Reviewer #3 (Public Review):

This work aims at testing hypotheses derived from the field of behavioral economics (Kahneman's theories), related to subjective value perception in ants foraging for food. The work was conceived to test how ants react to a specific feature which is the segregation or the bundling of food resources. Behavioral economics posits that individuals value more segregated resources than the same amount of resources presented in a bundled way. At the same time, if accessing the segregated resources implies an increase in energetic costs to access them (i.e. longer displacements), then costs would be also perceived as higher in the segregated-resource case than in the bundled-resource case.

Whether ants conform or not to this model is an interesting question, and irrespective of the results obtained, the experiments presented by the authors have been conceived to address this model as the experimental parameters varied refer to resource separation (drops of sucrose solution with different degrees of spacing between them) and to walking distances.

Yet, the manuscript suffers from various serious deficits that preclude being enthusiastic with respect to its present form. Various problems are listed below, which reduce the quality of this work. Hopefully, the authors can amend some of these problems to reach a more consistent version.

1) The inconsistent and unjustified "wrapping" with a "wanting vs liking" framework<br /> While it is unquestionable that the question raised by the authors revolves around behavioral-economic hypotheses on value perception and is fully addressed by the experiments performed, the "extra wrapping" of the "wanting/liking" framework added, probably to make the manuscript more attractive, is unjustified and excessively speculative. The use of a "wanting vs liking" interpretation framework is inappropriate as neither the experiments were conceived to address this topic, nor the results allow any robust conclusion on this point. These concepts originate in neuroscience analyses of neural-circuit activation in the mammalian brain upon situations that allow distinguishing several components related to reward: 1) the hedonic effect of pleasure itself (liking); 2) motivation to obtain the reward (wanting or incentive salience); and 3) and reward-related learning(1-3). These components refer to different identified neural circuits and brain areas as wanting for reward is generated by a large and distributed dopaminergic brain system including the frontal cortex, while liking is generated by a smaller set of hedonic hot spots within limbic circuitry and which are not dopamine-dependent.

Clearly, the use of the wanting vs liking terminology requires accuracy and appropriate studies to support it. This is not the case in the present manuscript which was not conceived to tackle this issue. Moreover, inconsistent testing procedures (see below point 3) undermine the use and interpretation of choice data as wanting. The authors have no proof of the involvement of wanting vs. liking systems in their design and even more, cannot disentangle between these components based on their behavioral data. Considering that pheromone deposits after food experience express "liking" can be questioned as it does not dissociate between individual liking and social information transfer (the liking and wanting systems are individually based systems). Moreover, the assignment of a choice in a binary-choice test to a wanting system is also questionable as the experiments cannot disentangle between the eventual individual wanting and the reward-related learning as animals are making choices based on odorant cues they have learned during their previous foraging bouts. In the absence of neurobiological data, the hypotheses of wanting vs. liking remain on a shaky, highly speculative ground.

Thus, the whole "wanting vs liking interpretation" (which attains alarming speculative levels in the Discussion section) should be omitted entirely from the manuscript if the authors want to provide a solid convincing framework articulated exclusively around the bundling vs. the segregation effects, which is precisely what their experiments tested. The rest is speculation in the absence of analyses supporting the wanting vs liking dissociation. An example of the kind of analysis necessary to go in this direction is provided by a recent work in which a dopamine-based wanting system was shown in honey bees(4), a work that the authors did not consider. We are clearly far from this kind of analysis in the present manuscript. As the authors wrote, "the present study is the first to examine bundling vs. segregation in an animal (line 99)", yet not liking vs. wanting.

2) Some experimental assumptions are not substantiated by data<br /> The experimental procedure relies on separating or aggregating reward (drops of sucrose solution) and determining the impact of this variation on pheromone deposition while returning to the nest and subsequent choice in a dual test situation in which two of the three treatments designed - distinguished by the odorant experienced en route to reward - were presented. While the "Segregated All Treatment" (Fig. 2A) managed to space the 0.2 µl reward drops by significant 25-cm segments, thus enhancing potentially both reward appreciation (segregated food drops) and cost appreciation (successive segments to be negotiated), the "Segregate Reward Treatment" (Fig. 2B) raises doubts about its validity.<br /> In this case, three drops were offered at the end of three consecutive 25-cm segments, with the assumption that drops spaced by 5 mm should be perceived as being segregated (two of 0.2 µl and 1 ad libitum). Yet, there is no proof - at least in the manuscript - that spacing two food drops by 0.5 mm induces a segregated perception in ants. The first experience with the first drop may induce both sensitization and a local search that may last until the very close next drop is detected so that for the ant, these drops would be perceived as belonging to the same resource rather than being perceived as segregated resources. The same applies to the vicinity between the 0.2 µl drop and the ad libitum drop.<br /> This raises the question of the real volume of the ad libitum drop, which is not mentioned (it is just described as beings "large"; line 205). One could argue that if drops separated by 5 mm were bound together, the results would be similar to those of the "Bundled Treatment" (Fig. 2C). Strictly speaking, this is not necessarily true if the volume of the large drop was known. If this were the case, the Bundled Treatment offered a volume that was 0.4 µl smaller than the total food provided in the "Segregate Reward Treatment".<br /> Overall, further controls are needed to support the assumptions of the different treatments chosen.

3) Unclear design in the testing procedures<br /> The authors did not specify in the methods if a reward was provided in the tests in which a Y maze was presented to the ants having experienced a succession of short and long segments. This information was provided later, in the Results section (line 309) and, as expected, no reward was provided during the tests, thus raising the question of the necessity of the three consecutive tests, with no refreshment trials in between. This procedure is puzzling because it induces extinction of the odor-length association - as verified by the authors (see lines 306-309) - and makes the design questionable. Only the results of the very first test should be kept and analyzed in the manuscript.<br /> The same remark applies to the three tests performed after comparing the experimental treatments, which - one discovers only in the Results Section - were also performed in the absence of refreshment trials. In fact, the absence of coherence in the results of these tests (e.g. lines 328-332) could be precisely due to a change of strategy between the tests following the absence of reward in the first test. This underlines the necessity of focusing exclusively on the first test and dismissing the data of the 2nd and 3rd tests in which performance may have been affected by extinction and strategy change. This again shows why speaking about "wanting" in this inconsistent framework makes no sense at all.

1 Berridge, K. C. & Robinson, T. E. Am Psychol 71, 670-679. (2016).<br /> 2 Berridge, K. C. & Kringelbach, M. L. Neuron 86, 646-664. (2015).<br /> 3 Berridge, K. C. & Kringelbach, M. L. Curr Opin Neurobiol 23, 294-303. (2013).<br /> 4 Huang, J. et al. Science 376, 508-512. (2022).

Reviewer #3 (Public Review):

This paper provides a novel framework for understanding prediction-based learning rules that are potentially employed by the hippocampus to optimize behavior. Specifically, the authors examined how a cognitive map containing predictive information (termed the successor representation) is computed in the hippocampus with spike-timing-dependent synaptic plasticity (STDP).

Strengths:<br /> By using an ecologically plausible computational model that is embedded with important biological characteristics, the authors propose a novel framework that demonstrates a set of computational principles employed by the hippocampus to achieve successful predictive learning. The paper clearly and thoroughly explains different components of the model with concrete examples and illustrations. Analytical solutions are also provided in addition to narratives to help readers understand the model setup as well as its relevance and connection to biological studies. Among the set of biologically realistic computational dynamics achieved by the modeling framework, the proposed model can elegantly account for both exponential and hyperbolic discounting by demonstrating that exponential discounting is utilized while the animals travel through space, whereas hyperbolic discounting is capitalized while the animals travel through time. Additionally, this paper discusses the model findings in the context of experimental and theoretical work which help readers understand how the proposed framework can be utilized in future work to guide investigations on predictive learning both empirically and computationally.

The proposed model makes connections to other theoretical frameworks

Weaknesses:<br /> While the framework proposed in this paper is potentially powerful in capturing different aspects of hippocampus-based predictive learning, the links between the model results and experimental findings are not sufficiently demonstrated. There are several biological concepts that are discussed in the context of the model. It is, however, unclear if the implementations of these concepts within the model capture the same underlying principles that happen in nature. For example, there is rich literature on hippocampal replays including their heterogeneity across contexts and species. The paper does not provide sufficient information regarding the specific types of replays or the specific aspects of replay dynamics that are observed in the model.

Reviewer #3 (Public Review):

The Nkx3.2 transcription factor is both necessary and sufficient for jaw joint development. In this paper the authors use comparative genomics to identify a conserved Nkx3.2 enhancer that they call a jaw regulatory sequence (JRS). With transgenic zebrafish they show that JRSs from multiple species of gnathostomes, including humans, can drive reporter expression in the larval jaw joint. Transgene expression in each case includes the joint interzone as well as adjacent cartilage and perichondrium. With CRISPR-targeted deletion they show requirements for the zebrafish JRS in larval jaw joint development. Analyses of additional gnathostome genomic sequence near Nkx3.2 suggest that jawless hagfish lack JRS-like sequences, consistent with an important role for this enhancer and Nkx3.2 in the evolutionary origin of jaws. Despite a growing recognition of the importance of enhancers in development and disease, very few have been shown to have essential functions in vivo.

The first part of the paper is straightforward, with clear evidence that the JRSs tested act as functional enhancers, since they drive reporter expression in very specific and similar subsets of skeletal cells. The images are high quality and the cellular resolution is impressive. There are also several moderate/major weaknesses that should be addressed. The experiments showing larval joint defects following JRS deletion in zebrafish are less clear, since the phenotypes are subtle in mutants and later recover to resemble wild type siblings. One major weakness is that there is no evidence that JRS deletion alters Nkx3.2 expression at any stage. In the absence of these data, it is possible that the JRS acts on other nearby genes. Another weakness is a lack of quantification of variation in this phenotype in the JRS mutants. Though the images of larval joint defects in the JRS mutants are clear, they are single examples. Finally, the apparent absence of an obvious JRS in the region adjacent to Nkx3.2 in hagfish is used to argue that it arose together with the origin of jaws during vertebrate evolution. Alternatively, this may instead reflect a unique loss of this element in hagfish.

Reviewer #3 (Public Review):

In this manuscript, the authors present data supporting FOXP2 as an oncogene in PCa. They show that FOXP2 is overexpressed in PCa patient tissue and is necessary and sufficient for PCa transformation/tumorigenesis depending on the model system. Over-expression and knock-down of FOXP2 lead to an increase/decrease in MET/PI3K/AKT transcripts and signaling and sensitizes cells to PI3K/AKT inhibition.

Key strengths of the paper include multiple endpoints and model systems, an over-expression and knock-down approach to address sufficiency and necessity, a new mouse knock-in model, analysis of primary PCa patient tumors, and benchmarking finding against publicly available data. The central discovery that FOXP2 is an oncogene in PCa will be of interest to the field.

However, there are several critically unanswered questions.

• No data are presented for how FOXP2 regulates MET signaling. ChIP would easily address if it is direct regulation of MET and analysis of FOXP2 ChIP-seq could provide insights.<br /> • Beyond the 2 fusions in the 100 PCa patient cohort it is unclear how FOXP2 is overexpressed in PCa. In the discussion and in FS5 some data are presented indicating amplification and CNAs, however, these are not directly linked to FOXP2 expression.<br /> • There are some hints that full-length FOXP2 and the FOXP2-CPED1 function differently. In SF2E the size/number of colonies between full-length FOXP2 and fusion are different. If the assay was run for the same length of time, then it indicates different biologies of the over-expressed FOXP2 and FOXP2-CPED1 fusion. Additionally, in F3E the sensitization is different depending on the transgene.<br /> • The relationship between FOXP2 and AR is not explored, which is important given 1) the critical role of the AR in PCa; and 2) the existing relationship between the AR and FOXP2 and other FOX gene members.

Reviewer #3 (Public Review):

Helsell et al. uses atomistic molecular dynamics simulations to characterize the structural dynamics of the M2 protein together with continuum elastic models to evaluate the energetic cost of the protein-induced bilayer deformations. Using unbiased simulations (without constraints on the protein) they show that the M2 structure is dynamic and that the AH helices are mobile (though they tend to retain their secondary structure), in agreement with experimental observations. Then, using simulations in which the peptide backbone was restrained to the starting structure, they were able to quantitatively characterize the protein-induced bilayer deformations as well as the acyl chain dynamics.

Both the atomistic simulations and the continuum-based determinations of the bilayer deformation energies are of high quality. The authors are careful to note that their unbiased simulations do not reach equilibrium, and the authors' conclusions are well supported by their results, though some issues need to be clarified.

1. P. 7: Choice of lipid composition: POPC:POPG:Cholesterol 0.56:0.14:0.3. This lipid composition (or POPC:POPG 0.8:0.2) has been used in a number of experimental studies that the authors use as reference. It differs, however, substantially from the lipid composition of the influenza membrane (Gerl et al., J Cell Biol, 2012; Ivanova et al., ACS Infect Dis, 2015), which is enriched in cholesterol, has a 2:1 ratio of phosphatidylethanolamine to phosphatidylcholine, and almost no PG. The choice of lipid composition is unlikely to impact the authors' major conclusions, but it should be discussed briefly. As noted by Ivanova et al., the lipids of the influenza membrane are enriched in fusogenic lipids. How will that impact the authors results.

2. The definition of the lipid tilt needs to be revisited. On P. 13 (in the Pdf received for review, the authors do not provide page numbers), the tilt is defined/approximated as "the angle between the presumed membrane normal (aligned with the Z axis of the box) and the vector pointing from each phospholipid's phosphate to the midpoint between the last carbon atoms of the lipid tails." This (equating the normal to the interface with the Z axis of the simulation box) may be an acceptable approximation for the lower leaflet, which is approximately flat, but probably not for the upper leaflet where the interface is curved in the vicinity of the protein. The authors should, at least, discuss the implications of their approximation in terms of their conclusion that there is little lipid tilt in the upper leaflet.

3. P. 14, last paragraph, Figure 5 and 6: The snapshots in Figure 5 are too small to see what the authors refer to when they write "tilt their lipid tails to wrap around the helices." The authors should consider citing the work of H W. Huang, e.g., Huang et al. (PRL, 2004), who introduced the notion of curvature stress induced by antimicrobial peptides, a concept similar to what the present authors propose.

4. P. 17-18, Figure 7: The authors introduce the bilayer midplane, which becomes important for the determination of the deformation energy in the (unnumbered) equation on P. 17, but do not specify how it is determined. This is a non-trivial undertaking, but critical for the evaluation of the deformation energy; please add the necessary details.

5. P. 18-19, Figure 8: The comparison of the MD and continuum membrane deformations is very informative, but the authors should discuss the implications of the increased symmetry further in terms of the estimated deformation energies. (I do not believe the authors really mean that they predicted the energies, they estimated/approximated them.)

Reviewer #3 (Public Review):

This communication describes the molecular design of antinociceptive peptides with the aim to improve the peptide affinity and blocking activity towards Nav1.7. The authors performed in vivo experimental assays of such molecular designed peptides to validate them. The methods incorporate state-of-the-art techniques, and the results are clear and of great quality.

Strengths: Many synthetic variants were generated to accomplish the best antinociceptive peptides including its in vitro and in vivo assays.

Weaknesses: Some of the reasonings for creating some of the in-silico peptide variants were not clear at all even though they were designed based on ligand-receptor models.

Reviewer #3 (Public Review):

The manuscript by Pauli and Chen et al. is a beautiful and much-needed study that characterizes the cell types that make up these nuclei.

The major strength of this study is it combines a profiling approach to identify subtypes (single-cell sequencing) with microscopy that reveals where the cells reside within the PBN (multiplex FISH) and a genetic approach to visualize the projection pattern of these cell types throughout the brain (genetic labeling with Cre-lines). The result is important new insight about the cell types in this structure. Highlights include (1) the identification of two inhibitory neuron subtypes and 19 excitatory cell types, (2) the discovery of two output streams, (3) insight about the ontogeny of cell types and transcription factors that may be involved in fate specification/determination, (4) clarification of which neuropeptides are expressed/not expressed in which cell types, (5) and the identification of suitable genetic markers to target many of the cell types. Importantly, all the data are available for researchers to mine their genes of interest. This information is a major advance in the field.

Reviewer #3 (Public Review):

Grande and colleagues used high-resolution 7 Tesla fMRI to investigate the topographical distribution of functional connectivity, and sensitivity to scene and object stimuli, across subregions of the entorhinal-hippocampal circuitry. They report scene-specific activations in functionally connected voxels of the posterior-medial entorhinal cortex (EC) and the distal subiculum. In contrast, no specific preference for object stimuli was detected.

