain age among participants who have taken part in a lifestyle intervention. In keeping with this, the provided information on the main effect of time on brain age is scarce, essentially limited to a sign test comparing the proportions of participants with an increase vs. decrease in relative brain age. Interestingly, this analysis did not suggest that the proportion of participants who benefit from the intervention (regarding brain age) significantly exceeds the number of participants who do not benefit. So strictly speaking, the data rather indicates that it's not the lifestyle intervention per sé that contributes to changes in brain age, but successful weight loss/body fat reduction. In sum, I feel that the authors' claims on the effects of the intervention cannot be underscored very well given the lack of a control group without lifestyle intervention.

Another major weakness is that no rationale is provided for why the authors use functional connectivity data instead of structural scans for their age estimation models. This gets even more evident in view of the relatively low prediction accuracies achieved in both the validation and test sets. My notion of the literature is that the vast majority of studies in this field implicate brain age models that were trained on structural MRI data, and these models have achieved way higher prediction accuracies. Along with the missing rationale, I feel that the low model performances require some more elaboration in the discussion section. To be clear, low prediction accuracies may be seen as a study result and, as such, they should not be considered as a quality criterion of the study. Nevertheless, the choice of functional MRI data and the relevance of the achieved model performances for subsequent association analysis needs to be addressed more thoroughly.

Reviewer #3 (Public Review):

This paper argues that it has developed an algorithm conceptually related to chemotaxis that provides a general mechanism for goal-directed behaviour in a biologically plausible neural form.

The method depends on substantial simplifying assumptions. The simulated animal effectively moves through an environment consisting of discrete locations and can reliably detect when it is in each location. Whenever it moves from one location to an adjacent location, it perfectly learns the connectivity between these two locations (changes the value in an adjacency matrix to 1). This creates a graph of connections that reflects the explored environment. In this graph, the current location gets input activation and this spreads to all connected nodes multiplied by a constant decay (adjusted to the branching number of the graph) so that as the number of connection steps increases the activation decreases. Some locations will be marked as goals through experiencing a resource of a specific identity there, and subsequently will be activated by an amount proportional to their distance in the graph from the current location, i.e., their activation will increase if the agent moves a step closer and decrease if it moves a step further away. Hence by making such exploratory movements, the animal can decide which way to move to obtain a specified goal.

I note here that it was not clear what purpose, other than increasing the effective range of activation, is served by having the goal input weights set based on the activation levels when the goal is obtained. As demonstrated in the homing behaviour, it is sufficient to just have a goal connected to a single location for the mechanism to work (i.e., the activation at that location increases if the animal takes a step closer to it); and as demonstrated by adding a new graph connection, goal activation is immediately altered in an appropriate way to exploit a new shortcut, without the goal weights corresponding to this graph change needing to be relearnt.

Given the abstractions introduced, it is clear that the biological task here has been reduced to the general problem of calculating the shortest path in a graph. That is, no real-world complications such as how to reliably recognise the same location when deciding that a new node should be introduced for a new location, or how to reliably execute movements between locations are addressed. Noise is only introduced as a 1% variability in the goal signal. It is therefore surprising that the main text provides almost no discussion of the conceptual relationship of this work to decades of previous work in calculating the shortest path in graphs, including a wide range of neural- and hardware-based algorithms, many of which have been presented in the context of brain circuits.

The connection to this work is briefly made in appendix A.1, where it is argued that the shortest path distance between two nodes in a directed graph can be calculated from equation 15, which depends only on the adjacency matrix and the decay parameter (provided the latter falls below a given value). It is not clear from the presentation whether this is a novel result. No direct reference is given for the derivation so I assume it is novel. But if this is a previously unknown solution to the general problem it deserves to be much more strongly featured and either way it needs to be appropriately set in the context of previous work.

Once this principle is grasped, the added value of the simulated results is somewhat limited. These show: 1) in practical terms, the spreading signal travels further for a smaller decay but becomes erratic as the decay parameter (map neuron gain) approaches its theoretical upper bound and decreases below noise levels beyond a certain distance. Both follow the theory. 2) that different graph structures can be acquired and used to approach goal locations (not surprising) .3) that simultaneous learning and exploitation of the graph only minimally affects the performance over starting with perfect knowledge of the graph. 4) that the parameters interact in expected ways. It might have been more impactful to explore whether the parameters could be dynamically tuned, based on the overall graph activity.

Perhaps the most biologically interesting aspect of the work is to demonstrate the effectiveness, for flexible behaviour, of keeping separate the latent learning of environmental structure and the association of specific environmental states to goals or values. This contrasts (as the authors discuss) with the standard reinforcement learning approach, for example, that tries to learn the value of states that lead to reward. Examples of flexibility include the homing behaviour (a goal state is learned before any of the map is learned) and the patrolling behaviour (a goal cell that monitors all states for how recently they were visited). It is also interesting to link the mechanism of exploration of neighbouring states to observed scanning behaviours in navigating animals.

The mapping to brain circuits is less convincing. Specifically, for the analogy to the mushroom body, it is not clear what connectivity (in the MB) is supposed to underlie the graph structure which is crucial to the whole concept. Is it assumed that Kenyon cell connections perform the activation spreading function and that these connections are sufficiently adaptable to rapidly learn the adjacency matrix? Is there any evidence for this? As discussed above, the possibility that an algorithm like 'endotaxis' could explain how the rodent place cell system could support trajectory planning has already been explored in previous work so it is not clear what additional insight is gained from the current model.

Reviewer #3 (Public Review):

Lauterbur et al. present an expansion of the whole-genome evolution simulation software "stdpopsim", which includes new features of the simulator itself, and 15 new species in their catalog of demographic models and genetic parameters (which previously had 6 species). The list of new species includes mostly animals (12), but also one species of plant, one of algae, and one of bacteria. While only five of the new animal species (and none of the other organisms) have a demographic model described in the catalog, those species showcase a variety of demographic models (e.g. extreme inbreeding of cattle). The authors describe in detail how to go about gathering genetic and demographic parameters from the literature, which is helpful for others aiming to add new species and demographic models to the stdpopsim catalog. This part of the paper is the most widely relevant not only for stdpopsim users but for any researcher performing population genomics simulations. This work is a concrete contribution towards increasing the number of users of population genomic simulations and improving reproducibility in research that uses this type of simulations.

Reviewer #3 (Public Review):

Dominici et al studied the effects of the type I PRMT inhibitor MS023 on skeletal muscle stem cells (MuSCs) and on muscle strength in dystrophin-deficient mdx mice. The authors observed an enhanced proliferative capacity of cultured MuSCs with an increase of Pax7+/MyoD- cells. The observations are more or less in line with previous studies of the same group, describing reduced differentiation but enhanced proliferation of MuSCs after genetic inactivation of Prmt1. scRNA-seq identified different subpopulations of MuSCs, showing a shift to increased Pax7 expression and elevated oxidative phosphorylation and glycolysis after treatment with MS023. Treatment of MuSC with MS023 during expansion in vitro enhanced engraftment of MuSCs and treatment of dystrophic mdx mice increased muscle strength.

Overall, the manuscript provides new insights into the beneficial effects of the type I PRMT inhibitor MS023 for skeletal muscle regeneration. The description of the MS023-induced transcriptional and metabolic changes in MuSC is interesting and the effects on MuSC transplantation and muscle strength are stunning. However, the proposed underlying mechanism, which is claimed to rely on the expansion of MuSC and 'reprograming' of MuSCs towards a "unique and previously uncharacterized identity" is not sufficiently supported. The extent of the description of scRNA-seq data is inappropriate. Some conclusions from the scRNA-seq data appear to be overinterpreted or are rather trivial. It remains completely unclear whether the MS023-stimulated increase of metabolic pathway activity (OXPHOS, glycolysis) plays any role for preserving stem cell properties of MuSC during expansion and improves engraftment. Additional functional and mechanistic studies are required to explore the underlying molecular processes. Furthermore, it remains completely unclear whether the acclaimed increase in grip and tetanic strength of mdx mice after MS023 treatment relies on enhanced expansion of MuSC mediated by PRMT1 inhibition.

Reviewer #3 (Public Review):

The strength of this article is that the experiment performed was successfully validated by previously published results. However, it would be useful to determine whether changes in protein levels correlated with changes in mRNA levels and whether or not the protein present was functional, and whether Stac3 was in fact stoichiometrically depleted in relation to Cacna1s. The authors suggest that the change in RyR1 protein levels may have a knock-on effect on the levels of other proteins, which is a reasonable claim, but no experiments (such as using RNAi) were performed to confirm this. The authors also claim that an adaptive response exists to compensate for deleterious mutations, which is indeed well-established (see dosage compensation in x-linked disorders between XX women and XY men, for example), and their experiment is consistent with this finding but does not itself show this on the level of cells, tissues, or the RyR itself.

Minor concerns.<br /> 1) In the abstract, the authors stated that skeletal muscle is responsible for voluntary movement. It is also responsible for non-voluntary. The abstract needs to be refocused on the mutation and on what we learn from this study. Please avoid vague statements like "we provide important insights to the pathophysiological mechanisms..." mainly when the study is descriptive and not mechanistic.<br /> 2) The author should bring up the mutation name, location and phenotype early in the introduction. This reviewer also suggests that the authors refocus the introduction on the mutation location in the 3D RyR1 structure (available cryo-EM structure), if there is any nearby ligand binding site, protomers junction or any other known interacting protein partners. This will help the reader to understand how this mutation could be important for the channel's function.

Reviewer #3 (Public Review):

This important study continues the development of normative models of neuroimaging-derived features initiated by themselves (Rutherford et al., 2022a) in two directions. First, the existing models - which were developed on structural imaging features - are complemented with features derived from functional networks. Second, these models are compared with the utilization of the features themselves in three different inference settings. Overall, the evaluation of the functional networks modeling yielded similar benchmarking metrics in agreement with their previous structural modeling. The study delivers strong evidence that normative models efficiently increased the statistical power in mass univariate group difference testing. The improvement in the other two inferential scenarios was less evident. However, normative modeling was not comparatively detrimental and should continue to be investigated.

The study showcases several major strengths:<br /> - The methodological approach is robustly supported by previous work and protocol definitions by the authors, mainly (Rutherford, 2022a; 2022b).<br /> - The intent of the manuscript is very clear, structured first with a confirmation of the soundness of their functional-networks model and second the "head-to-head" comparison (a term used in the abstract which effectively describes the aim) to alternative inference approaches.<br /> - The results of task 1 are very compelling. The other two tasks, while perhaps less robust, are definitely relevant to be part of the communication and help draw a more accurate picture of the role of normative models in years to come.<br /> - The manuscript is accompanied by a comprehensive set of tutorials, examples, documentation, and the sharing of code, models, and data. Sharing all these resources is a decisive effort toward research transparency that deserves full recognition as scientific scholarship.

As major weaknesses, I will speculate that some researchers could understand this work as incremental. Although there's continuity with the previous work of the authors (otherwise would be a weakness, in my opinion), my assessment is that the science in this manuscript should be considered new results and hence deserve independent communication.

Finally, I would like to highlight how normative modeling outperformed its "direct" (saving the removal of confounding factors) inference counterpart in task 1, providing solid evidence of the usefulness of normative models beyond the classical application in "easy" clinical decisions (I refer the readers to the manuscript, which elaborates on these aspects more appropriately and comprehensively).

Reviewer #3 (Public Review):

The manuscript presented the identification of an herbal drug combination via the approach of knowledge graph for the treatment of plasma cell mastitis (PCM), a breast inflammation with severe and intense clinical symptoms. The authors evaluated the efficacy of the herbal drug combination in clinical trial, which recruited 160 patients thus far (Trial number: NCT05530226). The clinical trial results showed that the herbal drug combination could significantly reduce the recurrence rate and reverse the clinical symptoms of PCM patients.

The manuscript provides strong evidence for the following,<br /> 1. The authors showed that, for the first time, knowledge graph is a useful approach for the identification of herbal drug combination towards plasma cell mastitis. This is novel because in the past, the design of formulae in TCM is solely based on the principle of 'syndrome differentiation'.<br /> 2. The herbal drug combination identified by knowledge graph can markedly suppress various inflammatory cytokines in serum and restore clinical symptoms of PCM patients.<br /> 3. The herbal drug combination could reduce the recurrence rate of PCM, a major obstacle for PCM treatment.

The major merit of the manuscript is that the authors introduced the concept of knowledge graph into the domain of herbal drugs or TCM. Namely, the authors designed a knowledge graph towards systematic immunity or immunotherapy based on massive data mining techniques. The authors successfully identified an herbal drug combination for PCM with the help of a scoring system. Moreover, the authors conducted a clinical trial study and the clinical data showed that the herbal drug combination holds great promise as an effective treatment for PCM. The weakness of the manuscript is that some details for the herbal drug combination and the clinical trial study are missing.

Reviewer #3 (Public Review):

In the proposed paper, the authors use a combination of case data and genetic data to characterise the impact of a dog vaccine campaign on rabies transmission on Pemba island. This represents an impressive set of data to answer key questions linked to rabies control. It is rare to see a combination of detailed genetic and epidemiology data from the same disease system. Overall, I thought it was an impressive paper. My only major concerns were with the phylogenetic analyses.

The phylogenetic analyses were difficult to understand. The authors use a phylogenetic framework to estimate the underlying number of rabid dogs per outbreak (171 in the first outbreak and 140 in the second one), but it was unclear to me where the information was coming from. From the supplementary material, it seems the authors build transmission trees consistent with the phylogenies. However, these are reliant on (a) a serial interval and (b) a dispersal kernel. There is no reference as to what serial interval distribution was used and how it was calculated. Similarly, there is no information on the dispersal kernel, including what data was used to fit it. I suspect that the serial interval for rabies (and probably the dispersal kernel) has a long tail, which would lead to substantial uncertainty in the transmission chains, however, I could not see uncertainty in the outbreak sizes.

Reviewer #3 (Public Review):

The authors previously reported a daily oscillation of the excitation/inhibition ratio occurs normally in layer 2/3 cortical neurons in wild-type mice. In this manuscript, they examined the E/I ratio in the primary visual cortex in two different autism mouse models and showed that the daily oscillation was disrupted in both, albeit in different ways. They further demonstrated that complementary changes in excitatory and inhibitory synaptic transmissions were underlying the disrupted E/I ratio, which is also accompanied by alterations in the endocannabinoid signaling but not sleep time in general.

Disruption of the E/I ratio (or balance) has been a major theme of proposed mechanisms underlying sensory and behavioral abnormalities observed in autism spectrum disorder patients and animal models. The demonstration and characterization of the shift/flattening of the daily oscillation of E/I in the two mouse models provide strong evidence for a disruption of the daily dynamic regulation of the E/I ratio instead of an overall change in the absolute level of E/I, at least in layer 2/3 pyramidal neurons in the visual cortex examined here. These results call for a re-visit of previous studies and offer a potential explanation to reconcile conflicting prior reports regarding the valence of E/I ratio changes in different autism models and brain areas, taking the recording time during the day into consideration. It also raises the question of how the dysregulated daily E/I oscillation affects brain functions. On the other hand, the dissociation of sleep and E/I oscillation observed in the autism models may also provide an opportunity to better understand the functional relevance of sleep-dependent E/I oscillation in a normal brain in the future.

Reviewer #3 (Public Review):

The paper by Cecon et al. presents a novel biosensor approach designed to study aspects of Tau aggregation that employ the luciferase-based NanoLuc Binary Technology (NanoBiT). The last decade has seen a rise in the number and variety of Tau biosensor systems, each with its own strengths and weaknesses to study various aspects of Tau aggregation. So far, these have proven to be extremely useful tools for the detection of proteopathic Tau molecules from different origins, by virtue of their capacity to induce easily detectable aggregation of the "endogenous" reporter Tau proteins in the intracellular environment, enabling for example to interrogate the structural features that render the protein pathogenic; in addition, they have been employed for screening of therapeutic candidates that can inhibit or slow down the aggregation process. As regards the study of the aggregation process itself, such systems encounter important limitations in that the modifications done to the protein likely impact reaction rates (both intramolecular and intermolecular interactions) and the aggregation mechanism itself. Additionally, the majority of them rely on overexpression systems, further altering the dynamics of physiological interactions. This paper implements a recently developed and commercially available technology based on nano-luciferase complementation, which has been used to study transient protein-protein interactions but not yet for Tau, and reports on its utility to study both inter- and intra-molecular interactions of Tau in live-cells and seeding activity of exogenously added Tau.