The authors managed to characterize functional connectivity patterns in the entorhinal-hippocampal circuitry to an impressive level of detail. The division of the subiculum and CA1 region in 5 and 3 segments, respectively, extends the very sparse body of literature on the organization of connectivity across the transversal axis of the hippocampal formation in humans. Notably, the authors replicate findings by Maass et al. 2015 of a dissociation of functional connectivity preference between voxels in anterior-lateral and posterior-medial EC with voxels in proximal and distal subiculum (informed by the well-described connectivity architecture of the hippocampal formation in rodents; see e.g. Witter et al. 2000). In addition, they report the novel finding of specific functional connectivity preference of voxels in anterior-medial and anterior-lateral EC seed regions with distal CA1 (again consistent with previous findings in rodents, as well as diffusion MRI findings in humans; Syversen et al. 2021).

After having established 4 different clusters of entorhinal voxels based on functional connectivity to 4 'source' regions, the authors report specific scene sensitivity in a posterior-medial cluster, partially replicating previous studies. In addition, they describe another novel finding of specific scene sensitivity in the two most distal segments of the subiculum.

I agree with the authors that understanding the connectivity of hippocampal subregions and their functional preferences is an important goal with relevance for many research disciplines, such as on episodic memory, spatial navigation, or Alzheimer's disease.

While the paper makes a number of important contributions to help understand entorhinal-hippocampal function and connectivity, I feel that the premise and research question is somewhat unclear and potentially misleading. Most notably, I don't think the conclusions pertaining to processing of object (item) information are supported by the results. An absence of a difference does not provide evidence for similar levels of processing of object and scene information.

Reviewer #3 (Public Review):

This manuscript, "Variation in Ubiquitin System Genes Creates Substrate-Specific Effects on Proteasomal Protein Degradation" studies the genetic basis of differences in protein degradation. The authors do so by screening natural genetic variation in two yeast strains, finding several genes and often several variants within each gene that can affect protein degradation efficiency by the Ubiquitin-Proteasome system (UPS). Many of these variants have "substrate-specific effects" meaning they only affect the degradation of specific proteins (those with specific degrons). Also, many variants located within the same genes have conflicting effects, some of which are larger than others and can mask others. Overall, this study reveals a complex genetic basis for protein degradation.

Strengths: Revealing the genetic basis for any complex trait, such as protein degradation, is a major goal of biology. The results of this paper make a significant step towards the goal of mapping the genes and variants involved in this specific trait. Fine mapping methods are used to home in on the specific variants involved and to measure their effects. This is very nicely done and provides a detailed view of the genetic basis of protein degradation. Further, the GFP/RFP system used to quantify the efficiency of the protein degradation system is a very elegant system. Also, the completeness of the analysis, meaning that all 20 N-degrons were studied, is impressive and leads to very detailed findings. It is interesting that some genetic variants have larger and opposite effects on the degradation of different N-degrons.

Weaknesses: Some of the results discussed in this paper are not surprising. For example, the finding that both large effect and small effect genetic variants contribute to this complex trait is not at all surprising. This is true of many complex traits. The discussion of human disease is also a bit extensive given this study was performed on yeast. It might be more productive to use these findings to understand the UPS better on a mechanistic level. Why does the same genetic variant have opposite effects on the degradation of different degrons, even in cases where those degrons are of the same type?

Overall, this manuscript excels at mapping the genetic basis of variation in the UPS system. It demonstrates a very complex mapping from genotype to phenotype that begs for further mechanistic explanation. These results are important to the UPS field because they may help researchers interrogate this highly conserved essential system. The manuscript is weaker when it comes to the broader conclusions drawn about the relative importance of large vs. small effects variants on complex traits, the amount of heritability explained, and the effects of genetic variation on protein abundance vs transcript abundance. Though in the case of protein vs transcript, I feel the cursory examination of the trends is perhaps at an appropriate level for the study, as it is mainly meant to show these things differ rather than to show exactly how and why they differ.

Reviewer #3 (Public Review):

This paper reports the humoral (neutralizing antibody concentrations from serum) and cellular (cytopathic effect on Vero cells) immune responses of volunteers enrolled in a randomized clinical trial for the CoronaVac® SARS-CoV-2 vaccine. The findings are useful and, through solid reporting, discussion, and statistical analyses, provide context for the efficaciousness of the 0-14 day and 0-28 day dosing schedules of CoronaVac®. The results show that these two dosing schedules are similar across most metrics. Furthermore, the findings pave the way for key future work, including reporting and understanding the clinically relevant protective effects, and how long they last, of CoronaVac® against the emerging variants/subvariants.

Reviewer #3 (Public Review):

Meissner et al. employ stochastic Gal4 labeling with MCFO to ease the identification candidate lines for split-Gal4 line generation to genetically target neurons of interest identified in EM traces. Data basis for the approach is a novel resource of 74k MCFO images aligned to the JRC18 template allowing the matching between EM and LM traces of single neurons. The resource is released in combination with data processing and query tools. In addition, an open web-based data portal to the released data collection and data mining tools is made available. This will allow broad access to this novel resource with the potential to create high impact in the community.

Strength:

The possibility to bridge between EM neuron traces and expression patterns in LM images is a key method to achieve and accelerate genetic access to individual neurons. The proposed resource and tools contribute to this effort and provide open and easy access to it. This also includes the possibility to upload and analyze own data using the provided infrastructure, which is a great asset.

Weaknesses:

While the generation and analysis of the MCFO data is described in great detail and the overall technical approach seems feasible, the description of the technical part and its evaluation are lacking important implementation details and scientific rigor. Although this is primarily a life science paper introducing a new data resource it's the mining capability making this resource really valuable. The provided evaluation of the image mining capabilities however is currently insufficient to support the very general claims on effectivity and speed of the method.

Reviewer #3 (Public Review):

Noel et al provide a neural representational account of three brain areas in a virtual, visual navigation task paradigm especially designed to achieve a closed action-perception loop closely resembling natural behaviour. The authors recorded hundreds of neurons from three monkeys while the animals were engaged in the task where latent cognitive variables like distance travelled and distance to target continuously changed. The authors build on their previous work where they robustly characterized animal behaviour on this task paradigm. Here, they aim to find neural codes of dynamic, latent variables and report a mixed and heterogeneous profile of task variable coding distributed across the two brain areas in the parietal cortex (MSTd and area 7a) and one in the prefrontal cortex (dlPFC).

Major strength: Multi-area recording and the close-loop behavioural paradigm are major strengths of this study. The robust model-based analysis of neural data strengthens the paper even more. The correlation of coupling between MSTd and dlPFC and behaviour, albeit in a coarse time scale (of sessions), is particularly interesting and makes the paper strong by quantitatively relating behaviour to neural activity.

Major weakness: The paper mainly gives a long list of what task variables the three brain areas code for along with measures of connectivity between areas. Although this is a valuable contribution to the field, the study is not designed to test predictions of specific computational hypotheses. Towards the end of the paper, the authors bring up the two alternate mechanisms: vector-coding vs distance-coding, but only as a speculation. These two hypotheses could have been developed further at the outset to make specific predictions for neural dynamics and subsequently be tested in their data. This will likely lead to richer findings going beyond representations of task variables. Nevertheless, the findings presented in the paper are surely novel and exciting.

Impact: The main impact of the paper is neurophysiology under a novel, naturalistic behavioral paradigm. The data, both behavioral and neurophysiological, is rich and has potential to test predictions of more fine-grained computational hypotheses. However, the observation that MSTd codes for latent variables is not as surprising as the authors claim. Given the recent observations of heterogeneous variables represented in brain areas traditionally thought to be highly specific (e.g. locomotion variables in V1, mixed coding in EC etc.), it is not surprising to find latent variables in a 'traditionally' sensory area, especially in a continual behavioral paradigm where many variables are changing and are correlated.

Based on their previous work and this work, the authors mention multiple times the task strategy and its embodied nature. While the authors conclusively show the involvement of eye movement in solving the task, it is difficult to imagine a concrete definition of an embodied task strategy without clear alternate hypotheses. How would the animals behave if their eye movements were prevented? Worse performance (like humans did in their previous paper) or unable to perform (akin to a bird unable to fly without wings) or a different strategy? What should we predict based on the neural observation reported here? The impact of this paper would be greater if the authors bring up these questions and provide some speculations rooted in neurophysiological observations.

Reviewer #3 (Public Review):

This manuscript should be of broad interest to readers not only in the field of gap junction (GJ) mediated cell-to-cell communication but also to scientists and clinicians working on the function of mitochondria and metabolism. Their data elucidates a new function of Cx43 in regulating the energy (ATP) generation of mitochondria, e.g., under oxidative stress.

The canonical function of gap junctions is in direct cell-to-cell communication by forming plasma membrane traversing channels that electrically and chemically connect the cytoplasms of adjacent cells. These channels are assembled from connexin proteins, connexin 43 (Cx43). However, more recently new, non-canonical cellular locations and functions of Cx43 have been discovered, e.g. mitochondrial Cx43 (mtCx43). However, very little is known about where Cx43 transported into mitochondria is derived from, how Cx43 is transported into mitochondria, where it is located in mitochondria, in which form Cx43 is present in mitochondria, (polypeptides, hemi-channels (HCs), complete GJ channels), and what the function of mtCx43 is. The authors addressed the latter question. The authors provide convincing evidence that mtCx43 modulates mitochondrial homeostasis and function in bone osteocytes under oxidative stress. Together, their study suggests that mtCx43 hemi-channels regulate mitochondrial ATP generation by mediating K+, H+, and ATP transfer across the mitochondrial inner membrane by directly interacting with mitochondrial ATP synthase (ATP5J2), leading to an enhanced protection of osteocytes against oxidative insult. These findings provide important information of a role of Cx43 functioning directly in mitochondria and not at the canonical location in the plasma membrane. While most of the functional assays presented in Figures 2-8 appear solid, the mitochondrial localization of Cx43, its translocation into mitochondria under oxidative stress, and its configuration as hemi-channels (Figure 1) is less convincing. I have five general comments that should be addressed:

1) This study was performed in MLO-Y4 osteocyte cells. Is the H2O2 induced increase of mitochondrial Cx43 MLO-Y4 cell type or osteocyte specific, or is Cx43 playing a more general role in mitochondrial function, e.g. under oxidative stress? Osteoblasts such as MC3T3-E1 and MG63, and many other cell types endogenously express Cx43, and oxidative stress is a general physiological stressor, not only for osteocytes and bone cells. Attending to this question would address the generality of the findings for mitochondrial function.

2) The images of MLO-Y4 cells (Figure 1A) and the primary osteocytes isolated from Csf-1+/- and control mice (Figure 8) do not show visible gap junctions. I guess this is due to the fact that slides were stained with the Cx43(E2) antibody. I feel, staining of these cells in addition with the Cx43(CT) antibody would be helpful to get a better understanding on the distribution of Cx43 in gap junctions and undocked/un-oligomerized Cx43 in these cells.

3) The images of cells presented in Figure 1A are quite fussy. No mitochondria are visible, and the Cx43 staining is hazy and does not localize to any subcellular structures. Also, it is not clear if the higher resolution image presented in Figure 1C actually represents a mitochondrion. A good DIC image, or co-staining with another mitochondrial marker such as MitoTracker (as shown in Figure 4-S1) would make the localization and translocation of Cx43 into mitochondria upon oxidative stress more convincing. This is especially important as the translocation, although statistically significant, increases only by about 10% or less (Figure 1B). Such a small difference (also represented in the Western analyses presented in Figure 1D) could easily be artefactual, depending on how the correlation coefficient was generated. Of note in this respect is that control cells in Figure 1A appear larger (compare the size of the nuclei) and are spread out more than the H2O2 treated cells. Better, more clear images would make the mitochondrial localization/translocation more convincing.

4) How pure are the mitochondria that were probed for Cx43 by Western shown in Figure 1D? The preparation method described is relatively simple, collecting the 10,000xg supernatant (here 9,000xg supernatant) as mitochondrial fraction. Is it possible that the Cx43 signal, at least in part, is derived from other, contaminating membranes, such as PM, Golgi, or ER? Testing the mitochondrial preparation by Western with marker proteins specific for these compartments would strengthen the author's results.

5) The authors rely on previous studies to postulate that Cx43 in mitochondria forms hemichannels in their system, is localized in the inner membrane, and is oriented with the Cx43 C-termini facing the inter-membrane space (as schemed in Figure 8C). The authors use lucifer yellow (LY) dye transfer and carbenoxolone, but both are not hemi-channel specific probes. They are transferred by, and block GJ channels as well. Experiments, using hemi-channel specific probes would be more convincing. This is important, as the information cited is based on only two references (Boengler et al., 2009; Miro-Casas et al., 2009), and it still is highly unclear how a membrane protein that is co-translationally inserted into the ER membrane, then traffics through the Golgi to be inserted into the plasma membrane is actually imported into mitochondria and in which state (monomeric, hexameric). Why the Cx43(CT) specific antibody traverses the outer mitochondrial membrane and reaches the Cx43CT while the Cx43(E2) specific antibody is not described and clear either. Where are these mitochondria permeabilized with Triton X-100 as described in M&M?

Reviewer #3 (Public Review):

With resting-state fMRI data, recent work has mapped the organisation of the cortex along a continuous gradient, and regions that share similar patterns of functional connectivity are located at similar points on the gradient (Margulies et al., 2016). In the current study, the authors investigate how this dimension of connectivity changes during conceptual retrieval with different levels of semantic association strength. Specifically, they perform gradient analysis on task-fMRI informational connectivity data and reveal a similar principal gradient to the previous study, which captures the separation of heteromodal memory regions from the unimodal cortex. More importantly, by comparing the gradient generated with data from different experimental conditions (i.e., strong vs. weak association), the authors find the separation of the regions at the two ends of the gradient can be regulated by the association strength, with more separation for stronger association. They also examine the relationships between the gradient values and dimensionality and brain-semantic alignment measures, to explore the nature of this shifting gradient as well as the corresponding brain areas.

Strengths:<br /> 1. The aim of this study is clear and the relevant background literature is covered at an appropriate level of detail. With the cortical gradient analysis approach, this study has the potential to make a contribution to the understanding of the topographical neural basis of semantics in a fine-grained manner.<br /> 2. The methodology in the current study is novel. This study validates the feasibility of performing gradient analysis on task-fMRI data, which is enlightening for future research. Using the number of PCs generated by PCA as a measure of dimensionality is also an interesting approach.<br /> 3. The authors have conducted multiple control analyses, which tested the validity of their results. Specifically, a control task without engaging semantic processing was built in the experimental design (i.e., the chevron task), and the authors conducted multiple parallel control analyses with the data from this control task as a comparison with their main results. Other control analyses were also performed to validate the robustness of their methodological choices. For example, varied thresholds were used during the calculation of dimensionality and similar results were obtained.

Weaknesses:<br /> 1. As a major manipulation in the experiment, it is not very clear how the authors split/define their stimuli into strong and weak semantic association conditions. If I understood correctly, word2vec was used to measure the association strength in each pair of words. Then the authors grouped the top 1/3 association strength trials as a "strong association" condition and the bottom 1/3 as "weak association" (Line 689), and all analyses comparing the effect of "strong vs. weak association" were conducted with data from these two subsets of stimuli. However, in multiple places, the authors indicate the association strength of their stimuli ranges from completely unrelated to weakly related to highly related (Line 612, Line 147, Line 690, and the examples in Figure 1B). This makes me wonder if the trials with bottom 1/3 association strength (i.e., those were used in the current study) are actually "unrelated/no association" trials (more like a baseline condition), instead of "weak association" trials as the authors claimed. These two situations could be different regarding how they engage semantic knowledge and control processing. Besides, I am very interested in what will the authors find if they compare all three conditions (i.e., unrelated vs. weak association vs. strong association).<br /> 2. Following the previous point, because the comparison between weak vs. strong association conditions is the key of the current study, I feel it might be better to introduce more about the stimuli in these two conditions. Specifically, the authors only suggested the word pairs fell in these two conditions varied in their association strength, but how about other psycholinguistic properties that could potentially confound their manipulation? For example, words with higher frequency and concreteness may engage more automatic/richer long-term semantic information and words with lower frequency and concreteness need more semantic control. I feel there may be a possibility that the effect of semantic association was partly driven by the differences in these measures in different conditions.<br /> 3. The dimensionality analysis in the current study is novel and interesting. In this section, the authors linked decreasing dimensionality with more abstract and less variable representations. However, most results here were built based on the comparison between the dimensionality effects for strong and weak association conditions. I wonder if these conclusions can be generalised to results within each condition and across different regions (i.e., regions having lower dimensionality are doing more abstract and cross-modal processing). If so, I am curious why the ATL (a semantic "hub") in Figure 3A has higher dimensionality than the sensory-motor cortices (quite experiences related) and AG (another semantic "hub").<br /> 4. I am not sure about the meaning/representational content underlying the semantic similarity matrix in the semantic-brain alignment analysis. According to the authors, this matrix was built based on the correlation of participants' ratings of associative strength (0, no link; 1~4, weak to strong) across trials. The authors indicate that this matrix reflects the global similarity of semantic knowledge between participants (Line 403). However, even though two participants share very similar ratings of association strength across trials, they could still interpret the meaning/knowledge underlying the associations very differently. For example, one participant may interpret the link between "man" and "car" as a man owns a car but another participant may interpret it as a man is hit by a car, although both associations could be rated as strong for this trial. This situation may be even more obvious for those pairs with weak association. Therefore, I am not confident this is a measure of similarity of semantic knowledge.

Reviewer #3 (Public Review):

Higher BMI in childhood is correlated with behavioral problems (e.g. depression and ADHD) and some studies have shown that this relationship may be causal using Mendelian Randomization (MR). However, traditional MR is susceptible to bias due to population stratification, assortative mating, and indirect effects (dynastic effects). To address this issue, Hughes et al. use within-family MR, which should be immune to the above-listed problems. They were unable to find a causal relationship between children's BMI and depression, anxiety, or ADHD. They do, however, report a causal effect of mother's BMI on depression in their children. They conclude that the causal effect of children's BMI on behavioral phenotypes such as depression and anxiety, if present, is very small, and may have been overestimated in previous studies. The analyses have been carried out carefully in a large sample and the paper is presented clearly. Overall, their assertions are justified but given that the conclusions mostly rest on an absence of an effect, I would like to see more discussion on statistical power.

1) The authors show that the estimates of within-family MR are imprecise. It would be helpful to know how much power they have for estimating effect sizes reported previously given their sample size.

2) They used the correlation between PGS and BMI to support the assertion that the former is a strong instrument. Were the reported correlations calculated across all individuals? Since we know that stratification, assortative mating, and indirect effects can inflate these correlations, perhaps a more unbiased estimate would be the proportion of childrens' BMI variance explained by their PGS conditioned on the parents' PGS. This should also be the estimate used in power calculations.

3) In testing the association of mothers' and fathers' BMI with children's symptoms, the authors used a multivariable linear regression conditioning on the child's own BMI. Was the other parent's BMI (either by itself or using the polygenic score) included as a covariate in the multivariable and MR models? This was not entirely clear from the text or from Fig. 2. I suspect that if there were assortative mating on BMI in the parent's generation, the effect of any one parent's BMI on the child's symptoms might be inflated unless the other parent's BMI was included as a covariate (assuming both mother's and father's BMI affect the child's symptoms).

4) They report no evidence of cross-trait assortative mating in the parents generation. The power to detect cross-trait assortative mating in the parents' generation using PGS would depend on the actual strength of assortative mating and the respective proportions of trait variance explained by PGS. Could the authors provide an estimate of the power for this test in their sample?

5) Are the actual phenotypes (BMI, depression or ADHD) correlated between the parents? If so, would this not suffice as evidence of cross-trait assortative mating? It is known that the genetic correlation between parents as a result of assortative mating is a function of the correlation in their phenotypes and the heritabilities underlying the two traits (e.g., see Yengo and Visscher 2018). An alternative way to estimate the genetic correlation between parents without using PGS (which is noisy and therefore underpowered) would be to use the phenotypic correlation and heritability estimated using GREML or LDSC. Perhaps this is outside the scope of the paper but I would like to hear the author's thoughts on this.

6) It would be helpful to include power calculations for the MR-Egger intercept estimates.

7) Finally, what is the correlation between PGS and genetic PCs/geography in their sample? A correlation might provide evidence to support the point that classic MR effects are inflated due to stratification.

Reviewer #3 (Public Review):

This study outlines the role of osteoclast-mediated resorption in integrating the skeletal elements during limb regeneration, using axolotls that can regenerate the entire limb upon amputation. Using calcium-binding vital dyes (calcein and alizarin red), the authors first demonstrated that a large portion of amputated skeletal elements is resorbed prior to blastema formation. They further show that 1) inhibiting bone resorption by zoledronic acid impairs proper integration of the pre-existing and regenerating skeletal elements, 2) removing the wound epithelium using the full skin flap surgery inhibits bone resorption, and 3) bone resorption and blastema formation are correlated. The authors reached the major conclusion that bone resorption is essential for successful skeletal regeneration. Notably, this study applies a well-established and elegant axolotl limb regeneration model and transgenic reporter strains to reveal the potential roles of resorption in limb regeneration.

Strengths:<br /> 1. The authors utilized a well-established axolotl limb regeneration model and applied elegant vital mineral dyes and transgenic reporter lines for sequential in vivo imaging. The authors also provided quantitative assessment by examining multiple animals, particularly in the early sections, ensuring the rigor and the reproducibility of the study.<br /> 2. The authors further performed important interventions that can impinge upon successful limb regeneration, including inhibition of bone resorption by zoledronic acid and impairment of the wound epithelium by full skin flap surgery. These procedures gave rise to useful insights into the relationship between bone resorption and successful limb regeneration.<br /> 3. The imaging presented in this manuscript is of exceptionally high quality.

Weaknesses:<br /> 1. Despite the high quality of the work, many analyses in this study are incomplete, making it insufficient to support the major conclusion. For example, in Figure 4, the authors did not provide any quantitative assessment to show how zol affects the integration of the skeletal elements (angulation?), which seems to be essential for supporting the conclusion. Likewise in Figure 7, the analyses of EdU+ cells and Sox9 reporter expression were not included in zol-treated animals. Similarly in Figure 5, quantification of osteoclasts was not performed with the full skin flap surgery group. Analyses of only normally regenerated animals are not sufficient to support many of the conclusions.<br /> 2. The phenotype of zol-treated animals in limb regeneration is somewhat disappointing. Although zol-treated animals show decreased blastema formation and unresorbed pre-existing skeletal elements, limb regeneration still occurs and the only phenotype is a relatively minor defect in skeletal integration. It is possible that zol-induced defect in blastema formation is not directly linked to the failure of integration at a later stage.<br /> 3. As an integration failure of the newly formed skeleton still occurs in untreated animals, it is not entirely clear how the authors can attribute this defect to a lack of bone resorption. More quantitative analyses would be necessary to demonstrate the correlation between zol treatment and lack of integration.

Reviewer #3 (Public Review):

In this work, Dumrongprechachan et al. impressively expanded their earlier work on the identification of cell type-specific subcellular proteomes from mouse brain by APEX2 proximity labeling. Instead of using viral expression of APEX2, the authors now created a Cre-dependent APEX2 reporter mouse line using CRISPR knock-in, which can be combined with multiple Cre-driver lines for proteomic applications. Using this novel tool in combination with sophisticated mass spectrometry and elegant bioinformatics, they mapped the temporal dynamics of the axonal proteome in corticostriatal projections (instead of only identifying a static cell type- and compartment-specific proteome) together with its phosphorylation status (instead of only looking at protein abundance). The data will provide a valuable resource on developmental trajectories at the proteomic and phosphoproteomic level, and will allow for pathway- and phosphosite-centric systems-level analyses as exemplified by the identification of proline-directed protein kinases as major regulators of corticostriatal projection development.

Strengths:<br /> The key tool developed in this work is the APEX2 reporter mouse line as it enables capturing of early postnatal time points, which was not possible before due to the time window of 2-4 weeks required for viral APEX expression. Thus, this tool puts the authors into position to access the temporal dynamics of the developing axon at time points spanning from neonate (as early as P5) to young adult (P50). Within this complex experimental design, the authors even managed to introduce a crucial compartment control at least for the time point P18, in which APEX expression is restricted to nucleus and soma upon viral expression. The resulting resource will be of high value as the data are derived from advanced mass spectrometric methods and stringent data handling. Examples of this high level of scrutiny include the use of MS3 methodology for the acquisition of TMT data to address the ratio distortion issues typically seen with isobaric labeling and thereby increase the quantification accuracy and the limitation to proteins quantified in all biological replicates.

Weaknesses:<br /> As to sample preparation for mass spectrometry, the authors follow the interesting concept of first enriching the phosphopeptides from the pool of TMT-labeled tryptic peptides and then using the unbound fraction from that step for further peptide fractionation, followed by mass spectrometric protein quantification. While this strategy sounds very straightforward in principle, one would expect that the phosphopeptide enrichment comes with an unspecific loss of other peptides in general, and with a semi-specific loss of acidic peptides in particular. Was this potential issue investigated by comparison with samples that were fractionated directly without prior phosphopeptide enrichment? Or with other words: the rationale for this sequential procedure is compelling - quantification of both protein and phosphopeptide abundance from the same (limited) sample, but what is the price for it as to peptide loss?

The APEX2 reporter mouse line is a novel tool with broad applicability for proximity labeling approaches and, understandably, the authors advertise its advantages, mainly via the suitability for short temporal windows. However, the discussion on the limitations of the approach falls short. The authors should make clear that the APEX method in general is limited to ex vivo approaches such as the acute brain slices used here due to the limitation that potentially toxic reagents (i.e. low membrane-permeable biotin-phenol and H2O2) have to be delivered to the target tissue. Although treatment with H2O2 is rather short, undesired oxidative stress signaling may have to be taken into account, particularly when protein phosphorylation rather than protein abundance is assessed. It would also be interesting to discuss the pros and cons of perfusing the mice prior to preparation of brain slices; e.g., in the context of removal of catalases/endogenous peroxidases or potential for substrate delivery (like recently shown in heart, doi: 10.1038/s41586-020-1947-z). Another issue with the Discussion is that the authors do not properly reflect the involvement of proline-directed kinases in the development of corticostriatal projections, which stands in contrast to the fact that they sell this as one of their major findings throughout the manuscript, including the Abstract.

Reviewer #3 (Public Review):

This study investigates the neuronal correlates of low-frequency changes in respiration volume per unit time (RVT). The authors report distributed patterns of correlations between RVT and fMRI that may represent a respiration-driven brain network. The ability to demonstrate that this pattern has neuronal origins would make an important contribution to the fMRI field, especially as physiological signals are typically treated as artifacts in fMRI analysis.

A major strength of this paper is the use of concurrent fMRI, physiological monitoring, and invasive electrophysiology (electrode in the anterior cingulate cortex; ACC) in the anesthetized rat, which allows for directly measuring local neuronal activity associated with changes in respiration. A second strength is that the authors demonstrate coherence between respiration (the raw signal as well as RVT) and gamma-band power in the ACC, and furthermore replicate prior findings of a close link between gamma-band power and the BOLD fMRI signal. The authors also take care to ensure that the pattern of correlation between RVT and fMRI is distinct from artifacts resulting from breathing-induced static field changes as well as from CO2-related effects of breathing on the BOLD signal. The findings are clearly presented throughout the paper.

I believe that additional information would help to more strongly support the main claim, i.e., that the reported RVT-fMRI correlation pattern is of neuronal origin. One analysis that supports this claim is that in the lightly anesthetized state, regressing out the gamma-band power signal considerably reduced correlations between RVT and fMRI. However, the more direct test of this possibility involves the experiment in which neural activity across the brain is silenced (isoelectric state) while respiration is artificially maintained. The resulting disappearance of correlation between RVT and fMRI data points to the neuronal nature of RVT-fMRI correlation. Yet, since the amount of temporal variation in RVT during the iso-electric state was not reported, it was not clear whether RVT itself also exhibited less temporal variation in the isoelectric state. Since respiration was maintained by a ventilator in the isoelectric state, I wondered if the respiration depth and volume was more constant compared to in the lightly anesthetized state, in which it is mentioned that spontaneous respiration occurred. Importantly, the authors do mention that the respiration patterns were visually similar between these conditions (Fig. 5C and line 219), which is very promising, but quantification of RVT properties would be important to provide as well.

Reviewer #3 (Public Review):

The study presents interesting new data on the role of the PTPRK D2 pseudophosphatase domain recruiting determining substrate specificity. The paper also demonstrates the utility of predicted structural models, an aspect that has been nicely integrated into this study. However, many open questions remain and additional experimental data should be provided to experimentally confirm the proposed substrate recognition model.

In particular:<br /> 1) Validation of reagents: The authors generated a pY1230 Afadin antibody claiming that (page 6) "this new antibody is specific to tyrosine phosphorylated Afadin, and that pY1230 is targeted for dephosphorylation by PTPRK, in a D2-domain dependent manner". The WB in Fig 1B shows a lot of background, two main bands are visible which both diminish in intensity in ICT WT pervanadate-treated MCF10A cell lysates. The claim that the developed peptide antibody is selective for pY1230 in Afadin would need to be substantiated, for instance by pull down studies analysed by pY-MS to substantiate a claim of antibody specificity for this site. However, for the current study it would be sufficient to demonstrate that pY1230 is indeed the dephosphorylated site. I suggest therefore including a site directed mutant (Y1230F) that would confirm dephosphorylation at this site and the ability of the pY antibody recognizing the phosphorylation state at this position.<br /> 2) The authors claim that a short, 63-residue predicted coiled coil (CC) region, is both necessary and sufficient for binding to the PTPRK-ICD. The region is predicted to have alpha-helical structure and as a consequence, a helical structure has been used in the docking model. Considering that the authors recombinantly expressed this region in bacteria, it would be experimentally simple confirming the alpha-helical structure of the segment by CD or NMR spectroscopy.<br /> 3) Only two mutants have been introduced into PTPRK-ICD to map the Afadin interaction site. One of the mutations changes a possibly structurally important residues (glycine) into a histidine. Even though this residue is present in PTPRM, it does not exclude that the D2 domain no longer functionally folds. Also the second mutation represents a large change in chemical properties and the other 2 predicted residues have not been investigated.<br /> 4) The interface on the Afadin substrate has not been investigated apart from deleting the entire CC or a central charge cluster. Based on the docking model the authors must have identified key positions of this interaction that could be mutated to confirm the proposed interaction site.<br /> 5) A minor point is that ITC experiments have not been run long enough to determine the baseline of interaction heats. In addition, as large and polar proteins were used in this experiment, a blank titration would be required to rule out that dilution heats effect the determined affinities.

Reviewer #3 (Public Review):

This paper uses transient dark exposure to induce plasticity in the adult visual cortex. It shows that transient dark exposure in the adult mice has opposing effects at the single neuronal level versus the population level. At the population level, the stimulus representation is degraded following dark exposure but rebounds back to normal within 8 days of light re-introduction. Thus, dark exposure does not have a lasting negative impact on the visual cortex. Unexpectedly, at the single neuronal level, following dark exposure a fraction of neurons show more stable responses and higher correlations among pairs of neurons. It is inspiring to hypothesize that this fraction of neurons may form a plastic substrate for representation of complex natural scenes.

Strengths:

The paper uses a combination of single neuron and population analyses to identify the effects of transient dark exposure on visual responses in the adult mouse visual cortex. It succeeds in identifying degradation of stimulus representation at the population level following dark exposure, and stabilization of visual stimulus preference at the single neuron level as well as stabilization of stimulus correlations among pairs of neurons. This success is in part due to an impressively large set of simple visual stimuli used (180 different stimuli). This large set allows the authors to identify even small changes in stimulus preferences at the single neuronal level.<br /> This paper uses transient dark exposure to induce plasticity. An alternative and commonly used method to induce plasticity is monocular deprivation. This paper shows that at the single neuron level, the effects of transient dark exposure are different from the previously reported effects of monocular deprivation. This is an important finding for the field.

Weaknesses:

The analysis methods used are thoughtful and complementary. The statistical tests are mostly performed on visual responses pooled across 6 mice. These statistical tests support the claims of the paper. However, we are left wondering whether the effects identified would also be significant for visual responses of each individual mouse.

Reviewer #3 (Public Review):

In a previous study, the authors screened a genome-wide CRISPRi library for sensitivity to a panel of antibiotics. One of the hits on this screen was found to be an essential adenylate cyclase, Rv3645. Rv3645 is a multidomain adenylate cyclase (AC), membrane-associated, and carries a HAMP domain (often associated with two-component signal transduction pathways). Surprisingly, Rv3645 was the only AC exhibiting this broad sensitivity to antibiotics. These observations were validated using a knock-down strategy and were also shown to be complemented by expressing a CRISPRi-resistant allele. To confirm that the sensitivity is not due to weakened cell walls or increased permeability of the cell to antibiotics, they measured the uptake of vancomycin using fluorescently conjugated vancomycin and by mass-spec. Interestingly, the essentiality and drug sensitivity of rv3645KD was found to be dependent on long-chain fatty acids. When Mtb was cultured in absence of fatty acids, rv3645 was no longer essential which allowed them to construct an rv3645 deletion strain. To determine the role of AC in lipid metabolism, the authors carried out a suppressor screen to identify mutants that reversed the fatty-acid phenotype. Mutants were identified in fatty acid transporter genes and in a cAMP phosphodiesterase gene, rv1339. The role of cAMP levels in mediating fatty acid metabolism and antibiotic resistance was further confirmed through the measurement of cAMP levels using mass spectrometry and expression of an enzymatically inactive mutant of rv3645.