Strengths<br /> The field of Alzheimer's will benefit greatly from cellular models that enable faithful replication of aggregation mechanisms that occur intracellularly involving Tau. The elucidation of high-resolution molecular structures of Tau fibrils from cryo-electron microscopy and the realisation that fibrils from different tauopathies display characteristic folds point to altered cellular states that drive the intrinsically-disordered protein (IDP) Tau to adopt specific conformations that spur pathological aggregation processes. The aggregate burden is known now to correlate well with disease progression. Tau has otherwise been described as a highly soluble protein, yet under certain circumstances it adopts a misfolded conformation that in the proximity of other monomers can template further misfolding and spur aggregation. Several biosensor systems have been developed that detect proteopathic Tau with high sensitivity, most notably those that consist of cell lines expressing intracellular FRET pairs. These have been invaluable to the field and have served to demonstrate that seeding activity strongly correlates with disease aggressiveness in Alzheimer's patients (see Dujardin et al. Nat Med 2021), among other important contributions. There are however major limitations in using these models to study aggregation mechanisms in a cellular context in that they rely on significant structural modifications to the protein that alter the aggregation energy landscape, among other artefactual concerns (e.g., protein overexpression).<br /> This paper sets out to showcase the applicability of the NanoBiT technology on the strength of the considerably smaller size of the fusion proteins. which comprise one large BiT fragment of 17.6 kDa and a small complementation peptide of only 11 amino acids, compared to for instance the popular Tau RD P301S FRET biosensor line that relies on CFP and YFP (both ~27 kDa) Tau-fused constructs as FRET pairs. This is important for interrogating intracellular inter- and intra-molecular interactions as steric effects impact reaction rates and mechanisms. This, coupled with high sensitivity of the bioluminescence signal and amenability for high throughput, comprise the most important advantages of this approach.

Weaknesses<br /> Perhaps the most significant advantage (conceptually) of the NanoBiT technology in this context is the ability to create intramolecular interaction sensors by fusing the fragments to opposite termini. This is especially useful for the N- and C- termini of Tau which are known to be in proximity in certain conformations. The same can be achieved with fluorescence complementation yet with the caveat of introducing larger molecules. Nevertheless, regardless of the smaller dimensions of the fusion protein, the modifications are likely to still alter protein interaction dynamics - this is relevant to both intra- and inter-molecular sensors. While this may not always be a major concern when working with globular proteins, it should be a key consideration when studying Tau aggregation. The energy landscape of intrinsically disordered proteins is highly sensitive to even small structural changes, as exemplified by conformational changes in Tau that render this otherwise highly-soluble protein aggregation-prone. The interaction between the complementary small and large fragments of NanoBiT is reversible and weak (reported as 190 uM), but may still stabilise non-intrinsic conformations. Demonstrating that interaction and aggregation kinetics are not affected significantly compared to the native protein in vitro would be required to support the physiological relevance of the claims related to inter- and intra-molecular interactions.

An additional concern with the intramolecular sensor is the ability to discriminate whether interactions are indeed intramolecular and not intermolecular, this introduces a confound for instance in the interpretation that a reduction in signal with the WT Tau conformation sensor after treatment with colchicine suggest that microtubules stabilise Tau in a conformation where N- and C- termini of a Tau monomer are in proximity, when this could also well be due to intermolecular interactions, or a combination of both (see the continuous stretch of density of Tau along protofilaments in Kellogg et al. Science 2018). Furthermore, the colocalization data is not of high enough quality to support the claims regarding microtubule interactions, in fact there seems to be stronger colocalization with the intramolecular sensor than with the intermolecular one. Better quality images and co-localization analysis are needed to support these interpretations. The paper thus falls short of providing compelling data to regard this method as a physiologically-relevant approach to study Tau molecular interactions.

Artefactual problems stemming from the aforementioned alterations are likely not as important for their applicability as sensors, as other Tau biosensors have shown the ability to detect proteopathic forms in a way that reflects the severity of pathology in various contexts, regardless of whether the ensuing aggregates faithfully replicate those encountered in pathology. It would then be of interest to assess how the NanoBiT technology fares compared to alternative cell models in regard to sensitivity. The paper provides a response curve with tissue extracted from a mouse model of tauopathy. The extracts are not purified for tau which makes comparison with other data difficult given that the degree of tauopathy is model and mouse dependent. A more extensive evaluation of the sensing capacity would be needed to establish sensitivity in a meaningful way, for instance with Tau forms for which concentration can be more appropriately estimated, e.g., recombinant Tau and IP-purified extracts from mouse and human tissues, or a direct comparison with other methods.

Reviewer #3 (Public Review):

The authors set out to test the idea that memories involve a fast process (for the acquisition of new information) and a slow process (where these memories are progressively transferred/integrated into more-long term storage). The former process involves the hippocampus and the latter the cerebral cortex. This 'dual-learning' system theoretically allows for new learning without causing interference in the consolidation of older memories. They test this idea by artificially increasing plasticity in the pre-limbic cortex and measuring changes in different learning/memory tasks. They also examined electrophysiological changes in sleep, as sleep is linked to memory formation and synaptic plasticity.

The strengths of the study include a) meticulous analyses of a variety of electrophysiological measurements b) a combination of neurobiological and computational tools c) a largely comprehensive analysis of sleep-based changes. Some weaknesses include questions about the technique for increasing cortical plasticity (is this physiological?) and the absence of some additional experiments that would strengthen the conclusions. However, overall, the findings appear to support the general idea under examination.

This study is likely to be very impactful as it provides some really new information about these important neural processes, as well as data that challenges popular ideas about sleep and synaptic plasticity.

Reviewer #3 (Public Review):

The study by Silva et al details the discovery and evaluation of a third class of broadly cross-reactive anti-Spike antibody that binds a conserved hinge region in the S2 domain. After immunizing mice with a stabilized S2 protein from MERS and generating scFv phage libraries, the authors were able to identify antibody 3A3, which showed broad cross-reactivity with SARS2 (including Omicron BA.1), SARS1, MERS, and HKU1 spike proteins. Using a combination of a low-resolution cryo-EM structure and HDX mass spectrometry, the authors were able to map amino acids in the antibody paratope and spike epitope, the latter of which is the hinge region of the Spike S2 domain (residues 980-1005) that plays a critical role in pre- to -post-fusion conformational changes. Through well-executed and comprehensive mutagenesis, binding, and functional assays, the authors further validated critical residues that lead to antibody escape, which centered around the 2P residues and diminished viral entry. While 3A3 and an affinity-enhanced engineered version, RAY53, did not show potent in vitro neutralization against the authentic virus, the antibody was shown to recruit Fc effector functions for viral clearance, in vitro.

Overall, the conclusions of this paper are well supported by the data, but the usefulness of such antibodies is likely limited. The work can be strengthened by extending the analysis of 3A3-like antibodies in the context of human immune responses and in vivo effectiveness.

1. Isolation of 3A3 was achieved after the generation of scFv-phage libraries following immunization with a MERS S2-domain immunogen in a mouse model. The fact that 3A3 binds well to 2P-stabilized sequences and binding/neutralization is diminished upon reversion of 2P mutations back to the native spike sequence (Figures 3a, 4c, and 5b), suggest that such antibodies would likely not arise from natural infection. This contrasts the isolation of fusion peptide and stem helix-directed antibodies, which were isolated from both immunized animals and convalescent individuals. To make their results more solid regarding the use of such antibodies in future vaccine strategies, the authors should provide evidence that 3A3-like antibodies can be identified in human donors. For example, they could enrich donor-derived S2-specific antibodies that bind both MERS and SARS2 S2 domains and evaluate the fraction of antibodies that recognize the hinge-epitope using competition binding assays (either ELISA or BLI), which have commonly been used to map epitope-specific sera responses. This could also be achieved with nsEMPEM of polyclonal IgGs bound to S2 proteins.

2. The authors speculate in the discussion that strategies to enhance access to the hinge epitope, which may include ACE2-mimicking antibodies, could promote enhanced viral clearance. In addition to ACE2-mimicking antibodies, several antibodies have been described that bind the RBD and promote S1 shedding (see for instance mAb S2A4 - Piccoli et al, 2020, Cell). Several 2nd generation vaccine platforms utilize RBD-only immunogens that are likely to induce high titers of ACE2-mimicking and cross-reactive S1-shedding antibodies. Thus, adding in vitro neutralization and ADCC experiments to assess synergy between 3A3/RAY53 and such antibodies would booster this speculative claim and be of interest to many in the field developing strategies for pan-coronavirus therapies.

3. The authors provide in vitro evidence in Figure 5c,d for Fc-mediated viral clearance. While in vivo data to show effectiveness in animal models is ideal, additional in vitro data that utilize engineered constructs that modulate effector function (e.g., DLE (+) or LALA (-)) would boost the authors' claims regarding Fc-mediated viral clearance mechanisms by EA3/RAY53.

Reviewer #3 (Public Review):

In this manuscript, Li et. al, investigate whether epithelial or stromal Nphp2 loss, a gene causative of nephronophthisis (NPHP), drives polycystic kidney disease (PKD) and kidney fibrosis in a novel floxed model of Nphp2. The authors found that only epithelial and not stromal Nphp2 loss results in NPHP-like phenotypes in their mouse model. In addition, the authors show that concurrent cilia, via Ift88 loss, and Nphp2 loss within the kidney epithelium as well as HDAC inhibition results in less severe PKD/kidney fibrosis, as has been shown in mouse models of other non-syndromic forms of PKD, such as autosomal dominant PKD caused by mutations to Pkd1 or Pkd2.

The authors aimed to understand (1) whether the published NPHP phenotype (kidney cysts and fibrosis), known from the global Nphp2 knockout mouse, is driven by the function of NPHP2 in the kidney epithelium or stromal cells; (2) if kidney fibrosis in NPHP is linked to kidney damage caused by cysts, or independent and preceding of the PKD phenotype; (3) whether cilia are required, causative, or prohibitive of NPHP cystogenesis; and (4) if a broad spectrum HDAC inhibitor is a potential therapeutic approach for NPHP.

With the provided results, the authors established that epithelial Nphp2 loss is likely a predominant driver of PKD in their model; however, they cannot exclude that stromal NPHP2 does not play a role in cysts growth post-initiation because the authors failed to directly compare their cell type-specific models to a global cre knockout (e.g. Cagg-cre). In addition, it is possible that cyst initiation/growth upon stromal Nphp2 loss occurs substantially slower compared to epithelial Nphp2 loss. However, it seems the authors did not look at kidney phenotypes beyond 28 days of age. Publications from the ADPKD field suggest, that stromal Pkd1 loss initiates cystogenesis much slower than epithelial Pkd1 loss. Further, while the authors suggest that kidney fibrosis precedes cyst development, the results supporting this conclusion are limited to one time point, analyzing IF staining of a single marker that can be compared between non-cystic and cystic time points. These analyses need to be extended to make any firm conclusions.

The most interesting finding of the manuscript, and likely most impactful to the field, is, that loss of cilia within the setting of epithelial Nphp2 loss reduces PKD severity. This finding parallels published findings for Pkd1 and Pkd2 which are suggested to function in a cilia-dependent cyst-activation mechanism. Unfortunately, the here shown studies, do not add to the mechanistic insight beyond showing the descriptive finding. Most importantly, it remains unclear whether NPHP2 functions in the same pathway as polycystin-1 or -2 (the Pkd1, Pkd2 gene products) or in a separate independent pathway.

With respect to the HDAC preclinical studies, the authors show supporting data that a broad-spectrum HDAC inhibitor may be suitable for slowing cyst growth in their model of NPHP. Overall, these studies are not novel to the field, as HDAC inhibition has been shown to slow PKD progression in various models of PKD al while not in NPHP specifically. Further, the studies seem like an add-on, which does not directly link to the prior cell type-specific studies of NPHP2, and no mechanisms linking the two concepts are provided.

Reviewer #3 (Public Review):

Software UX design is not a trivial task and a point-and-click interface may become difficult to use or misleading when such design is not very well crafted. While Phantasus is a laudable effort to bring some of the out-of-the box transcriptomics workflows closer to the broader community of point-and-click users, there are a number of shortcomings that the authors may want to consider improving. Here I list the ones I found running Phantasus locally through the available Bioconductor package:

1. The feature of loading in one click one of the thousands of available GEO datasets is great. However, one important use of any such interfaces is the possibility for the users to analyze his/her own data. One of the standard formats for storing tables of RNA-seq counts are CSV files. However, if we try to upload from the computer a CSV file with expression data, such as the counts stored in the file GSE120660_PCamerge_hg38.csv.gz from https://www.ncbi.nlm.nih.gov/geo/query/acc.cgi?acc=GSE120660, a first problem is that the system does not recognize that the CSV file is compressed. A second problem is that it does not recognize that values are separated by commas, the very original CSV format, giving a cryptic error "columnVector is undefined". If we transform the CSV format into tab-separated values (TSV) format, then it works, but this constitutes already a first barrier for the target user of Phantasus.

2. Many RNA-seq processing pipelines use Ensembl annotations, which for the purpose of downstream interpretation of the analysis, need to be translated into HUGO gene symbols. When I try to annotate the rows to translate the<br /> Ensembl gene identifiers, I get the error

"There is no AnnotationDB on server. Ask administrator to put AnnotationDB sqlite databases in cacheDir/annotationdb folder"

3. When trying to normalize the RNA-seq counts, there are no standard options such as within-library (RPKM, FPKM) or between-library (TMM) normalization procedures. If I take log2(1+x) a new tab is created with the normalized data, but it's not easy to realize what happened because the tab has the same name as the previous one and while the colors of the heatmap changed to reflect the new scale of the data, this is quite subtle. This may cause that an unexperienced user to apply the same normalization step again on the normalized data. Ideally, the interface should lead the user through a pipeline, reducing unnecessary degrees of freedom associated with each step.

4. 4. Phantasus allows one to filter out lowly-expressed genes by averaging expression of genes across samples and discarding/selecting genes using some cutoff value on that average. This strategy is fine, but to make an informed decision on that cutoff it would be useful to see a density plot of those averages that would allow one to identify the modes of low and high expression and decide the cutoff value that separates them. It would be also nice to have an interface to the filterByExpr() function from the edgeR package, which provides more control on how to filter out lowly-expressed genes.

5. When attempting a differential expression (DE) analysis, a popup window appears saying:

"Your dataset is filtered. Limma will apply to unfiltered dataset. Consider using New Heat Map tool."

One of the main purposes of filtering lowly-expressed genes is mainly to conduct a DE analysis afterwards, so it does not make sense that the tool says that such an analysis will be done on the unfiltered dataset. The reference to the "New Heat Map tool" is vague and unclear where should the user look for that other tool, without any further information or link.

6. The DE analysis only allows for a two-sample group comparison, which is an important limitation in the question we may want to address. The construction of more complex designs could be graphically aided by using the ExploreModelMatrix Bioconductor package (Soneson et al, F1000Research, 2020).

7. When trying to perform a pathway analysis with FGSEA, I get the following error:

"Couldn't load FGSEA meta information. Please try again in a moment. Error: cannot open the connection In call: file(file, "rt")

Finally, there have been already some efforts to approach R and Bioconductor transcriptomics pipelines to point-and-click users, such as iSEE (Rue-Albrecht et al, 2018) and GeneTonic (Marini et al, 2021) but they are not compared or at least cited in the present work. One nice features of these two tools that I missed in Phantasus is the possibility of generating the R code that produces the analysis performed through the interface. This is important to provide a way to ensure the reproducibility of the analyses performed.