Overall, this is a very elegant study that uses cutting-edge bacterial genetics to address the role of cAMP in mycobacterial pathogenesis. All the experiments have been well designed with the necessary controls and rigor. The studies clearly establish the role of cAMP, especially mediated through rv3645 in fatty acid metabolism and resistance against different classes of antibiotics. While the upstream signal is still unknown this can be for future follow-up studies.

Reviewer #3 (Public Review):

This paper presents a rigorously performed series of studies to improve the ability of the PhIP-seq method to discover autoantibodies against peptide antigens that span the whole peptidome at scale, and increase the ease of validation and definition of disease specificity. The paper is an extension of a recent paper from the DeRisi and Anderson groups done on APS1 patients, which defined and validated a novel series of tissue-specific autoantigens in APS1. The current studies show that the authors can find the antibodies they previously defined, and using larger numbers of disease and control samples, can expand some what they detect. They then use the new method to look at multiple additional processes in which autoimmunity has been demonstrated/postulated.

The dataset may be of use to others interested in defining novel autoantibodies. The findings really did not share significant new insights into the processes they studied,. As the authors note, they were unable to detect the antibodies (~10% of patients) recognizing type I IFNs in severe COVID-19, where these had been demonstrated effectively using ELISA previously. Unlike APS1, where their findings about uncommon tissue specific autoantibody responses across a population with known genetic deficiency and heterogeneous phenotypes could really illustrate the power of the method and approach, that elegance and powerful and novel conclusion is not as evident here.

Reviewer #3 (Public Review):

The authors have determined a range of conformations of the high-affinity prokaryotic K+ uptake system KdpFABC, and demonstrate at least two novel states that shed further light on the structure and function of these elusive protein complexes.

The manuscript is well-written and easy to follow. The introduction puts the work in a proper context and highlights gaps in the field. I am however missing an overview of the currently available structures/states of KdpFABC. This could also be implemented in Fig. 6 (highlighting new vs available data). This is also connected to one of my main remarks - the lack of comparisons and RMSD estimates to available structures. Similarity/resemblance to available structures is indicated several times throughout the manuscript, but this is not quantified or shown in detail, and hence it is difficult for the reader to grasp how unique or alike the structures are. Linked to this, I am somewhat surprised by the lack of considerable changes within the TM domain and the overlapping connectivity of the K indicated in Table 1 - Figure Supplement 1. According to Fig. 6 the uptake pathway should be open in early E1 states, but not in E2 states, contrasting to the Table 1 - Figure Supplement 1, which show connectivity in all structures? Furthermore, the release pathway (to the inside) should be open in the E2-P conformation, but no release pathway is shown as K ions in any of the structures in Table 1 - Figure Supplement 1. Overall, it seems as if rather small shifts in-between the shown structures (are the structures changing from closed to inward-open)? Or is it only KdpA that is shown?

My second key remark concerns the "E1-P tight is the consequence of an impaired E1-P/E2-P transition" section, and the associated discussion, which is very interesting. I am not convinced though that the nucleotide and phosphate mimic-stabilized states (such as E1-P:ADP) represent the high-energy E1P state, as I believe is indicated in the text. Supportive of this, in SERCA, the shifts from the E1:ATP to the E1P:ADP structures are modest, while the following high-energy Ca-bound E1P and E2P states remain elusive (see Fig. 1 in PMID: 32219166, from 3N8G to 3BA6). Or maybe this is not what the authors claim, or the situation is different for KdpFABC? Associated, while I agree with the statement in rows 234-237 (that the authors likely have caught an off-cycle state), I wonder if the tight E1-P configuration could relate to the elusive high-energy states (although initially counter-intuitive as it has been caught in the structure)? The claims on rows 358-360 and 420-422 are not in conflict with such an idea, and the authors touch on this subject on rows 436-450. Can it be excluded that it is the proper elusive E1P state? If the state is related to the E1P conformation it may well have bearing also on other P-type ATPases and this could be expanded upon.

Reviewer #3 (Public Review):

The authors introduce an integrative platform for identifying small molecule ligands that can disrupt RNA-protein interactions (RPIs) in vitro and in cells. The screening assay is based on prior work establishing the MT bench assay (Boca et al. 2015) for evaluating protein-protein interactions in cells by utilizing microtubules as a platform to recruit and detect PPIs in cells. In the current manuscript, the authors adapted this methodology to evaluate small molecules targeting RNA-binding protein (RBPs) interactions with mRNA in cells. By combining the MT bench assay with computational docking/screening and ligand-binding evaluations by NMR, the authors discover inhibitors of the RBP YB-1, which included FDA-approved PARP-1 inhibitors. The impact of this work could be high given the critical roles of RNA-binding proteins in regulating the function and fate of coding and non-coding RNA. While the presented data are promising, the ability to generally apply this method beyond YB-1 and to RBPs in general remains to be addressed.

Reviewer #3 (Public Review):

Gicking et al. analyze the relation between DDB (retrograde motor complex) and different members of kinesin family. The authors directly linked DDB and kinesin-1, -2 and -3 using DNA linker. Consistent with previous force measurement, kinesin-1 can dominate DDB. On the other hand, it is an unexpected and interesting observation that kinesin-2 and -3 can withstand loads by DDB because these motors are sensitive to load and easily detach from microtubules under loaded conditions in optical tweezers experiments. The authors performed computer simulations and suggested that fast detachment in kinesin-2 and -3 can be antagonized by fast reattachment. The work will impact thinking about physical properties of kinesins under loaded conditions.

Weaknesses:<br /> (1) To show DDB-kinesin-2 relation, the authors analyzed KIF3A/KIF3A homodimers. This reviewer does not think KIF3A/KIF3A homodimers represent kinesin-2. The motor domain of kinesin-2 is a heterodimer composed of KIF3A and KIF3B in the cell. The authors have previously shown that properties of KIF3A/KIF3A homodimer are different from those of KIF3A/KIF3B (Andreasson et al., Curr Biol., 2015).

(2) While these in vitro results are interesting, physiological meaning of these findings is not very clear.

Reviewer #3 (Public Review):

The manuscript provides evidence that larvae are capable of operant, as opposed to classical, conditioning: optogenetic activation of serotonergic neurons after a larva bends in one direction increases the likelihood that it will bend in that direction again.

Furthermore, the manuscript shows that serotonergic neurons located in the ventral nerve cord are capable of inducing this associative conditioning. While dopaminergic and serotonergic neurons, notably the dopaminergic PAM cluster in the Mushroom Bodies, have previously been implicated in classical conditioning, where different subsets apply positive or negative valence, these data suggest that specific serotonergic neurons may also contribute to learned behaviors. Although the cellular and circuit mechanisms remain unclear, and the consequences of silencing these neurons in contexts where the larva might more naturally employ operant learning are not tested, this research suggests new areas for exploring the adaptive capacity of a powerful model organism.

Reviewer #3 (Public Review):

The authors demonstrate in mice that the amount of sleep is related to stress resilience, and specifically that increased sleep after stress exposure supports resilient behavior. The aims are achieved through an array of methodologies, which highly strengthens the conclusions of the work. The question of whether sleep is related to stress resilience is highly significant and in the current research, the authors tackle the questions by evaluating differences in sleep homeostasis in stress-resilient compared to stress-susceptible mice. To induce more stress-susceptibility, the authors challenge the mice with sleep restriction, and to induce more stress-resilience, the authors chemogenetically induce increased NREM sleep. Mechanistically the authors demonstrate that cortically mediated NREM sleep is sufficient to promote resilience. Despite the challenging nature of the technological approaches at hand, particularly in mice, the experiments are well-designed and the authors are commended for the execution of these studies.

It is very difficult to separate sleep loss and stress responses, as losing sleep is inevitably a stressful experience. The authors attempt to quell the notion that sleep restriction was also stressful to the animals by measuring fecal corticosterone, however, the measurements were from fecal pellets collected during an entire 24 hr period raises concerns that acute changes in HPA response may not be evident through this measurement. This is a challenging notion to tackle and deserves a bit more consideration.

Chemogenetic experiments induce a beautiful increase in NREM sleep at the expense of REM loss, yet all the animals treated with chemogenetic agents are resilient to social defeat stress. The authors conclude that because sleep restriction also reduced REM, yet opposite effects occur on social interaction, REM sleep is unlikely to be related to resilience. In this context, it would be beneficial to discuss the theories of sleeping to forget and sleeping to remember, and supporting literature that REM sleep is critical to the consolidation of memories, particularly upon stressful experiences.

Reviewer #3 (Public Review):

This study addresses fundamental aspects of the eco-evolutionary dynamics of highly fecund organisms experiencing huge mortality rates during early life stages. In such species, a mechanism called "sweepstakes reproductive success" (Hedgecock, 1994) has been proposed to understand the dynamics of recruitment, in which individual reproductive success shows high variance and skewed distribution. Sweepstakes reproductive success can be either neutral due to random environmental variation influencing the recruitment of reproducing offspring, or selective because genetic variation at particular loci influences the likelihood of successful recruitment. Unfortunately, empirical tests of sweepstakes reproduction remain scarce due to the difficulty of studying individual reproductive success directly, particularly in highly fecund marine organisms.

By analysing genome-wide genetic diversity data under different coalescent models representing alternative recruitment dynamics, this pioneering study specifically tests whether random or selective sweepstakes reproduction occurs in the highly fecund Atlantic cod. Using the classical Kingman coalescent and two multiple-merger coalescent models approximating random sweepstakes (the Xi-Beta-coalescent model) and selective sweepstakes (the Durrett-Schweinsberg model), the authors show that genetic diversity in the Atlantic cod genome is most likely shaped by pervasive selective sweeps of new beneficial mutations. The best-fit selective sweepstakes model is able to reproduce the main characteristics of the allele frequency spectrum of each Atlantic cod population, while alternative models include either random sweepstakes or other biologically plausible scenarios (i.e. historical demographic changes, cryptic breeding structure, and background selection) show a much poorer fit.

These findings have a broad impact on evolutionary genomics since they provide a new and exciting perspective on the choice of appropriate coalescent models for the study of highly fecund organisms that may experience high rates of selective mortality during early life stages. The low-fecundity low-variance reproductive success model classically used in evolutionary genetics may simply not apply in highly fecund organisms with skewed offspring distribution.

By confronting different alternative models of coalescence with genome-scale genetic diversity data, this work provides a roadmap for exploring fundamental processes at the crossroads between ecology and evolution. It highlights the importance of (i) understanding the potential impact of species-specific biological characteristics when inferring demography and selection from molecular data, and (ii) being aware of the potentially significant effects of unaccounted aspects of the data (e.g. variant misorientation, past admixture) on the interpretation of results.

Reviewer #3 (Public Review):

The manuscript by Ronzano et al presents a rigorous neuroanatomical study to convincingly demonstrate that there is no difference in the medio-lateral organization of flexor and extensor premotor interneurons. The study uses monosynaptic restricted transsynaptic tracing from ankle flexor and extensor muscles with several (4) strategies for delivery of the G protein complement and delta G Rabies virus, and additional (2) variations that consider titer and cre line. The authors went to great lengths here in attempt to replicate prior studies for which they had initial conflicting findings. Further, the experiments are performed in laboratories in four different locations. The variations on the Rabies and complement delivery, regardless of lab performing the experiment and analysis, all converge on the same conclusion. Aside from the primary conclusion, the paper can be used as a manual for anyone considering transsynaptic tracing as it details the benefits and caveats of each strategy with examples.

The initial conflicting results put the onus on the authors to demonstrate where the divergence occurred. The authors took a highly comprehensive approach, which is a clear strength of the paper. All of the data is fully and transparently presented. Standardizations and differences between experiments run or analyzed in each lab are well laid out. Figure 1 and Table 2 provide a great summary of the techniques and their limitations. These are also well thought out and discussed within each section of results.

The only thing missing is a likely explanation for the differences seen. Although the authors made several attempts to provide such explanation, the question remains - how did two groups who published independent studies using different strategies demonstrate flexor and extensor separation in the dorsal horn, when this study, using several strategies in multiple labs, show that the premotor neurons are in complete overlap? Additional small differences in methodologies could be identified which are not discussed and may provide potential explanations, but only for discrepancies in results of single techniques, not for all of the strategies used. The lack of reason for the discrepancy with prior studies despite the extensive efforts is unsatisfying, but, most importantly, the experiments were rigorously performed and the data support the conclusions presented.

Reviewer #3 (Public Review):

Zhao and Sharpe identified telocytes in the periodontium. To address their contribution to periodontal diseases, they conducted scRNA-seq analysis and lineage tracing in mice. They demonstrated that telocytes are activated in periodontitis. The activated telocytes send HGF signals to surrounding macrophages, converting M2 to M1/M2 hybrid status. The study implies that targeting telocytes and HGF signal for the potential treatment of periodontitis.

The significance of the study could be improved by authors testing if targeting telocytes or HGF signals could ameliorate periodontitis in the mouse model. The current form of the manuscript lacks the data that demonstrate the actual contribution of telocytes in the homeostasis of periodontium or progression of periodontitis.

Major comments:

1) I see the genetic validation of the role of telocytes or HGF signals are crucial to assure the significance of this manuscript. I recommend either of two experiments. a. testing the role of HGF signals by deleting the Hgf gene in telocytes. Using Wnt11-Cre; Hgf f/f mice, the authors could address the role of HGF signals in periodontitis. CX3CR1-Cre; cMet f/f mice will delete HGF signals in monocyte-derived macrophages. This will be another verification, but not sure if the PDL macrophages are derived from yolk sac or monocytes. b. measuring the contribution of telocytes in the homeostasis or disease progression. The mouse model could be challenging though, the system if achieved will be very informative. The authors could first check the expression of telocyte enriched genes, such as Lgr5 or Foxl1 reported previously in other tissue telocytes. Delete those genes under the Wnt1-Cre driver and check if telocyte lineage is removed. The system would be very useful for next-level study. DTA model could be an alternative, but Wnt1-Cre is vastly expressed in neural crest lienage.

2) This paper points out that the M1/M2 hybrid state of macrophages appears upon periodontitis. The authors could further characterize the hybrid macrophages by the expression of more markers, production of cytokines, and morphology. Need to clarify if this means some macrophages are in M1 state and others are in M2 state, or one macrophage possesses both M1 and M2 phenotype. Please conduct either FACS or immunofluorescence to demonstrate if one macrophage expresses both markers. Please introduce more information about the M1/M2 hybrid state of macrophage based on other present literature.

3) In the introduction part, the author lists several markers that can be used for telocyte identification, such as CD34+CD31-, CD34+c-Kit+, CD34+Vim+, CD34+PDGFRα+. Could authors explain why they chose CD34 CD31, but not other markers?

4) In figure 5g, I don't think the yellow color cell shows the reduction trend in the Tivantinib treatment group compared with a control group. Please validate the observation by gene expression analysis, WB, etc. In addition, please show c-Met+ cells level in the Tivantinib treatment group and control group.

Reviewer #3 (Public Review):

In this MS by Sefton et al., the authors investigate the role of HGF/MET pathway, as well as the cellular source of these molecules, during diaphragm development. In particular, the authors address the function of this pathway on muscle progenitors and phrenic nerve. They further provide evidence for the expression of HGF in pleuroperitoneal folds and for its requirement for muscle progenitor recruitment and maintenance during diaphragm muscle formation. This study is interesting and in general the results support the conclusions. The work could be improved by (1) providing appropriate controls for the role of HGF in the connective tissue and (2) linking the muscleless diaphragms and HGF to the hernia phenotype.

Reviewer #3 (Public Review):

This manuscript aimed to reveal the difference and similarity of sharp-wave ripples in awake vs. sleeping mice. To do this, the authors used wide-view voltage and glutamate activity imaging in awake head-fixed mice. The two-photon Ca imaging was applied to examine the spiking activity of the retrosplenial cortex.

They showed that the mean membrane potential and glutamatergic transmission of the neocortex's superficial layers were suppressed and enhanced, respectively, just after the sharp-wave ripples in awake mice, contrary to the same authors' previous findings in urethane-anesthetized and naturally sleeping mice. The retrosplenial cortex was most strongly modulated in membrane potential and glutamatergic transmission by awake sharp-wave ripples. The authors also found two groups of retrosplenial cortical neurons, whose spiking activity, measured by Ca dynamics, was suppressed and enhanced by awake sharp-wave ripples. These findings revealed the critical difference between sharp-wave ripples during waking vs. sleep, which would impact the field of memory research.