Reviewer #3 (Public Review):

The authors present in great detail a novel transfer of learning AI model architecture called diffRBM, which is based on the original RBM papers [Hinton, 2002, Hinton and Salakhutdinov, 2006]. They further show how this tool can be used to assess the immunogenicity of TCR positions and the importance of different by-position amino acid usages in creating this immunogenicity. They show that this novel method identifies all known important positions at least as well as existing analytical and structural methods, potentially in a more explanatory way.

Reviewer #3 (Public Review):

This manuscript uses novel techniques to examine the intracellular trafficking and membrane insertion of AMPA receptors to dissect the molecular mechanism involved in regulating these processes in neuronal cultures under basal conditions and during the induction of a chemical form of long-term potentiation (LTP). Specifically, they examine the role of the interaction of the GluA1 subunit with two neuronal proteins SAP97 and 4.1N. The manuscript uses a novel approach to synchronize and temporally control the release of GluA1-containing receptors from the ER and examine its trafficking through the Golgi and dendrites to the plasma membrane. This assay can measure the number of GluA1-containing intracellular vesicles, their speed of trafficking, and the delivery of newly synthesized GluA1 to the surface.

First, the authors use shRNA knockdown (KD) techniques to decrease the expression of SAP97 and 4.1 and found dramatic effects on the number of GluA1-containing vesicles and plasma membrane insertion of GluA1. SAP97 had a larger effect on trafficking while 4.1N had a larger effect on plasma membrane insertion. The authors then went on to use mutants of GluA1 that lack the whole C-terminal domain or mutations in the SAP97 and 4.1N biding sites in GluA1 C-termini and examine the trafficking of these mutants. These mutations decreased the intracellular trafficking and the membrane insertion of GluA1. In addition, the authors mutated phosphorylation sites that have been reported to regulate the interaction of GluA1 with 4.1N. Mutations in these sites that eliminated phosphorylation inhibits membrane insertion while the phosphomimetic mutations did not affect membrane insertion. Finally, mutations in the SAP97 and 4.1N binding sites including mutations in the phosphorylation sites also inhibited chemical-induced LTP increases in the regulation of GluA1 ER-Golgi exit, intracellular transport, and membrane insertion.

These studies are well done and novel and provide support for the role of the GluA1 C-termini and its protein interactors in the trafficking of the AMPA receptor under basal and plasticity conditions. This contributes new data using a novel approach to the controversy over the role of the C-termini of AMPA receptors in the regulation of AMPA receptor function. It supports the role of these interactions in AMPA receptor function.

Reviewer #3 (Public Review):

Darunavir (DRV) has been shown to be a potent HIV-1 protease inhibitor in individuals, has pM binding to the protease active site, has activity to protease inhibitor resistant HIV-1s, and has been reported to be difficult to develop resistance to individuals and in tissue culture. The authors argue that given published studies of generating HIV-1 resistance to DRV in tissue culture was not accomplished and all published studies started with either a drug-resistant virus or a combination of drug-resistant viruses for selection, new information can be gleaned as to the viral mutational pathways leading to drug-resistant viruses from HIV-1 wild type (no pre-existing drug mutations) NL4-3.

To better understand the development of HIV-1 wild-type DRV resistance, Spielvogel and colleagues detail their studies on characterizing HIV-1 protease genomic and structural alterations and viral fitness before and during the development of tissue culture resistance to DRV, as well as 10 new compounds (UMass compound series) based on DRV. The UMass compounds have distinct R1 and R2 groups as compared to DRV, which provides for a comprehensive chemical toolset to probe protease genetics and structural changes and alterations in viral fitness resulting during HIV protease drug resistance development in tissue culture. Differences in HIV protease resistance patterns developing over time combined with the potency of the protease inhibitors to HIV mutants resulting from inhibitor selections provide insights as to how DRV chemical groups impact resistance development. The manuscript is comprehensive, well-written, and informative, yet dense and with some figures that readers may not find informative.

Protease inhibitor tissue culture selection of wild-type NL4-3 was based on increasing protease inhibitor concentrations over time. Generally, the DRV resistance mutations that came up early de novo from wild-type NL4-3 virus were, 84V, followed by the acquisition of accessory mutations, predominately 54L and 82I, with 84V, 85V, 46I, 47V, 63P, and others as well, which became entrenched over time. The 84V mutational series have been reported for DRV as the authors noted. To determine the DRV selection pattern from pre-existing HIV single drug-resistant population a pool of 26 single mutant viruses was used for selection. Similar patterns were seen as for wild-type viruses, starting with 84V.

Interestingly, when the UMass compound series was used to select wild-type NL4-3 in tissue culture, 3 mutational series resulted, a protease mutational pattern similar to DRV (UMass 1, and 4, a protease mutational pattern starting with 50V, and followed by the predominate accessory mutations 10F, 13V, 33F, 46I, 63P, and 71V, but not 84V (UMass 3,6,7,8,9, and 10) and a mixture of both populations (UMass 2 and 5). When the HIV single drug-resistant population pool was used, which didn't contain 50V, was used for selection, UMass 2,4,7, and 8 retained the same mutational patterns as the original wild-type HIV selection, where, interestingly, UMass 6 utilized the 84V mutational pathway, rather than 50V, when the 84V mutation was pre-existing.

The results pointed out that modification of the DRV R2 and R1 groups alters selection patterns. It appears that a smaller hydrophobic side chain at the P1' position appears to drive towards 84V selection, whereas a larger side chain selects for the 50V pathway. UMass compounds 2, 5, 7, and 10 demonstrate the highest potency to both 50V/71V and 84V mutant viruses. Interestingly, UMass 2 and 5 were selected for both 50V/71V and 84V resistance mutational pathways, whereas 7 and 10 were selected for 50V/71V pathways.

Based on entry/replication studies, the authors argue that pushing viruses to select 50V/71V mutational pathways in protease, vs 84V mutational pathways in protease, promotes a higher genetic barrier to overcome resistance. This would be due to the reduction in fitness for the 50V/71V protease mutant and the large number of accessory mutants required to regain fitness. However, more in-depth analyses of the various mutants are warranted to support this point, such as head-to-head viral replication studies. A further limitation to the general conclusions is whether mutations in Gag provide for compensatory mutations to augment protease (and viral) fitness for the UMass compound findings.

Reviewer #3 (Public Review):

This manuscript provides a remarkably simple, yet effective, model of hippocampal replay. A replay event is stitched together as a chain of reactivated experiences. Individual experiences are prioritized for reactivation according to three intuitive measures: the spatial proximity of an experience to that previously reactivated, the frequency of and reward associated with an experience, and an inhibitory term that propagates the replay across space. Under certain conditions, their model can produce replays that are nearly as optimal--in terms of teaching a reinforcement learning agent to successfully navigate to a reward--as those produced by Mattar and Daw's 2018 model which, by design, generates the most behaviorally useful replays.

The authors assert that their model can recapitulate the replay statistics observed in a subset of experimental works, including the ability of replay to generate novel 'short cuts' from segments of past experience, the resemblance of replay to Brownian diffusion following random exploration, the ability of replay to steer around environmental barriers, and the observation of pre-play. These claims are generally well supported by the data presented (in particular, the model seems to be quite robust to different parameters).

One important caveat is that the proposed model requires two modes ('default' and 'reverse') to simultaneously account for empirical findings and provide behavioral utility (the performance of the agent is poor when using the default mode, but comparable with that of Mattar and Daw in the reverse mode). The authors suggest that the brain could dynamically switch between modes (dubbed the 'dynamic' mode). I feel that the paper would be strengthened by focusing on this dynamic mode throughout and demonstrating that it produces replays with statistics matching empirical data. For example, what is the distribution of forward and reverse replays produced by the default model (figure 3D)? Since neither mode by itself is adequately consistent with experimental findings, showing that the model appropriately switches between modes would strengthen its plausibility.

The authors state that their model is able to recapitulate the finding that replay in sleep following random exploration can be described by Brownian diffusion. A key point in that paper was that the preceding behavior was not diffusive. The authors go some way to address this point by showing that their model produces diffusive replays even if the strength of experience across space is not uniform. However, it isn't clear to me that modeling non-uniform experience strength is equivalent to modeling non-diffusive behaviorally trajectories. A more convincing test would have been to simulate realistic behavioral trajectories and show that subsequent replay events are still diffusive.

In my view, the fact that the model can generate 'pre-play' (in this case, replay of a visually cued, but unvisited arm of the maze) is not particularly informative. In order to generate pre-play, the authors allow the agent to 'visually explore' the cued arm. The implementation of this visual exploration is equivalent to allowing the agent a limited amount of real physical experience on the cued arm. Thus, the finding of replay for the cued arm is unsurprising. It would have been more useful to show that the model over-represents the rewarded arm on a T-maze, given equal exploration of the arms (as in Mattar and Daw).

Also debatable is the authors' assertion that their model is biologically plausible, while that of Mattar and Daw is not. While the former model is certainly computationally less expensive, little experimental data exists that could definitively point to the biological plausibility or implausibility of either model.

Overall, this model is impressive in its ability to generate replay events with realistic and varied statistics, using only a few simple rules. It will be a welcomed addition to the fields of replay, learning and memory, and reinforcement learning.

Reviewer #3 (Public Review):

Zhang, Q. et al. developed a two-photon fluorescence microscope (2PFM) by incorporating direct wavefront sensing adaptive optics (AO), which is optimized for mouse in vivo retinal imaging. By using the same 2PFM with the option of using or not using the incorporated AO system, this team compared the in vivo retinal images and convincingly demonstrated that AO correction acquired brighter and higher resolution images of retinal ganglion cells (RGCs) and their axons in both densely and sparse labeled transgenic mouse lines, normal and defected capillary vasculatures, and RGC spontaneous activities detected by genetic Ca2+ sensor. Interestingly and importantly, this team found that a global correction by removing the common aberration from the entire FOV enhances imaging signals throughout the entire large FOV, indicating a preferable AO imaging strategy for large FOVs. The potential applications of the in vivo retinal imaging techniques and strategies developed by this study will certainly inspire further investigation of the dynamic morphological and functional changes of retinal vasculatures and neurons during disease progression and before and after treatments.

It would be beneficial to the manuscript and the readers if the authors can elaborate on optic design a little bit more. For example, whether the incorporation of AO adversely affects the 2PFM optic design? If the 2PFM can be further optimized by uncompromised optic design without incorporating AO, the quality of in vivo images will comparable to the AO-2PFM or not?

Reviewer #3 (Public Review):

In this manuscript Zhao et al investigated how multiple Rab27 effectors work to regulate insulin secretion by murine pancreatic b-cells. They do this by comparing the phenotypes of b-cells/islets lacking effectors doubly or singly. Their main findings/contributions are that:

Mlph works downstream of Myrip/exophilin-8 to mobilise granules for fusion from the actin network to the plasma membrane after stimulation.

Mlph and exophilin-8 interact via the exocyst

Down-regulation of exocyst affects exocytosis in cells expressing exophilin-8

Exophilin-8 promotes fusion of granules docked by granuphilin at the membrane

Exophilin-8 not required for Grph related granule docking at the plasma membrane

A model for how the three effectors coordinate ISG secretion. According to this model there are 2 insulin secretion pathways in b-cells; a) where Exo8 acts upstream of Mlph and with actin/Myosin Va/VIIa, exocyst and syntaxin 4 to move dock granules in actin and promote exocytosis, and b) where Exo8 works in an antagonistic manner with Grph promoting secretion of granules docked at the membrane by Grph.

This is an interesting/important question and the authors make important contributions (above). In general experiments are well designed and controlled but there are some questions that remain open that could have been included to make the study a more comprehensive analysis of Rab27 effectors in insulin secretion.

Reviewer #3 (Public Review):

By popular single-cell RNA-seq, the authors identified FOXC2 as an undifferentiated spermatogonia-specific expressed gene. The FOXC2+-SSCs can sufficiently initiate and sustain spermatogenesis, the ablation of this subgroup results in the depletion of the uSPG pool. The authors provide further evidence to show that this gene is essential for SSCs maintenance by negatively regulating the cell cycle in adult mice, thus well-established FOXC2 as a key regulator of SSCs quiescent state.

The experiments are well-designed and conducted, the overall conclusions are convincing. This work will be of interest to stem cell and reproductive biologists.

Reviewer #3 (Public Review):

In this manuscript, the authors examine the role of VAPA in focal adhesion (FA) turnover and cell motility via effects on ER-PM contact site functions. The authors show that VAPA KO CaCo2 cells form larger FA and have aberrant migration behavior and spreading. Those cells show lower levels of PI(4,5)P2 at PM, but no change in PI(4)P at Golgi and endosomes. PI(4)P is not tested at the PM. The authors show that VAPA KO cells have a similar number but less stable GFP-MAPPER positive ER-PM contact sites as compared to control cells. In contrast, FA are more stable over time in VAPA KO. The authors also aimed to evaluate GFP-MAPPER proximity with vinculin spots and concluded that ER-PM contacts partially overlap with FA, whereas they are more distant in VAPA KO. Thus, a correlation between stable contact sites near FA and FA disassembly likely exists. From this set of data, the authors suggest that VAPA has a key role at ER-PM contacts near FA by mediating lipid transfer, which ultimately enables internalization of integrins and FA disassembly.

The approach in the paper is innovative and interesting because VAPA is a major tether at contact sites and the link between contact sites and cytoskeleton dynamics and cell motility remains little explored. This can potentially lead to significant advances in the field. The experiments presented are technically well executed, but most of the results and hypotheses arising from VAPA KO cells are not tested by rescue experiments with exogenous VAPA and VAPA mutants. Although the proposed role for VAPA might fit with the data, the final model is not experimentally tested and is thus highly speculative. The role of VAPA at ER-PM contact sites near FA, and the direct link between VAPA, PI(4,5P)2, and FA disassembly, are not established. VAPA is not shown at ER-PM contacts in the manuscript. Some controls are missing and statistics must be improved. In summary, this work seems to be on the right track, but looks quite preliminary.

Reviewer #3 (Public Review):

Macrophage colony-stimulating factor (M-CSF) plays key roles in the differentiation of myeloid-lineage cells, including monocytes, macrophages and osteoclasts. The latter mediate bone resorption, which is important for physiological bone remodelling but, unrestrained, contributes to bone loss in conditions such as in post-menopausal osteoporosis. M-CSF production within the bone marrow is implicated in the maintenance of myeloid and skeletal homeostasis, but the cellular source of bone marrow M-CSF has remained elusive. In this study, Inoue et al address this issue through advanced transcriptomic and gene targeting approaches. They conclude that a population of Adipoq-expressing progenitors within the bone marrow, designated "AdipoQ-lineage progenitors", is the key cellular source of M-CSF. Consistent with this, they find that transgenic deletion of M-CSF from these cells disrupts macrophage and osteoclast development, leading to osteopetrosis and possibly preventing bone loss following ovariectomy. However, they have not adequately addressed the possibility that M-CSF production from other cell types, particularly adipocytes in peripheral adipose tissues, may also be influencing these phenotypes. Specific strengths and weaknesses are as follows:

Strengths:

1. The manuscript is written in a clear, succinct manner and the data are generally nicely presented. It is therefore a pleasure to read.

2. The analysis of single-cell transcriptomic data is clear and convincing, and the skeletal phenotyping has been done to a high standard.

Weaknesses:

1. The authors underplay the potential contribution of M-CSF production from other cell types, particularly from adipocytes in peripheral adipose tissues. They show that M-CSF expression from these cells is lower than from the bone marrow progenitors that they focus on; however, based on this they allude to "no expression" of M-CSF from these other adipocytes. This overlooks the findings of other studies showing that peripheral adipocytes produce M-CSF and that this has biological functions. Whether their knockout model alters M-CSF expression in peripheral adipose tissue, whether for whole tissue or for isolated adipocytes, has not been tested.

2. The decreases in M-CSF have been assessed at the transcript level, but not for M-CSF protein. Whether their knockout model

3. It is also unclear if the Adipoq-lineage progenitors consist exclusively of adipogenic cells, or if osteogenic progenitors are also part of this population.

If these weaknesses are addressed then this work has potential to yield firm conclusions and new insights into the regulation of myeloid and skeletal homeostasis, both in normal physiology and in clinically relevant conditions.