This manuscript's strength is that it compares the dynamics of membrane potential and glutamate transmission using wide view imaging. Both experimental and analytical methods were appropriate and supported their main conclusions.

Reviewer #3 (Public Review):

The authors attempted to, and succeeded at, testing the recent hypothesis that the large theropod dinosaurs Spinosaurus was a fast and capable swimmer and diver.

The strengths of the paper are the extent of the analyses which address and test numerous aspects of the 'aquatic hypothesis' with some depth, though in places this needs a better explanation of the details of the process and organisation. The results do support the conclusions, though these should be more specific and clear and relate to the recent literature on Spinosaurus habits to say what is, and is not, possible/plausible based on their analyses.

Overall this is likely to be a major step forwards in resolving the biology of this animal (and kin) and add considerable depth to the discussion by adding new data and results.

Reviewer #3 (Public Review):

In the manuscript by Bosada et al, the authors present work identifying and interrogating two cis-regulatory elements at TBX5 associated with atrial fibrillation. Mouse models lacking both copies of either element, but particularly one in the last intron of the Tbx5 gene, referred to as RE(int), results in increased Tbx5 expression, changes to cardiac electrophysiology, and downstream gene expression changes. Of interest, RE(int) induces expression of Prrx1, also associated with atrial fibrillation, and compound mutants partially rescues the RE(int) phenotype. Overall, this paper is of interest and advances our understanding of TBX5 in atrial fibrillation risk in humans. Critically, this study focuses on the impact of risk SNPs, which increase TBX5 expression in patients, while previous studies involving TBX5 in atrial fibrillation have focused on decreased expression.

The authors' work presents the following major claims:<br /> Figure 1. Identification of two, independently segregating risk regions at TBX5, which are conserved in humans and mice with predicted cis-regulatory functions termed RE(int) and RE(down).<br /> Figure 2. Homozygous RE(int) and RE(down) mutants, with a particular focus on RE(int) mutants, resulting in increased expression of Tbx5. The functional SNP appears to be rs7312625 A>G.<br /> Figure 3. Homozygous RE(int) mutants demonstrate several cardiac electrophysiological changes consistent with increased atrial fibrillation risk in humans.<br /> Figure 4. Cellular electrophysiology of RE(int) mutant cardiomyocytes demonstrates additional supportive changes to explain whole organ phenotypes presented in Figure 3.<br /> Figure 5. Transcriptional profiling of RE(int) and RE(down) homozygous mutants demonstrates many significant differences from control samples that are suggestive of specific mechanisms disrupting cardiac electrophysiology, including calcium and potassium regulators and gap junctions.<br /> Figure 6. Homozygous RE(int) and Prrx1(enh) mutant alleles genetically interact and result in partial rescue of phenotypes from RE(int) alone.

Reviewer #3 (Public Review):

Experimental and computational works have proposed that neurons in the hippocampus represent a predictive map of the environment called the successor representation. This theoretical study examines how plasticity in a model network of recurrently connected neurons can lead to such a representation. The main conclusion is that any plasticity rule that encodes transition probabilities in synaptic weights gives rise to the successor representation at the level of neural activity. This fundamental theoretical insight gives additional credibility to the idea that the hippocampus can implement the successor representation.

Strengths:<br /> - elegantly designed theoretical study<br /> - very clear writing that progressively introduces the main result and argues for its generality<br /> - comparison of the model with data in a random foraging task

Weaknesses:<br /> - certain technical choices need additional motivation

Reviewer #3 (Public Review):

The present study is a comparison of brain magnetic resonance imaging (MRI) of mice who developed in an enriched environment laboratory environment, in which some mice become habituated while other mice maintain active exploration of the environment over time. Between these groups, differences are shown in the pattern of correlations between brain regions of interindividual variability, which may indicate differences in brain connectivity or other shared maturational processes between regions. Because the mice are genetically inbred and have the same shared environment, these differences are attributed to individual-level differences in environment and behavior, which are extremely difficult to isolate in non-laboratory settings.

My comments are focused on aspects of the paper that overlap with my area of expertise which is human brain MRI methods. The strengths of the paper include the unique environmental paradigm that provides support for important hypotheses about individual-level variation. The imaging methods are rigorous and sound, and there is a nice convergence with human work. The application of structural covariance is interesting. The weaknesseses of the paper are that the writing could be clearer. Alternative explanations for structural covariance and alterations in "down roamers" should be more fully considered. The statistical approaches could be more rigorous in places. The areas of novelty relative to past work should be more explicitly articulated.

Reviewer #3 (Public Review):

Lillvis et al present a new method for quick targeted analysis of neural circuits through a combination of tissue expansion and (lattice) light sheet microscopy. Three color labeling is available which allows to label neurons of a molecularly specific type, presynaptic and/or post-synaptic sites.

Strengths:<br /> - The experimental technique can provide much higher throughput than EM<br /> - All source code has been made available<br /> - Manual correction of automatic segmentations has been implemented, allowing for an efficient semi-automatic workflow<br /> - Very different kinds of analyses have been demonstrated<br /> - Inclusion of electrical connections is really exciting, what a great complement to the existing EM volumes!

Weaknesses:<br /> - Limitations of the method are not really discussed. While the approach is simpler and cheaper than EM, it's still important to give the readers a clear picture of the use cases where it's not expected to work before they embark on the journey of acquiring tens of terabytes of data. Here are just a few examples of the questions I would have if I wanted to implement the method myself - I am a computational person and can easily imagine my "wet lab" colleagues would have even more to ask about the experimental side:

-- It is not very clear to me if the resolution of the method is sufficient to disentangle individual neurons of the same type. It has been demonstrated for a few examples in the paper, but is it generally the case? Are there examples of brain regions/neuron types where it wouldn't be possible? If another column was added to the table in Figure 1, e.g. "individual neuron connectivity", EM would be "+", LM "-", what would ExLLSM be?<br /> -- Similarly, the procedures for filling gaps in the signal could result in falsely merged neurons. Does it ever happen in practice?<br /> -- How long does semi-manual analysis take in person-hours/days for a new biological question similar in scope to the ones demonstrated in the paper?<br /> -- How robust are the networks for synaptic "blob" detection? The authors have shown they work for different reporters, when are they expected to break? Would you recommend to retrain for every new dataset? How would you recommend to validate the results if no EM data is available?

Reviewer #3 (Public Review):

Almedia and Macklin sought to characterize oligodendrocyte behavior at the earliest onset of myelination in the central nervous system. By sparsely labeling oligodendrocytes with transgenic fluorescent reporters in zebrafish larvae, they show that oligodendrocytes in the dorsal and ventral spinal cord have characteristic numbers of sheaths and sheath lengths. With impressive and technically laborious time-lapse imaging, they demonstrate that oligodendrocytes repetitively sample axon segments before stabilizing a nascent sheath, with most (~90%) immature sheaths failing to stabilize. They quantify differences in dorsal and ventral oligodendrocyte sampling and convincingly show that dorsal oligodendrocytes form more sheaths due to increased sampling relative to ventral, with similar rates of sheath retraction. Finally, the authors conclude that Rab5 and Rab11 promote myelination locally and cell-autonomously in oligodendrocytes, showing specifically that Rab5 is critical for stabilization of nascent sheaths but is dispensable for sampling. Altogether, the authors provide novel and detailed visualization of early myelin sheath development by oligodendrocytes.

Strengths:<br /> This is one of the first studies to closely examine early oligodendrocyte behavior at high resolution and adds to a body of work showing how oligodendrocytes initiate and maintain myelin sheaths. The authors find that sampling is widespread while most immature sheaths destabilize. This is an intriguing finding, as sampling is likely an energetically intensive process, but its prevalence in wild-type animals suggests that it is an important part of development.

The authors' claims are substantiated by technically challenging mosaic labeling experiments that monitored individual oligodendrocyte development over the course of days. Importantly, the authors have measured the sheath accumulation and loss phase for a single oligodendrocyte over the course of several days, and can pinpoint when individual sheaths are maintained with high resolution.

The imaging acquisition and data analyses are thorough, and the labor-intensive nature of the experiments is commendable. The authors carefully use statistics to validate their conclusions, including power analyses to determine appropriate sample size.

Limitations:<br /> Prior studies suggested that the potential for each oligodendrocyte to produce myelin sheaths is at least partially dependent upon the diameter of axons enwrapped. While axons are labeled to demonstrate ensheathment, axonal diameter is not measured, and it is unclear whether dorsal and ventral oligodendrocytes behavior could be explained by regional or individual differences in axon caliber.

Other recent studies suggest that early myelination is driven by axonal factors as much as oligodendrocyte-intrinsic factors. For instance, neuronal activity stabilizes myelination for a subset of early-born neuronal types. Because of the sparse labeling techniques and focus on oligodendrocyte behavior, it is unknown how or whether axonal subtypes and activity influence early oligodendrocyte sheath sampling and stabilization.

While the authors provide a tantalizing suggestion that early oligodendrocyte sampling primes axonal segments for myelination, it is not tested directly here. Thus, the paper does not address why, or even if, repeated sampling is important in development.

Reviewer #3 (Public Review):

The authors have constructed a large-scale interaction perturbation network from 2,167 CRC tissues and 308 normal tissues, deciphering six GINS subtypes with particular clinical and molecular peculiarities. In addition, the GINS taxonomy was rigorously validated in 19 external datasets (n =3,420) with distinct conditions. From an interactome perspective, this study identified and diversely validated a high-resolution classification system, which could confidently serve as an ideal tool for optimizing decision-making for CRC patients. The multifariously biological and clinical peculiarities of GINS taxonomy improve the understanding of CRC heterogeneity and facilitate clinical stratification and individuation management. Additionally, candidate specific-subtype agents provide more targeted or combined interventions for six subtypes, which also need to be validated in clinical settings.

Reviewer #3 (Public Review):

In this report, the authors examined 3 mutations in the BRC-repeat region of BRCA2 in a series of functional assays. They found that two of the mutants showed severe defects in BRCA2 function, whereas the third mutant had no clear phenotype. The two mutants with functional defects are tested most thoroughly. The assays used here a numerous and have been validated and performed with appropriate controls and statistics. There are no concerns about the experiments themselves or the conclusions. So, the strength of the study is the number of assays performed in a rigorous manner.

However, the weakness of the study is that it is unclear why these results are impactful. Several reports over the years, including some recent studies mentioned at the end of the Discussion, have involved parallel functional analysis of hundreds of alleles of BRCA2, with a clear end goal of improving medical decision-making for carriers of these BRCA2 alleles. Certainly, these studies have usually focused on other domains of BRCA2, like the DNA binding domain, but nonetheless, since these studies have typically involved testing hundreds of BRCA2 alleles, it is unclear how this manuscript studying 3 alleles fits into a broader population science effort to categorize BRCA2 variants of unknown significance (VUS). Perhaps the authors would argue that their study involves a comprehensive analysis of the 3 alleles, whereas other studies typically involve one or two functional assays. However, if that is the case, then is the argument that multiple assays are needed for accurate characterization of VUS? If so, what is the evidence for that assertion? Are there particular assays that are more likely to be predictive of pathogenicity based on their analysis?

The mechanistic insight of the study is also unclear. These alleles are in conserved residues of the BRCA2 BRC repeats, which have been established as being important for BRCA2 function. Indeed, in the Discussion, it appears that the findings here are largely confirmatory for other mechanistic studies of the BRC repeats of BRCA2. What new information has been determined about the role of the BRC2 and BRC7 repeats from this study?

Reviewer #3 (Public Review):

This study was designed to test the hypothesis that output from a subpopulation of neurons (PKCδ neurons) in the central nucleus of the amygdala (CeA) inhibits ZI neurons in a neuropathic pain condition and this ZI inhibition results in pain-related behaviors (Fig. 5).

First, the targets of CeA-PKCδ neurons were identified using cre-dependent viral vector for anterograde labeling with red-shifted channelrhodopsin (CrimsonR-tdTomato) or mCherry, and cholera toxin B (CTB) in PKCδ-tdTomato mice for retrograde labeling. The ZI was identified as one of the targets with approximately 19% of CTB+ CeA neurons identified as PKCδ- tdTomato positive, which is significant and makes this pathway worth exploring.

Next, electrophysiological (patch-clamp) studies showed monosynaptic inhibitory transmission from CeA to both VGAT+ and VGAT- neurons of the ZI and found no significant difference between these projections (from CeA to GABAergic or non-GABAergic ZI neurons).

Finally, chemogenetics are used to activate or silence GABAergic ZI neurons and determine behavioral consequences. Inhibition of GABAergic ZI neurons induced hypersensitivity in naïve mice and activation of these neurons reversed hypersensitivity in a neuropathic pain model. Interestingly, these effects were modality specific.

The combination of tracing techniques, electrophysiology, chemogenetics and behavior is a strength of this study, and so this the impressive amount of high-quality data. The focus on CeA-PKCδ neurons in the modulation of ZI is an important novelty of the present study.

However, slice physiology and behavioral data presented here do not actually link CeA-PKCδ neurons to ZI. Electrophysiological data show inhibitory transmission from CeA to ZI, but not specifically from CeA-PKCδ neurons to ZI. Behavioral studies assess the effects of modulation of ZI neurons but not of CeA-PKCδ to ZI projections. Previous data already showed the effects of activation and inhibition of GABAergic ZI neurons on pain behaviors, including in a neuropathic pain model.

Therefore, although the proposed model of CeA-PKCδ to ZI interactions in pain (Fig. 5) is novel and significant, additional experiments focusing on CeA-PKCδ neurons and their ZI projections would be needed to fully support this concept and enhance impact of the work.

Reviewer #3 (Public Review):

The authors have used both overall and local genetic correlations to understand how genes associated with two traits relate to those same traits. Their work focuses on understanding why in some cases local genetic correlations may disagree with overall correlation in terms of the direction of effect and exploit known biology to understand why and when this arises.

Overall the work is solid methodologically as it relies on well-established statistical methods and known biology. I don't see particular weaknesses in this work limited to the presented examples. It remains unclear how these observations will generalise to other less well-known biology or traits, but this is a matter of future work.

The work is in my opinion highly impactable as it creates a framework to be used to investigate the pleiotropic effects of genes and could help understand their biological role.

Reviewer #3 (Public Review):

This study reports on the phenotypes of a CRISPR-engineered zebrafish mutants in kinesin light chain 4 (KLC4). KLC4 is expressed prominently in spinal cord sensory neurons, and mutants have defects in peripheral axon branching/stabilization and branch repulsion, as well as make occasional ectopic axon branches. Imaging also demonstrates that axonal microtubule growth dynamics are altered. These axonal phenotypes are nicely characterized with beautiful light sheet time-lapse microscopy and clever image analyses methods. Additionally, the growth of adult KLC4 mutants is stunted, and they exhibit a variety of behavioral defects.

The strengths of this paper are the creation of a new mutant for studying axonal transport, the impressive imaging methods, and the development of image analysis methods for characterizing axonal trajectories across a population.

The main weaknesses is the lack of a specific mechanistic explanation for how kinesin dysfunction leads to axonal defects-what kinesin cargoes play a role in branch stabilization and branch repulsion? How does kinesin-mediate transport affect microtubule growth?

Another weakness is the lack of a connection between the cellular defects characterized in larval sensory neurons, and the behavioral defects in adults. Since the adult behavioral defects likely do not involve sensory neurons, these two parts of the paper don't fit together. The authors may want to consider moving the behavior to a different paper. Additionally, the cellular basis of the adult behavioral defects is unknown, and likely involves a complex combination of defects in multiple cell types.

Reviewer #3 (Public Review):

In this manuscript, Zhou et al describe basal cell heterogeneity in the mouse trachea. They describe how dorsally vs ventrally located tracheal basal cells which are supported by different stromal cell populations show differential potential to undergo squamous metaplastic differentiation. Furthermore, they suggest that the differences in these basal cells might be epigenetically programmed as they are maintained after these basal cells have been isolated and cultured in vitro. However, it is not clear whether dorsal vs ventral supporting stromal cell populations made it into the culture medium.

Reviewer #3 (Public Review):

This work is important for understanding both how immune cells are regulated and how alterations in receptor signaling can affect the balance of health and development of autoimmune diseases. The work uses CRISPR-based genetic manipulation of the autoimmunity associated PTPN22 gene in single donor human cord-derived naïve T cells to analyze T-cell receptor functions. The authors conclude that the autoimmunity associated PTPN22 variant PTPN22(620W) is a loss-of-function mutant as T cells expressing PTPN22(620W) phenocopies PTPN22 deficient T cells. The use of a single donor minimizes potential other effects that would be observed when comparison cellular functions from multiple donors.