Reviewer #3 (Public Review):

In this study, the authors sought to develop an ex vivo organ culture system that would allow for long-term (>12 hours) live imaging of the lymph gland (LG), the hematopoietic organ in Drosophila, in order to gain insights into the process of differentiation during hematopoiesis. The authors successfully built such a system through trial and error and showed that the LG could survive for over 12 hours and that it recapitulated many of the aspects seen in in vivo LGs.

The authors also developed sophisticated quantitative image analysis tools that allowed them to identify new modes of differentiation that may help explain the cellular heterogeneity previously seen by other groups. Furthermore, they were able to follow mitosis in real-time and showed evidence that not only can progenitors undergo symmetric cell division but that mitosis shows some orientation bias which may help explain the overall structure of the organ. The authors went on to show that upon infection, modes of differentiation and mitosis orientation seem to shift, but they did not provide any mechanistic insight into how this may occur or whether these shifts would impact the final cell fate or function of the mature hemocytes. Nevertheless, the identification and description of these patterns are in itself helpful and informative and provide a basis for future studies delving into these mechanistic questions.

The major strengths of the methods include the advancement in live-imaging technology and the development of quantitative image analysis tools. Weaknesses of the results include small sample sizes (and relatively high p-values), which limit the strength and breadth of some conclusions. This is to be expected as there is a trade-off between long-term live imaging of individual samples and sample number, nevertheless, it represents a minor weakness. Overall this weakness is overshadowed by the strength of the advancements afforded by live imaging and following in real-time the process of differentiation and mitosis. Furthermore, the quantitative analysis tools developed and used in this study can be applied across multiple subfields and represents an important step forward in the field.

The evidence presented here is generally solid and the results tend to support their conclusions although some specific conclusions are supported by data with no p-values noted or relatively high p-values and low correlation coefficients, and so should be interpreted with this in mind.

This study represents a compelling and convincing theoretical and technical advance in efforts to understand hematopoiesis in flies. This is a powerful and versatile system that will allow for not only genetic manipulation of the LG but also of the tissues co-cultured with the LG to elucidate the mechanisms that control various signaling pathways during homeostasis. In fact, which additional tissues (like the fat body and brain) that had to be included in the co-culture system in order for the LG to survive recapitulate what past studies have shown about where key signals come from that help maintain homeostasis in the LG.

One caveat of the work is that because the authors used Eater-DsRed to follow differentiation, these modes may only apply to the formation of plasmatocytes and not necessarily crystal cells, which the authors noted do not tend to go through an Eater-DsRed intermediate state. Future work using this live-imaging system and image analysis tools to study the formation of the various mature cell types in flies will be a valuable addition to the field.

The methods developed here will be highly useful to both the specific subfield and to the general scientific community and will likely spark new insights into the process of hematopoiesis when combined with different markers and genetic manipulations, as outlined by the authors in the discussion. Future studies that explore whether the different modes of differentiation identified here ultimately result in divergent cell fates for the mature hemocytes will be important for understanding the significance of the findings more generally. But the identification of changes in the ratios and rates of the modes of differentiation upon infection with E.coli suggests functional ramifications of the different modes. It will be interesting to see if other types of infection or systemic stresses cause similar or different changes in differentiation modes.

Reviewer #3 (Public Review):

The method of ATRAP provides a useful workflow for processing and analysing single-cell sequencing data of TCRs and barcoded pMHC. The method addresses an important subfield of research, as the availability of these datasets is increasing substantially due to the wider availability of commercial reagents and tools.

Overall the study is highly technical and can be considered almost a "user manual" to assist researchers who pursue this TCR-pMHC specificity experiments by single-cell sequencing. Convincing experimental work, data analysis, appropriate controls, and technical details are provided throughout.

Reviewer #3 (Public Review):

Cancer cell populations co-evolve under the pressure exerted by the recognition of tumor-associated antigens by the adaptive immune system. Here, George and Levine analyze how cancers could dynamically adapt the rate of tumor-associated antigen loss to optimize their probability of escape. This is an interesting hypothesis that if confirmed experimentally could potentially inform treatments. The authors analyze mathematically how such optimally adapting tumors gain and lose tumor-associated antigens over time. By simplifying the complex interplay of immune recognition and tumor evolution in a toy model, the authors are able to study questions of practical interest analytically or through stochastic simulations. They show how different model parameters relating to the tumor microenvironment and immune surveillance lead to different dynamics of tumor immunogenicity, and more immunologically hot or cold tumors.

Simple models are important because they allow an exhaustive study of dynamical regimes for different parameters, such as has been done elegantly in this study. However, in this quest for simplification, the authors have not considered biological features that are likely to be of importance for understanding the process of cancer immune co-evolution in generality: tumor heterogeneity and immune recognition that only stochastically results in cancer elimination. In this sense, this paper might be seen as the opening act in a series of more sophisticated models, and the authors discuss avenues towards such further developments.

Reviewer #3 (Public Review):

Overall, this is an interesting and well performed study that described a comprehensive landscape of m1A modification in primary neuron and investigated the role of m1A in the circRNA/lncRNA‒miRNA-mRNA regulatory network following OGD/R. The focus on the two different complex regulatory networks for differential expression and differential methylation is important and it will be a valuable resource for the research community that focuses on epitranscriptomics and central nerve system diseases. Collectively, the authors present an exciting piece of work that certainly adds to the literature regarding epitranscriptomic features in neuron. While interesting results obtained and the paper is nicely written, I have the following suggestions for minor revisions to improve the paper.

1. The authors have explored the role of m1A modification in neuron, but it would have been helpful if the authors described the significance of these findings in depth in some sections (Figure 5 and Figure 6) to enhance the value of the article.<br /> 2. The authors should describe in detail the current research state of m1A modification and the significance of this study to the field of epitranscriptomics in the introduction and discussion section.

Reviewer #3 (Public Review):

In this work, the authors find that similar to mammals, sialylation is critical in neurons within flies, yet in flies the critical substrate for sialylation, CMP-Neu5Ac, is 'outsourced' to glial cells. These findings are shown through an extensive array of knockout, knockdown, and transgenic flies where CMP-Neu5Ac biosynthesis and sialyltransferase expression is modulated in either glial cells or neurons. The importance of sialylation in neurons is demonstrated by showing that sialylation impacts the expression levels of a critical voltage-gated ion channel.

This elegant work dissecting sialylation in the fly brain convincingly demonstrates the requirement for glial cells in the process of sialylation of neurons and deserves to be published. The major unaddressed question remaining is precisely how the CMP-Neu5Ac is delivered from the glial cells to neurons with several possibilities that merit further discussion including (but not limited to): extracellular vesicles, receptor-mediated uptake (unlikely but can't be ruled out), or exocytosis. The authors could make the point stronger that CMP-Neu5Ac should not be able to cross the neuronal membrane (or the Golgi membrane for that matter), requiring specific transport mechanisms.

Reviewer #3 (Public Review):

This work compares transcriptional responses of shoots and roots harvested from four plate-based assays that simulate drought and from plants subjected to water deficit in pots using the model plant Arabidopsis thaliana with the aim to select a plate-based assay that best recapitulates transcriptional changes that are observed during water-deficit in pots. Polyethylene glycol (PEG), mannitol, and sodium chloride (salt) treatments that are commonly used by molecular biologists to simulate drought were used for the plate-based assays as well as a new assay that uses increased concentrations of agar and nutrients to elicit drought which was developed by the authors and termed a 'low-water agar' assay since the amount of water added to the media mix and plates was lowered. Plants in pots were grown on vermiculite with the same nutrient mix as used in the plates and drought was induced by withholding watering for five days. Additionally, treatment with abscisic acid was conducted to study whether growth on plates itself led to artifacts compared to water deficit in pots. Shoot and root samples were harvested from all treatments for RNA sequencing analysis and differentially expressed genes were called against control samples.