Reviewer #3 (Public Review):

Angueyra et al. tried to establish the method to identify key factors regulating fate decisions in the retinal visual photoreceptor cells by combining transcriptomic and fast genome editing approaches. First, they isolated and pooled five subtypes of photoreceptor cells from the transgenic lines in each of which a specific subtype of photoreceptor cells are labeled by fluorescence protein, and then subjected them to RNAseq analyses. Second, by comparing the transcriptome data, they extracted the list of the transcription factor genes enriched in the pooled samples. Third, they applied CRISPR-based F0 knockout to functionally identify transcription factor genes involved in cell fate decisions of photoreceptor subtypes. To benchmark this approach, they initially targeted foxq2 and nr2e3 genes, which have been previously shown to regulate S-opsin expression and S-cone cell fate (foxq2) and to regulate rhodopsin expression and rod fate (nr2e3). They then targeted other transcription factor genes in the candidate list and found that tbx2a and tbx2b are independently required for UV-cone specification. They also found that tbx2a expressed in the L-cone subtype and tbx2b expressed in L-cones inhibit M-opsin gene expression in the respective cone subtypes. From these data, the authors concluded that the transcription factors Tbx2a and Tbx2b play a central role in controlling the identity of all photoreceptor subtypes within the retina.

Overall, the contents of this manuscript are well organized and technically sound. The authors presented convincing data, and carefully analyzed and interpreted them. It includes an evaluation of the presented data on cell-type specific transcriptome by comparing it with previously published ones. I think the current transcriptomic data will be a valuable platform to identify the genes regulating cell-type specific functions, especially in combination with the fast CRISPR-based in vivo screening methods provided here. I hope that the following points would be helpful for the authors to improve the manuscript appropriately.

1) The manuscript uses the word "FØ" quite often without any proper definition. I wonder how "Ø" should be pronounced - zero or phi? This word is not common and has not been used in previous publications. I feel the phrase "F0 knockout", which was used in the paper cited by the authors (Kroll et al 2021), is more straightforward. If it is to be used in the manuscript, please define "FØ" and "CRISPR-FØ screening" appropriately, especially in the abstract.

2) Figure 1-supplement 1 shows that opn1mw4 has quite high (normalized) FPKM in one of the S-cone samples in contrast to the least (or no) expression in the M-cone samples, in which opn1mw4 is expected to be detected. The authors should address a possible origin of this inconsistent result for opn1mw4 expression as well as a technical limitation of using the Tg(opn1mw2:egfp) line for detection of opn1mw4 expression in the GFP-positive cells.

3) The manuscript lacks a description of the sampling time point. It is well known that many genes are expressed with daily (or circadian) fluctuation (cf. Doherty & Kay, 2010 Annu. Rev. Genet.). For example, the cone-specific gene list in Fig.2C includes a circadian clock gene, per3, whose expression was reported to fluctuate in a circadian manner in many tissues of zebrafish including the retina (Kaneko et al. 2006 PNAS). It appears to be cone-specific at this time point of sample collection as shown in Fig.2, but might be expressed in a different pattern at other time points (eg, rod expression). The authors should add, at least, a clear description of the sampling time points so as to make their data more informative.

Reviewer #3 (Public Review):

At the heart of this manuscript is a debate concerning the role of the orbitofrontal cortex (OFC) in goal-directed behavior. One commonly sees a paper in which Ostlund and Balleine placed large OFC lesions in behaviorally-experienced rats cited as irrefutable evidence that OFC is not involved in goal-directed behavior because these rats could perform typically in a simple devaluation task. Meanwhile, others have argued that the ventrolateral OFC (VLO) sits at a nexus between the medial PFC structures (which are attuned to reinforcer value, etc.) and the far lateral regions (which appear to be more specialized in Pavlovian associations) and may therefore play a role in goal-directed behavior (e.g., this argument is put forward in Gourley and Taylor, 2016, Nature Neuroscience). The present team published a crucial manuscript a couple of years ago showing that selective VLO lesions do indeed disrupt goal-seeking behaviors, particularly when value and contingency information needs to be integrated and/or updated (Parkes 2018). Because this sophisticated process is not tested in simple devaluation assays, it would have been missed in the older study. The Parkes 2018 paper, meanwhile, supports other investigations that also selectively manipulate the VLO and require animals to integrate new information into existing instrumental response strategies.

Here, the team first depleted NE fibers in the OFC and found that rats were unable to encode new associations in an instrumental reversal. This same deficit was not observed with parallel DA manipulation. They found that LC-OFC and not mPFC projections had the same effect. Throughout, important control experiments were conducted, and the tools being used were largely well-validated. The conclusions are sensible, and the writing is clear.

I would be curious about the authors' thoughts regarding the recent Duan ... Robbins Neuron paper (https://pubmed.ncbi.nlm.nih.gov/34171290/), in which marmosets displayed paradoxical responses to VLO inactivation and stimulation in contingency degradation tasks. Are there ways to reconcile these reports?

Reviewer #3 (Public Review):

The authors constructed a single-cell transcriptome atlas of bone marrow in normal and R-ISS-staged MM patients. A group of malignant PC populations with high proliferation capability (proliferating PCs) was identified. Some intercellular ligand receptors and potential immunotargets such as SIRPA-CD47 and TIGIT-NECTIN3 were discovered by cell-cell communication. A small set of GZMA+ cytotoxic PCs was reported and validated using public data.

For scRNA-seq data analysis, the authors did QC and filtering and removed low quality cells, including some doublets and followed by batch effect correction. Malignant PC populations were identified using the copy number analysis tool - "inferCNV".

The authors have done lots of analysis. But I think the results can be improved if they can do more analyses. I would recommend to 1) analyze doublets; 2) remove cell cycle effect; 3) GO and pathway analysis for genes with copy number change; 4) do cell-cell communication with more cell type/clusters.

Data analysis of public data was sufficient to prove the small set of GZMA+ cytotoxic PCs. More data analysis or wet experiment proof is required.

Reviewer #3 (Public Review):

The authors identified a splicing factor that regulates mitochondrial homeostasis by regulating the alternative splicing of the pro-apoptotic protein BAX, which induces basal upregulation of interferon stimulated genes and sensitizes cells to apoptotic cell death. They report that loss of Serine/Arginine Rich Splicing factor 6 (SRSF6) results in accumulation of an alternatively spliced form of BAX known as BAX-, which results in increased release of mitochondrial DNA (mtDNA). The released mtDNA is sensed by cGAS, which leads to upregulation of interferon stimulated genes via IRF3. Importantly, the increase in BAX- sensitizes macrophages to apoptosis and various pathogens decreased the expression of SRSF6 during infection, which served a protective role. Interestingly, Mycobacterium tuberculosis decreases SRSF6 expression, but this resulted in a replication advantage. Overall, these findings add new mechanistic insight into the role of alternative splicing in regulating immunity and cell death. This work can potentially open novel avenues of inquiry into the role of BAX in regulating apoptosis.

Strengths:

The paper is well written, and the major conclusions are rigorously tested by numerous experiments. The data supports the major conclusions, which are that loss of SRSF6 increases ISG and leads to accumulation of alternatively spliced BAX, sensitizing cells to death.

Weaknesses:

The authors make a very interesting discovery that SRSF6 KD sensitizes macrophages to a caspase independent death by up regulating an alternatively spliced variant of BAX, a protein that has a well-established role in mediating caspase dependent death, but they did not rigorously test whether it was truly caspase independent.

Reviewer #3 (Public Review):

In the manuscript, the authors provided the development of a sensitive and rapid diagnostic tool for detection of pathogenic bacteria in respiratory infections given the limitations of traditional cultures in the clinical settings. Rapid identification and treatment of bacterial infections can impact the prognosis in sepsis. This work highlights how a new rapid diagnostic tool may be beneficial in the treatment of patients with bacterial pneumonia given the time-consuming nature and low sensitivity of traditional culture methods.

Strengths:

The manuscript authors created a diagnostic tool using CRISPR-Cas12 with bacterial species-specific DNA-tags to 10 epidemic bacteria at their local intensive care unit (ICU). The appendix data provided detailed reports of the reaction conditions, sample preparations and reaction incubation time.

A 2-stage validation process was used. The initial validation stage compared the use of the novel diagnostic tool to traditional cultures from bronchoalveolar lavage samples from ICU patients. Once the accuracy of the diagnostic tool was evaluated, the second validation stage was pursued in the form of a randomized controlled trial at the ICU of the study. The second validation stage demonstrated that the proposed novel diagnostic tool had faster results and correlated with improved APACHE II scores and more effective antibiotic coverage rates in the experimental group.

The use of the novel diagnostic test highlighted limitations traditional culture modalities may have in identifying polymicrobial infections which were identified more frequently in the two validation stages

Weaknesses:

Although the study has many strengths, a potential weakness could lie in the unclear use of next-generation sequence (NGS) testing where samples were reported to be sent at random. However, similar to the novel diagnostic tool proposed in this manuscript, NGS testing has been noted to have high sensitivity and specificity and both had similar results in the manuscript.

Additionally, the novel diagnostic testing demonstrated increased detection of polymicrobial infection when compared to traditional cultures; however, clinical evaluation will remain important to help decipher potential "false positive" results or identification of non-pathogenic colonization.

Based on the author's proposed aims to develop a rapid and sensitive diagnostic tool for bacterial pathogens in pneumonia; the authors demonstrated a highly sensitive and specific test when compared to gold-standard testing. Random samples were assessed against NGS testing technology with similar reported results. The development of this rapid, sensitive diagnostic tool can have wide-spread clinical implications to guide management in patient care where earlier time to effective treatment can have important impacts on prognosis.

Reviewer #3 (Public Review):

In the manuscript by Gao et al, the authors were trying to achieve an understanding of how Kiaa1024L/Minar2 is necessary for hearing in vertebrates. It is known that the Kiaa1024L/Minar2 mutation causes deafness in mice but not much beyond that is known.

Strengths:<br /> - In this manuscript, they were successful in making two zebrafish mutant zebrafish strains in the Kiaa1024L/Minar2 gene using Crispr/Cas9. The mutant(s) has defects in hearing (using the C-start assay and determining thresholds) and reduced hair cell numbers in the ear (phalloidin labeling to determine hair cell density in utricle and saccule) and the lateral line (including using the AM1-43 assay). From these data, they demonstrate that hair cells are defective in these mutants.

- The authors show that Lamp1-GFP labeled lysosomes change in size in the minar2fs139 mutant. In addition, they show that GFP-Minar2 localizes to lysosomal membranes in cultured cells (human and monkey).

- They performed primary amino acid sequence analysis on Minar2 and showed that it contained a putative CSD of caveolin, which is known to interact with cholesterol. They then show that when Minar2 is expressed in cells in culture, there is an increase in cholesterol detection in the region that contained Minar2, supporting the idea that cholesterol interacts with Minar2.

The experiments in figure 5 seem to show that lowering cholesterol levels using pharmacology exacerbates hair cell defects in a minar2 mutant.

Weaknesses:<br /> 1. The authors attempt to show localization (Fig 2 A and B) of Minar2 to the stereocilia and the apical region of hair cells using GFP-MINAR2 fusion protein expression in hair cells of transgenic animals. Although this is a typical way of demonstrating localization, it is usually used to validate location after a similar pattern has been shown using an antibody (usually in mice.) So, special precautions must be taken when interpreting this kind of transgenic data. According to the authors, GFP-MINAR2 localized to the stereocilia and the apical region of hair cells. This needs to be validated by some other means. I can also see the localization of the green signal at the basolateral area of the cells in Fig 2a. Moreover, it's important to note that other mislocalized fusion proteins localize to the apical region of hair cells.

2. Figure 2C and D. The defects in the hair bundles are plausible but not convincing. Electron microscopy should be used to validate. Also, are hair bundle defects seen in the neuromast? EM would be easier to do there.

3. Fig 1A do prim 1- and prim 2-derived neuromasts express minar2? Do anterior neuromasts express minar2?

4. It's my impression that the authors don't take into account that there is much more plasma membrane in the stereocilia than in the basolateral membrane. So, this statement, "These data suggested that there are high levels of accessible cholesterol located to the stereocilia membranes, while the accessible cholesterol levels are marked lower in the basolateral membranes in the hair cells" based on Figure 4 needs to be reconsidered. The authors need to show that the little reporter that is present in the basolateral membrane is not equal to the reporter present in a single sheet of the plasma membrane in a stereocilium. I can see basolateral labeling in the lateral line hair cells.

5. It's not clear if there is a paralog of the Kiaa1024L/Minar2 gene.

Reviewer #3 (Public Review):

The manuscript by Sureshchandra et al is a very extensive analysis of monocyte function and their molecular landscape in cord bloods from lean and obese mothers. They aimed to analyze the effects of pre-pregnancy BMI on the functioning of the innate immune system in newborns in a very extensive way. The combination of functional and molecular analyses strengthens their observations and shows many different sides of monocyte activation. I think this approach needs to be praised and should be an inspiration to many others who study monocyte function. This allows for a broad view on the matter and also shows where potential targeting will be necessary in the future. Overall, the manuscript and particularly the methods section is very well written and extensive, making it easy to study how robust the data are.

Reviewer #3 (Public Review):

Through a series of rigorous in vitro studies, the authors determined McdB's domain architecture, its oligomerization domains, the regions required for phase separation, and how to fine-tune its phase separation activity. The SEC-MALS study provides clear evidence that the α-helical domains of McdB form a trimer-of-dimers hexamer. Through analysis of a small library of domain deletions by microscopy and SDS-PAGE gels of soluble and pellet fractions, the authors conclude that the Q-rich domain of McdB drives phase separation while the N-terminal IDR modulates solubility. A nicely executed study in Figure 4 demonstrated that McdB phase separation is highly sensitive to pH and is influenced by basic residues in the N terminal IDR. The study demonstrates that net charge, as opposed to specific residues, is critical for phase separation at 100 micromolar. In addition, the experimental design included analysis of McdB constructs that lack fluorescent proteins or organic dyes that may influence phase separation. Therefore, the observed material properties have full dependence on the McdB sequence.

Studies of proteins often neglect short, disordered segments at the N- or C- terminus due to unclear models for their potential role. This study was interesting because it revealed a short IDR as a critical regulator of phase separation. This includes experiments that remove the IDR (Fig 2 & 3) and mutate the basic residues to show their importance towards McdB phase separation. In a nice set of SDS-PAGE experiments, the authors showed that as the net charge of the IDR decreased the construct became more soluble.

One challenge is in the experimental design when mutating residues is to assess their impact on phase separation. The author's avoided substitutions to alanine, as alanine substitutions have synthetically stimulated phase separation in other systems. The authors, therefore, have a good rationale for selecting potentially milder mutations of lysine/arginine to glutamine. A potential caveat of mutation to glutamine is that stretches of glutamines have been associated with amyloid/prion formation. So, the introductions of glutamines into the IDR may also have unexpected effects on material properties. Despite these caveats, the authors show mutation of six basic residues in the short IDR abolished phase separation at 100 mM.

Computational studies (Fig 7) also suggest that this short N-IDR region may play a role as a MORF upon potential binding to a second protein McdA. The formulation of this hypothesis is strengthened by the fact that for other ParA/MinD-family ATPases, the associated partner proteins have also been shown to interact with their cognate ATPase via positively charged and disordered N-termini. This aspect of understanding McdB's N-IDR as a MORF is at a very early stage. This study lacks experimental evidence for an N-IDR: McdA interaction and experimental data showing conformational change upon McdA binding. However, the computation study sets up the future to consider whether and how the phase separation activity of McdB is related to its structural dynamics and interactions with McdA.

In summary, this study provides a strong foundation for the contribution of domains to McdB's in vitro phase separation. This knowledge will inform and impact future studies on McdB regulating carboxysomes and how the related family of ParA/MinD-family ATPases and their cognate regulatory proteins. For example, it is unknown if and how McdB's phase separation is utilized in vivo for carboxysome regulation. However, the revealed roles of the Q-rich domain and N-IDR will provide valuable knowledge in developing future research. In addition, the systematic domain analysis of McdB can be combined with a similar analysis of a broad range of other biomolecular condensates in bacteria and eukaryotes to understand the design principles of phase separating proteins.

Reviewer #3 (Public Review):

In this manuscript, the authors aim to identify the regulators of epithelial invasiveness upon Lethal giant larvae (Lgl), a basolateral polarity protein, knockdown in the follicular epithelium of the Drosophila ovaries, which can serve as a model system to investigate cellular plasticity when apical-basal polarity is lost. Knockdown (KD) of Lgl causes a multilayered epithelium and through extensive single cell RNA-seq analyses, the authors demonstrate that Lgl-KD triggers the appearance of groups of cells exhibiting tumor-associated molecular signatures and invasive behaviour. Overall, the manuscript is technically sound and the combination of computational and experimental approaches results in a thorough characterisation of the earliest steps of epithelial de-stabilisation upon the loss of apical-basal polarity. In my view, the aims set by the authors are met and the experimental data provided support the claims. Interpretations are balanced and the display items are presented logically and informatively for even non-experts. Together, this work will set the basis for further investigations using apical-basal destabilisation of the follicle epithelium as a model of epithelial tumorigenesis.

Reviewer #3 (Public Review):

Barsi-Rhyne reports a novel mode of engagement of beta arrestins as endocytic adaptors and associates this novel mode together with the previously known canonical mode to the regulation of endocytosis and signaling by class A versus class B receptors. The manuscript is very well written, very good to read, almost flawless, extremely interesting, and highly relevant to the GPCR field with very well-crafted figures and fantastic microscopy.

Reviewer #3 (Public Review):

The authors use a previously developed technology, CRISPR activation screening, in which pooled sgRNAs are used to guide an RNA-associated regulatory complex (MS2-p65-HSF1 transcriptional activators) to promoter regions resulting in increased expression of a specific target gene. The authors screen two different pooled libraries TM1 (single pass) and TM2+ (multiple pass) with 20 different recombinant biotinylated soluble ligands and identified 22 novel interactions. These interactions were further characterized by SPR and cell-based binding experiments; however, several of the interactions are low affinity and were not characterized for any activity or function beyond the relatively weak biochemical binding. Therefore, while the data provide evidence of potential novel interactions, the biological relevance remains unclear.

Reviewer #3 (Public Review):

Aside from one critical reservation, I thought this paper was excellent. The figures are clear, the manuscript is well-written, the scope of the study is well-defined (i.e. it characterizes traveling beta), and the authors were circumspect in all aspects of the work, with the authors' consideration of wave propagation along different cortical meshes being but one example in a generally deft and careful approach.

However, the inverse problem remains the inverse problem, and I believe there is one thorny issue to treat regarding the 3D geometry of the central sulcus as it pertains to synchronized beta events before I can accept the authors' conclusions. After this subtle issue is treated, I believe the work will be an important step forward and generally impactful on the community interested in human brain rhythms.

The authors were gracious enough to raise the issue of spatially synchronized events themselves in their discussion: Their argument, with which I mainly agree, is that the beamformer method essentially removes synchronous components from consideration, leaving the traveling component for analysis.

However, synchronization across the sulcus introduces a further bias into event detection by means of physical source-cancellation. I will here defer to Ahlfors et al (2010), who state that "Substantial cancellation occur also for locally extended patches of simulated [cortical] activity, when the patches extended to opposite walls of sulci and gyri."

With that in mind, let's look at Figure 1, where the authors seem to show a higher density of beta events relatively deep in the sulcus compared to the sulcal walls. This is certainly an interesting result if true! But even given only the occasional synchronization of mesoscale cortical neighborhoods, it appears that events in the sulcal walls will still be systematically undersampled and those deep in the sulcus oversampled here, by vice or virtue of cortical geometry as it pertains to the magnetic field.

This spatial sampling bias could impact nearly all aspects of the event propagation analysis that follows, and so I believe it must be considered in some detail before I can fully agree with the manuscript's conclusions.

Reviewer 3 (Public Review):

This is an interesting study that describes a single cell RNAseq analysis of human menisci. The study describes cell profiling of healthy and degenerated menisci divided into two zones, inner and outer meniscus.

Reviewer #3 (Public Review):

This article by Roberts, Hayden and colleagues expands on an interesting high-throughput experimental approach developed by Kobori and Yokobayashi (2016; Angew Chem) by determining the relative activity for every possible single and double mutant of five known self-cleaving ribozymes. While this approach is not in itself new, the fact that the authors analyze their data by looking at epistasis (non-additive effects between pairs of mutations) provides an additional opportunity for extracting meaningful structural information that is proposed to be similar to chemical or enzymatic probing experiments obtained on these self-cleaving ribozymes. In fact, this type of high throughput mutagenesis analysis might provide data closer to comparative sequence analysis and as such, might provide even more reliable structural information than structural probing experiments, especially when a relative activity can be properly assessed for the studied RNAs.

(1) Overall, the experiments have been carefully performed and the data seem to be highly reliable.<br /> (2) The strength of this article is that it demonstrates the generality of the approach initially developed by Kobori and Yokobayashi (2016; Angew Chem) by validating its usefulness in identifying most (if not all) the structural features of the studied ribozymes. The determination of positive and negative epistasis is very useful as it can facilitate the identification of base pairs covariations that are indicative of RNA structural elements.<br /> (3) At the present time, the authors have not really discussed how their data analysis compares to comparative sequence analysis. This aspect is important.<br /> (4) It is necessary to mention more clearly that this article builds on the method of Kobori and Yokobayashi (2016). Overall, with the exception of a few experimental details, the experimental method described herein is almost identical to the one of Kobori and Yokobayashi (2016) and this should be better emphasized.<br /> (5) Most importantly, this article provides an analysis of self-cleaving ribozymes for which the three-dimensional structures are known. Considering the scope of this article, instead of mostly focusing on the 2D structural aspect, it would be absolutely necessary to provide more 3D structural information.<br /> (6) When a self-modifying enzymatic activity is associated with the studied RNA, a relative activity could potentially be derived from high throughput sequencing. Could the authors expand on the generality and requirement of their high throughput approach for the study of RNA?

Reviewer #3 (Public Review):

Menjivar et al. present an analysis of the role of immunosuppressive Arginase 1 in myeloid cells in pancreatic cancer. They show that depletion of Arg1 in macrophages leads to attenuation in progression from PanIN to PDAC and use single cell analysis to understand underlying changes in immune activation, including an increase in cytotoxic T cells. Interestingly, the authors observed what seems to be a compensatory upregulation in Arg1 in epithelial cells and used arginase1 inhibitor to assess the therapeutic potential of targeting Arg1 systemically. This study is overall well performed and generates novel mouse models to study immunosuppression in pancreatic cancer. While the notion that Arginase1 is immunosuppressive is not novel, the observation that Arg1 is upregulated in epithelial cells is interesting. There are several instances of overstating conclusions that, if addressed in the main text (not just relegated to the discussion section), could significantly strengthen the manuscript.

Reviewer #3 (Public Review):

The central conclusion of this beautiful experimental study is that bumblebees prefer flowers on the basis of their remembered ranking in their context, but are insensitive to their absolute properties. Thus, let's say that there 4 flower types, ranked as follows in nectar concentration: A>B>C>D. However, when the bee learns about these flowers, it does in either of two 'contexts', populated as follows: A & B, or C & D. Thus, the bee experiences that B is the worse option in the context in which it is found, and C is the better one in its own context. If, at a later time, the bee has to make a novel choice, this time between B and C, its memory for ranking leads it to prefer C over B, while its (putative) memory for nectar concentration should favour B over C. The authors find, in a variety of different treatments, evidence for the influence for ranking, but they do not find any evidence for sensitivity to absolute properties (i.e., concentration).

One difficulty that permeates the argument is the ubiquitous difficulty in proving the null hypothesis as true: lack of significant evidence for a putative effect in one or a few experiments, does not mean reliable absence of the effect.

Another difficulty is that in my view memory for absolute properties was not given a full chance: bees were always trained in situations where both dimensions (concentration and ranking) were present. In such situations, they preferentially used ranking. However, to learn ranking between flower types in sequential encounters, they must remember the absolute properties, so that in each encounter they contrast the present flower with the memory for others. Say the bee encounters a type B flower. How does it store its ranking if it doesn't remember the properties of A at all? To take this objection into account and still maintain the claim, it is necessary to say that it remembers the properties of A when in the A & B context, but it erases it from memory when in the context B & C.

Neglecting memory for concentration may be an overshadowing effect. Overshadowing is known in learning studies, and it means that, when more than one cue is paired with an outcome, the most salient between them may reduce learning about the predicting power of the other. In this case, bees may remember and use concentration when trained in contexts where there is only flower type, so that there is no chance of using ranking, and then offered choices between pairs of them. In this case, the bees would not have access to ranking, so that there would be a stronger opportunity for absolute memory to manifest itself.

In experiment 4, during training, they could move between two zones representing the 'contexts', each with 2 flower types, and they were then given choices between the 4 types, rather than just binary choices as previously. In this case, the bees did prefer the top-quality flower type (type A), which is consistent with memory for absolute concentration and with ranking, because A offered the highest concentration of the 4-type context. Why this happened is not clear, but it indicates that the context of choice may be crucial. It is known from other studies that the number of options at the time of choice can be very influential. For instance, in one study, it was shown that starlings appeared to be risk prone when offered a binary choice and risk averse when offered a trinary choice, even if the choices were all intermingled in the same sessions. In any case, this experiment raises doubts as to the claimed insensitivity to memory for nectar concentration. Another possibility is that the separation between contexts in this experiment (a partially avoidable wall) was not extreme as in the previous ones, so that the bees could now establish a ranking among the 4 types because they were all encountered intermingled to an extent.

There is one potential mechanism that may also be discussed. It is known from other species, that state at the time of learning influences subjective value of alternatives. To explain this effect I will exemplify the problem with a non-eusocial consumer. Say that food sources B and C are of equal caloric value. Say, further, that B is encountered when the subject is less food deprived than when it encounters C. Then the hedonic (conditioning) power of B will be lower, because it causes a smaller improvement in fitness (this was Daniel Bernoulli's argument regarding the concept of utility). In animal studies this effect is called State-Dependent Valuation Learning (SDVL). Since in the present experiments the context A & B was richer than the context C & D, the bees would have been in a consequently more favourable state (maybe carrying bigger sugar loads), so that each encounter with B would cause a smaller improvement than each encounter with C. This effect is totally different from remembering the ranking of flower types. The two alternative explanations for preference of C over B (ranking and SDVL) can, fortunately, be confronted because it is possible to change the state of the bees by a common 3rd source that could be used to equate or manipulate the average richness of the contexts.

All the reasons mentioned above should make it clear that this reviewer finds the study of very great interest and much merit, but considers that the conclusion for exclusive impact of ranking on preference should be tempered, or at least defended more strongly against these doubts.

Reviewer #3 (Public Review):

In this ms Li et al. examine the molecular interaction of Rabphilin 3A with the SNARE complex protein SNAP25 and its potential impact in SNARE complex assembly and dense core vesicle fusion.

Overall the literature of rabphilin as a major rab3/27effector on synaptic function has been quite enigmatic. After its cloning and initial biochemical analysis, rather little new has been found about rabphilin, in particular since loss of function analysis has shown rather little synaptic phenotypes (Schluter 1999, Deak 2006), arguing against that rabphilin plays a crucial role in synaptic function.

While the interaction of rabphilin to SNAP25 via its bottom part of the C2 domain has been already described biochemically and structurally in the Deak et al. 2006, and others, the authors make significant efforts to further map the interactions between SNAP25 and rabphilin and indeed identified additional binding motifs in the first 10 amino acids of SNAP25 that appear critical for the rabphilin interaction.

Using KD-rescue experiments for SNAP25, in TIRF based imaging analysis of labeled dense core vesicles showed that the N-terminus of SN25 is absolutely essential for SV membrane proximity and release. Similar, somewhat weaker phenotypes were observed when binding deficient rabphilin mutants were overexpressed in PC12 cells coexpressing WT rabphilin. The loss of function phenotypes in the SN25 and rabphilin interaction mutants made the authors to claim that rabphilin-SN25 interactions are critical for docking and exocytosis. The role of these interaction sites were subsequently tested in SNARE assembly assays, which were largely supportive of rabphilin accelerating SNARE assembly in a SN25 -terminal dependent way.

Regarding the impact of this work, the transition of synaptic vesicles to form fusion competent trans-SNARE complex is very critical in our understanding of regulated vesicle exocytosis, and the authors put forward an attractive model forward in which rabphilin aids in catalyzing the SNARE complex assembly by controlling SNAP25 a-helicalicity of the SNARE motif. This would provide here a similar regulatory mechanism as put forward for the other two SNARE proteins via their interactions with Munc18 and intersection, respectively.

While discovery of the novel interaction site of rabphilin with the N-Terminus of SNAP25 is interesting, I have issues with the functional experiments. The key reliance of the paper is whether it provides convincing data on the functional role of the interactions, given the history of loss of function phenotypes for Rabphilin. First, the authors use PC12 cells and dense core vesicle docking and fusion assays. Primary neurons, where rabphilin function has been tested before, has unfortunately not been utilized, reducing the impact of docking and fusion phenotype.

In particular the loss of function phenotype in figure 3 of the n-terminally deleted SNAP25 in docking and fusion is profound, and at a similar level than the complete loss of the SNARE protein itself. This is of concern as this is in stark contrast to the phenotype of rabphilin loss in mammalian neurons where the phenotype of SNAP25 loss is very severe while rabphilin loss has almost no effect on secretion. This would argue that the N-terminal of SNAPP25 has other critical functions besides interacting with rabphilin. In addition, it could argue that the n-Terminal SNAP25 deletion mutant may be made in the cell (as indicated from the western blot) but may not be properly trafficked to the site of release.

Reviewer #3 (Public Review):

The manuscript by Le T.D.V. et al used in vitro cell culture and inhibitors for cellular signaling molecules and found that GLP-1 receptor activation stimulated the phosphorylation of Raptor, which was PKA-mediated and Akt-independent. The authors reported the physiological function of this GLP-1R-PKA-Raptor in liraglutide stimulated weight loss. This timely study has high significance in the field of metabolic research for the following reasons.

(1) The authors' findings are significant in the field of obesity research. GLP-1 receptor (GLP-1R) is a successful target for diabetes (and weight loss) therapeutics. However, the mechanisms of action for the weight-loss effect of GLP-1 agonists are not fully understood. Therefore, mechanistic studies to elucidate the signaling pathways of GLP-1 receptors pertaining to weight loss at the cellular level are timely.

(2) G protein-coupled receptors (GPCRs) induces various signaling activities, which could be cellular and tissue specific. As these are an important protein family for drug targeting, understanding the basic biology of these receptors is of interest to a broad readership.

(3) The authors have made important discoveries that Exendin-4 stimulated mTORC1 signaling was essential for the anorectic effect induced by Exendin-4. The study reported in this current manuscript provides more details of brain GLP-1R signaling pathways and is innovative.

Overall, the authors have presented sufficient background in a clear and logically organized structure, clearly stated the key question to be addressed, used the appropriate methodology, produced significant and innovative main findings, took potential caveats into consideration, and made a justified conclusion.

The manuscript can be further strengthened with more clarification on the following points.

1. In Figure 1 panels B and C, please provide the quantification for pCREB/CREB. In Figure 1 panel D, please provide the quantification for pAkt/Akt.

2. The western blots to assess the signaling activities revealed the phosphorylation status of the key signaling molecules at a single time point. Whether the overall signaling dynamics have been affected is unclear.

3. Figure 3 panels A and B demonstrated the remarkable importance of the Ser791 Raptor. However, this PKA-resistant mutant did not completely abolish the weight loss effect of Liraglutide. The authors pointed out the importance of AMPK in mTORC1 signaling. Other pathways that may complement GLP-1R-PKA-Raptor signaling can be further discussed.

4. Food intake was decreased on day 2 in Figure 3D but became comparable between WT and S791A Raptor groups on the following days. Could this be due to some compensatory mechanisms?

Reviewer #3 (Public Review):

The authors identify tse1, a gene located in the type 6 secretion system (T6SS) locus of the bacterium Pseudomonas chlororaphis, as necessary and sufficient for induction of Bacillus subtilis sporulation. The authors demonstrate that Tse1 is a hydrolase that targets peptidoglycan in the bacterial cell wall, triggering activation of the regulatory sigma factor sigma-w. The sporulation-inducing effects of sigma-w are dependent on the downstream presence of the sensor histidine kinases KinA and KinB. Overall, this is a well-structured paper that uses a combination of methods including bacterial genetics, HPCL, microscopy, and immunohistochemistry to elucidate the mechanism of action of Tse1 against B. subtilis peptidoglycan. There are some concerns regarding a few experimental controls that were not included/discussed and (in a few figures) the visual representation of the data could be improved. The structure of the manuscript and experiments is such that key questions are addressed in a logical flow that demonstrates the mechanisms described by the authors.

To begin, we have concerns regarding the sporulation assays and their results. The data should be presented as "Percent sporulation" or "Sporulation (%)" - not as a "sporulation rate": there is no kinetic element to any of these measurements, so no rate is being measured (be careful of this in the text as well, for instance near lines 204). More importantly, there is no data provided to indicate that changes in percent spores are not instead just the death of non-sporulated cells. For example, imagine that within a population of B. subtilis cells, 85% of the cells are vegetative and 15% are spores. If, upon exposure to tse1, a large proportion of the vegetative cells are killed (say, 80% of them), this could lead to an apparent increase in sporulation: from 15% for the untreated population to ~50% of the treated, but the difference would be entirely due to a change in the vegetative population, not due to a change in sporulation. The authors need to clearly describe how they conducted their sporulation assays (currently there is no information about this in the methods) as well as provide the raw data of the counts of vegetative cells for their assays to eliminate this concern.