The authors observed that gene expression responses of roots in their 'low-water agar' assay resembled more closely the water deficit in pots compared to the PEG, mannitol, and salt treatments (all at the highest dose). In particular, 28 % of PEG led to the down-regulation of many genes that were up-regulated under drought in pots. Through GO term analysis, it was pointed out that this may be due to the negative effect of PEG on oxygen solubility since downregulated genes were over-represented in oxygen-related categories. The data also shows that the treatment with abscisic acid on plates was very good at simulating drought in roots. Gene expression changes in shoots showed generally a high concordance between all treatments at the highest dose and water deficit in pots, with mannitol being the closest match. This is surprising, since plants grow in plates under non-transpiring conditions, while a mismatch between water loss by transpiration on water supply via the roots leads to drought symptoms such as wilting in pot and field-grown plants. The authors concluded that their 'low-water agar' assay provides a better alternative to simulate drought on plates.

Strengths:

The development of a more robust assay to simulate drought on plates to allow for high-throughput screening is certainly an important goal since many phenotypes that are discovered on plates cannot be recapitulated on the soil. Adding less water to the media mix and thereby increasing agar strength and nutrient concentration appears to be a good approach since nutrients are also concentrated in soils during water deficit, as pointed out by the authors. To my knowledge, this approach has not specifically been used to simulate drought on plates previously. Comparing their new 'low-water agar' assay to popular treatments with PEG, mannitol, salt, and abscisic acid, as well as plants grown in pots on vermiculite led to a comprehensive overview of how these treatments affect gene expression changes that surpass previous studies. It is promising that the impact of 'low-water agar' on the shoot size of 20 diverse Arabidopsis accessions shows some association with plant fitness under drought in the field. Their methodology could be powerful in identifying a better substitute for plate-based high-throughput drought assays that have an emphasis on gene expression changes.

Weaknesses:

While the authors use a good methodological framework to compare the different drought treatments, gene expression changes were only compared between the highest dose of each stress assay (Fig. 2B, 3B). From Fig. 1F it appears that gene expression changes depend significantly on the level of stress that is imposed. Therefore, their conclusion that the 'low-water agar' assay is better at simulating drought is only valid when comparing the highest dose of each treatment and only for gene expression changes in roots. Considering how comparable different levels of stress were in this study leads to another weakness. The authors correctly point out that PEG, mannitol, and salt are used due to their ability to lower the water potential through an increase in osmotic strength (L. 45/46). In soils, water deficit leads to lower water potential, due to the concentration of nutrients (as pointed out in L. 171), as well as higher adhesion forces of water molecules to soil particles and a decline in soil hydraulic conductivity for water, which causes an imbalance between supply and demand (see Juenger and Verslues, The Plant Cell 2022 for a recent review). While the authors selected three different doses for each treatment that are commonly used in the literature, these are not necessarily comparable on a physiological level. For example, 200 mM mannitol has an approximate osmotic potential of around -5 bar (Michel et al. Plant Physiol. 1983) whereas 28 % PEG has an osmotic potential closer to -10 bar (Michel et al. Plant Physiol. 1973). It also remains unclear how the increase in agar concentration versus the increase in nutrient concentration in the 'low-water agar' affect water potentials. For these reasons it cannot be known whether a better match of the 'low-water agar' at the 28% dose to water deficit in pots for roots in comparison to the other treatments is due to a good match in stress levels with the 'low-water agar' or adverse side-effect of PEG, mannitol, or and salt on gene regulation. Lastly, since only two biological replicates for RNA sequencing were collected per treatment, it is not possible to know how much variance exists and if this variance is greater than the treatments themselves.

Reviewer #3 (Public Review):

This study focuses on the role of the chromatin remodeller ISWI in Cryptococcus. The authors show that a) ISWI modulates Cryptococcus' ability to grow in the presence of antifungal drugs and b) ISWI post-translational modifications (Acetylation and Ubiquitination) regulate ISWI protein stability. The observation that post-translational modifications regulate ISWI activity and stability is exciting and it could unveil novel mechanisms to rapidly and reversibly regulate the response to antifungal drug treatments. However, the study lacks a fundamental characterisation of ISWI. This information is essential to understand the mechanistic regulations of ISWI in Cryptococcus and how it mediates drug response. The following are questions that should be addressed:

1. ISWI chromatin remodellers are well-characterised in many organisms. How many ISWI proteins does Cryptococcus contain? Why did the authors focus on ISWI?<br /> 2. What is the ISWI protein complex(es)? The Mass-Spec analysis should reveal this.<br /> 3. Is Cryptococcus ISWI a transcriptional activator or repressor?<br /> 4. Is ISWI function in drug resistance linked to its chromatin remodelling activity?<br /> 5. Does ISWI interact with chromatin? If so, which are ISWI-target genes? Does drug treatment modulate chromatin binding?

Reviewer #3 (Public Review):

The work from Dupuy et al aims to characterize the mutagenic effects of two DinB homologs of Mycobacteria, DinB2, and DinB3. The manuscript shows solid and convincing biochemical data about slippage promoted by DinB 2 on various homopolymeric templates. Overall, this study makes a solid contribution to the understanding of the properties of polymerases from the different DinB subfamilies of bacteria, although some points of the in vivo experiments should be critically evaluated by the readers as described below.

In vivo DinB2 is the more mutagenic of the two and is toxic when overexpressed. Nevertheless, these results are obtained with the overexpression of the polymerases and should be interpreted with caution. In this sense, it would have been interesting to have a quantification of how much overexpression the plasmids constructs achieve in the conditions used in the experiments, for a better assessment of the relevance of the data. For example, a physiological 10-fold increase in the expression of DinB2 is mentioned in the discussion - would that be close to what is achieved with plasmid-based overexpression?

The finding of kanR CFUs without any detectable mutations in the kan marker is worrisome and should be better discussed in the text. The same for sacB data in supplementary material. The explanation given in lines 216-218 does not make sense. Markers 7G and 8G clearly are barely measuring any mutagenesis. I think that the experiments in which most of the supposed KanR revertants actually have no Kan mutation should either be removed from the manuscript or better discussed, because it is uncertain what they are measuring, therefore no conclusion can be drawn from them. For the Kan markers, one possible explanation is that translational frameshifts are occurring and allow residual growth of some of the cells. Gene amplification as seen in the lac system of Cairns and Foster in E. coli could also promote growth without actual mutations. Is the KanR phenotype of these colonies heritable and stable?

Also, spontaneous mutagenesis should have been more precisely measured by using fluctuation analysis of larger sample sizes. In many instances, the results shown are the means of a few cultures with very large differences in mutant frequencies (several hundred-fold - e.g. Figures 4C, D and E, 5C and F, S3). Authors could discuss/explain their choice of statistical analysis and sample sizes.

Reviewer #3 (Public Review):

In this manuscript, Kidwell & Casalini, et al. use cell biology and functional approaches to investigate the dynamics and consequences mitochondrial transfer from macrophages to breast cancer cells. Unlike prior studies that emphasize the metabolic benefits of mitochondrial reconstitution in cells with defective mitochondrial DNA, they ask how mitochondrial transfer affects breast cancer cells with intact mitochondria. They observe that macrophage co-culture or "bathing" breast cancer cells in isolated mitochondria from macrophages results in low frequency mitochondrial transfer, which increases cell cycling, ERK signaling, and cell proliferation rate of recipient cells. Interestingly, fluorescent dyes and sensors were used to determine that transferred mitochondria had low mitochondrial membrane potential and were highly oxidized, suggesting dysfunctional mitochondria with elevated ROS. In addition, activation of mitochondrial ROS by photobleaching a region of mitochondria in cells expressing mito-KillerRed was sufficient to similarly increase cell cycling, and mitochondrial targeted antioxidants could mitigate the proliferative benefits of mitochondrial transfer. Finally, the authors used several in vitro and in vivo models to demonstrate that M2-like macrophages had more fragmented mitochondria, had higher mitochondrial transfer rates, and promoted cell cycling in tumors.

Overall, a strength of the study is the usage of creative cell biology techniques and rigorous mouse models to provide compelling support for their primary claims, many of which go against the grain of current thinking in mitochondrial transfer research. While the discrepancies with the literature are by no means the fault of the authors, this study could nonetheless improve its reach by directly seeking resolution to these differences. In addition, the study raises some important questions how mitochondrial ROS from transferred dysfunctional mitochondria might be beneficial and at what doses, which should be further investigated to contextualize the findings.