A related concern is regarding the analysis of the kinases and the effects of their deletions on the impact of Tse1. Previous literature shows that the basal levels of sporulation in a B. subtilis kinA or a kinB mutant are severely defective relative to a wild-type strain; these mutants sporulate poorly on their own. Therefore, the data presented on Lines 394+ and the associated Supplemental Figure regarding the sporulation defects of these two mutants are not compelling for showing that these kinases are required for this effector to act. It is likely that simply missing these kinases would severely impact the ability of these strains to sporulate at all, irrespective of the presence of Tse1, and no discussion of this confounding concern is discussed.

Another concern is regarding the statistical tests used in Figure 2. For statistical tests in A, B, and D, it should be stated whether a post-test was used to correct for multiple comparisons, and, if so, which post-test was used. For C, we suggest the inclusion of a mock control in addition to the two conditions already included (i.e., an extraction from an E. coli strain expressing the empty vector) to provide a stronger control comparison.

An additional concern regarding controls is that there is an absence of loading controls for the immunoblot assays. In Figure 5D and all immunoblot assays, there is no mention of a loading control, which is a critical control that should be included.

Some of the visualizations could be improved to help the reader understand and appropriately interpret the data presented. For instance, in Figures 3 and 4 the scale bars are different across each of the Figure's imaging panels. These should be scaled consistently for better comparison. Additionally, the red false colorization makes the printed images difficult to see. Black-and-white would be easier to see and would not subtract from the images.

An additional weakness of the paper is that the RNA-seq data is not fully investigated, and there is an absence of methods included regarding the RNA-seq differential abundance analysis (it is mentioned on L379-380 but no information is provided in the methods). As stated by the authors, 58% of differentially regulated genes belonged to the w regulon, but the other 42% of genes are not discussed, and will hopefully be a target of future investigations.

Another methodological concern in this paper is the limited details provided for the calculation of the permeabilization rate (Figure 4, L359, L662-664). It is not clear how, or if, cell density was controlled for in these experiments.

Finally, one weakness of the paper is the broad conclusions that they draw. The authors claim that the mechanism of sporulation activation is conserved across Bacilli when the authors only test one B. subtilis and one B. cereus strain. They further argue (lines 469+) that Tse1 requires a PAAR repeat for its targeting, but do not provide direct evidence for this possibility.

Reviewer #3 (Public Review):

Leander et al used deep mutational scanning to assess the effect of nearly all possible point mutations on four homologous bacterial allosteric transcription factors (aTFs). In particular, they identified mutations that abrogated the transcription factor response to a small molecule effector. The authors go on to use machine learning to determine which physicochemical properties distinguish mutations with allostery-eliminating effects from those without an effect. They report that mutations that eliminate the allosteric response to small molecules are quite variable across homologs and that global features are more predictive of which mutations will break allostery relative to local properties. Overall, the experimental strategy is well-chosen, and a comprehensive comparison of mutational sensitivity across allosteric homologs is highly important to understand how conserved (or not) the implementation of allostery is across homologs. Moreover, the idea to use machine learning to assess which features are most predictive of "allosteric hotspots" is very nice, and provides some insight into what physical properties distinguish mutations that influence allostery. The authors include some interesting results on transfer learning (evaluating whether models trained on one protein predict allostery in another), and the use of alternate sequence representations (e.g. UniRep) in their machine learning analyses. However - at least in the manuscript's present form - the paper suffers from key conceptual difficulties and a lack of rigor in data analysis that substantially limits one's confidence in the authors' interpretations. More specifically:

1) A key conceptual challenge shaping the interpretation of this work lies in the definition of allostery, and allosteric hotspot. The authors define allosteric mutations as those that abrogate the response of a given aTF to a small molecule effector (inducer). Thus, the results focus on mutations that are "allosterically dead". However, this assay would seem to miss other types of allosteric mutations: for example, mutations that enhance the allosteric response to ligand would not be captured, and neither would mutations that more subtly tune the dynamic range between uninduced ("off) and induced ("on") states (without wholesale breaking the observed allostery). Prior work has even indicated the presence of TetR mutations that reverse the activity of the effector, causing it to act as a co-repressor rather than an inducer (Scholz et al (2004) PMID: 15255892). Because the work focuses only on allosterically dead mutations, it is unclear how the outcome of the experiments would change if a broader (and in our view more complete) definition of allostery were considered.

2) The experimental determination of which mutations impacted allostery is given only a limited description in the methods, but if we understand what was done, the analysis seems to neglect both (1) important caveats due to assay specifics and (2) more general limitations of deep mutational scanning data. In particular:<br /> a. The separation in fluorescence between the uninduced and induced states (the assay dynamic range, or fold induction) varies substantially amongst the four aTF homologs. Most concerningly, the fluorescence distributions for the uninduced and induced populations of the RolR single mutant library overlap almost completely (Figure 1, supplement 1), making it unclear if the authors can truly detect meaningful variation in regulation for this homolog.<br /> b. The methods state that "variants with at least 5 reads in both the presence and absence of ligand in at least two replicates were identified as dead". However, the use of a single threshold (5 reads) to define allosterically dead mutations across all mutations in all four homologs overlooks several important factors:<br /> i. Depending on the starting number of reads for a given mutation in the population (which may differ in orders of magnitude), the observation of 5 reads in the gated non-fluorescent region might be highly significant, or not significant at all. Often this is handled by considering a relative enrichment (say in the induced vs uninduced population) rather than a flat threshold across all variants.<br /> ii. Depending on the noise in the data (as captured in the nucleotide-specific q-scores) and the number of nucleotides changed relative to the WT (anywhere between 1-3 for a given amino acid mutation) one might have more or less chance of observing five reads for a given mutation simply due to sequencing noise.<br /> iii. Depending on the shape and separation of the induced (fluorescent) and uninduced (non-fluorescent) population distributions, one might have more or less chance of observing five reads by chance in the gated non-fluorescent region. The current single threshold does not account for variation in the dynamic range of the assay across homologs.<br /> c. The authors provide a brief written description of the "weighted score" used to define allosteric hotspots (see y-axis for figure 1B), but without an equation, it is not clear what was calculated. Nonetheless, understanding this weighted score seems central to their definition of allosteric hotspots<br /> d. The authors do not provide some of the standard "controls" often used to assess deep mutational scanning data. For example, one might expect that synonymous mutations are not categorized as allosterically dead using their methods (because they should still respond to ligand) and that most nonsense mutations are also not allosterically dead (because they should no longer repress GFP under either condition). In general, it is not clear how the authors validated the assay/confirmed that it is giving the expected results.<br /> 3) In several places, the manuscript lacks important statistical analyses needed to firmly establish the authors' claims<br /> a. The authors performed three replicates of the experiment, but reproducibility across replicates and noise in the assay is not presented/discussed<br /> b. In the analysis of long-range interactions, the authors assert that "hotspot interactions are more likely to be long-range than those of non-hotspots", but this was not accompanied by a statistical test (Figure 2 - figure supplement 1)

4) Data availability and analysis transparency need improvement. The raw fastq reads do not seem to be publicly available, nor did we see access to the code used to perform the analysis. If the code is not provided, the description of the analysis in the methods section needs to be more detailed for reproducibility.

Overall, these concerns with fundamental aspects of the data analysis make it challenging to assess the reproducibility of the results, the fidelity of the assay (in reporting allosterically dead mutations), and the extent to which the data robustly support the authors' claims.

Reviewer #3 (Public Review):

The authors assess response to ocean acidification with three populations of mussels encompassing two species: Mytilus trossulus from the intertidal and subtidal and M. galloprovincialis from a subtidal aquaculture farm. All three species received an ambient of low pH treatment prior to a freezing treatment. The authors find species differences in freeze tolerance in mussels, with intertidal M. galloprovincialis showing the least freeze tolerance. The authors go a step further and do a comprehensive assessment of the metabolic capacity and molecular components with analyses of amino acids, fatty acids, and osmolytes and anaerobic byproducts.

The authors hypothesized metabolic changes due to OA and cold temperatures, yet they demonstrated a significant amount of stasis with high similarity among species at the molecular level. The fatty acids in the intertidal M trossulus, the most freeze tolerant, did not change. Further, there is little explanation of molecular/metabolic changes that could explain their results. Because of this somewhat unexpected lack of signal of these stressors, I would like to see an enhanced explanation of animal homeostasis. The authors mention previous results relating to heat stress, and I thought it would be beneficial to discuss how the lack of a molecular response to freezing is related to the strong responses seen in heat stress.

The idea that species in fluctuating environments (here, the intertidal) might respond differently to those in constant environments (here, the subtidal) has been explored in multiple systems. These general concepts could be elaborated on more in the paper to increase the connection to other studies.

Reviewer #3 (Public Review):

This manuscript presents and analyzes a novel calcium-dependent model of synaptic plasticity combining both presynaptic and postsynaptic mechanisms, with the goal of reproducing a very broad set of available experimental studies of the induction of long-term potentiation (LTP) vs. long-term depression (LTD) in a single excitatory mammalian synapse in the hippocampus. The stated objective is to develop a model that is more comprehensive than the often-used simplified phenomenological models, but at the same time to avoid biochemical modeling of the complex molecular pathways involved in LTP and LTD, retaining only its most critical elements. The key part of this approach is the proposed "geometric readout" principle, which allows to predict the induction of LTP vs. LTD by examining the concentration time course of the two enzymes known to be critical for this process, namely (1) the Ca2+/calmodulin-bound calcineurin phosphatase (CaN), and (2) the Ca2+/calmodulin-bound protein kinase (CaMKII). This "geometric readout" approach bypasses the modeling of downstream pathways, implicitly assuming that no further biochemical information is required to determine whether LTP or LTD (or no synaptic change) will arise from a given stimulation protocol. Therefore, it is assumed that the modeling of downstream biochemical targets of CaN and CaMKII can be avoided without sacrificing the predictive power of the model. Finally, the authors propose a simplified phenomenological Markov chain model to show that such "geometric readout" can be implemented mechanistically and dynamically, at least in principle.

Importantly, the presented model has fully stochastic elements, including stochastic gating of all channels, stochastic neurotransmitter release and stochastic implementation of all biochemical reactions, which allows to address the important question of the effect of intrinsic and external noise on the induction of LTP and LTD, which is studied in detail in this manuscript.

Mathematically, this modeling approach resembles a continuous stochastic version of the "liquid computing" / "reservoir computing" approach: in this case the "hidden layer", or the reservoir, consists of the CaMKII and CaM concentration variables. In this approach, the parameters determining the dynamics of these intermediate ("hidden") variables are kept fixed (here, they are constrained by known biophysical studies), while the "readout" parameters are being trained to predict a target set of experimental observations.

Strengths:

1) This modeling effort is very ambitious in trying to match an extremely broad array of experimental studies of LTP/LTD induction, including the effect of several different pre- and post-synaptic spike sequence protocols, the effect of stimulation frequency, the sensitivity to extracellular Ca2+ and Mg2+ concentrations and temperature, the dependence of LTP/LTD induction on developmental state and age, and its noise dependence. The model is shown to match this large set of data quite well, in most cases.

2) The choice for stochastic implementation of all parts of the model allows to fully explore the effects of intrinsic and extrinsic noise on the induction of LTP/LTD. This is very important and commendable, since regular noise-less spike firing induction protocols are not very realistic, and not every relevant physiologically.

3) The modeling of the main players in the biochemical pathways involved in LTP/LTD, namely CaMKII and CaN, aims at sufficient biological realism, and as noted above, is fully stochastic, while other elements in the process are modeled phenomenologically to simplify the model and reveal more clearly the main mechanism underlying the LTP/LTD decision switch.

4) There are several experimentally verifiable predictions that are proposed based on an in-depth analysis of the model behavior.

Weaknesses:

1) The stated explicit goal of this work is the construction of a model with an intermediate level of detail, as compared to simplified "one-dimensional" calcium-based phenomenological models on the one hand, and comprehensive biochemical pathway models on the other hand. However, the presented model comes across as extremely detailed nonetheless. Moreover, some of these details appear to be avoidable and not critical to this work. For instance, the treatment of presynaptic neurotransmitter release is both overly detailed and not sufficiently realistic: namely, the extracellular Ca2+ concentration directly affects vesicle release probability but has no effect on the presynaptic calcium concentration. I believe that the number of parameters and the complexity in the presynaptic model could be reduced without affecting the key features and findings of this work.

2) The main hypotheses and assumptions underlying this work need to be stated more explicitly, to clarify the main conclusions and goals of this modeling work. For instance, following much prior work, the presented model assumes that a compartment-based (not spatially-resolved) model of calcium-triggered processes is sufficient to reproduce all known properties of LTP and LTD induction and that neither spatially-resolved elements nor calcium-independent processes are required to predict the observed synaptic change. This could be stated more explicitly. It could also be clarified that the principal assumption underlying the proposed "geometric readout" mechanisms is that all information determining the induction of LTP vs. LTP is contained in the time-dependent spine-averaged Ca2+/calmodulin-bound CaN and CaMKII concentrations, and that no extra elements are required. Further, since both CaN and CaMKII concentrations are uniquely determined by the time course of postsynaptic Ca2+ concentration, the model implicitly assumes that the LTP/LTD induction depends solely on spine-averaged Ca2+ concentration time course, as in many prior simplified models. This should be stated explicitly to clarify the nature of the presented model.

3) In the Discussion, the authors appear to be very careful in framing their work as a conceptual new approach in modeling STD/STP, rather than a final definitive model: for instance, they explicitly discuss the possibility of extending the "geometric readout" approach to more than two time-dependent variables, and comment on the potential non-uniqueness of key model parameters. However, this makes it hard to judge whether the presented concrete predictions on LTP/LTD induction are simply intended as illustrations of the presented approach, or whether the authors strongly expect these predictions to hold. The level of confidence in the concrete model predictions should be clarified in the Discussion. If this confidence level is low, that would call into question the very goal of such a modeling approach.

4) The authors presented a simplified mechanistic dynamical Markov chain process to prove that the "geometric readout" step is implementable as a dynamical process, at least in principle. However, a more realistic biochemical implementation of the proposed "region indicator" variables may be complex and not guaranteed to be robust to noise. While the authors acknowledge and touch upon some of these issues in their discussion, it is important that the authors will prove in future work that the "geometric readout" is implementable as a biochemical reaction network. Barring such implementation, one must be extra careful when claiming advantages of this approach as compared to modeling work that attempts to reconstruct the entire biochemical pathways of LTP/LTD induction.

Reviewer #3 (Public Review):

Accumulating evidence supports the expression of anterior pituitary glycoprotein hormone family of receptors, namely FSHR, TSHR, and luteinizing hormone/human chorionic gonadotropin receptor (LHCGR), in various brain regions, and their function in regulating peripheral actions. However, the link between the stimulation of these receptors in the brain and the regulation of peripheral physiological processes remains poorly understood. Using RNAscope, a cutting-edge technology that detects single RNA transcripts, the authors created a comprehensive neuroanatomical atlas of glycoprotein hormone receptors in the mouse brain. Overall, these are a very comprehensive and well-done set of studies that offer new insights into the distributed brain network of anterior pituitary hormone receptors. The atlas provides an important resource for scientists to explore the link between the stimulation or inactivation of these receptors on somatic function.

Reviewer #3 (Public Review):

The authors combine outcomes data from patients hospitalised with COVID-19 across 30 countries to investigate differences in likelihood of death from the Omicron variant vs pre-Omicron variants. Data are from the ISARC COVID-19 database; variant status is inferred from country-specific GISAID data. The principal finding is a 36% reduced risk of 14-day death in the Omicron period (OR 0.64 (0.59 - 0.69)) compared with the pre-Omicron period, after multiple adjustment.

The strengths of this paper are the large N and large number of participating countries from different regions, and also the careful and thorough analytical approaches. The main findings are stress-tested through a range of sensitivity analyses using different variant-dominance thresholds and statistical approaches and found to be robust. The figures are clear, well-chosen and easily interpretable.

The principal weaknesses, as acknowledged in the discussion, are the imbalance in the data sources (96.6% of the observations came from GBR or SA), and the lack of fidelity of data on vaccination (vaccination status is limited to a binary 'one or more vaccinations received Y/N' variable). This latter means that conclusions about the innate severity of Omicron vs pre-Omicron variants cannot be drawn.

Nonetheless the findings represent a useful contribution to the literature on the severity of COVID-19 variants, and the approach establishes a template for rapid international collaboration, using GISAID data to infer variant status, that will be useful for formulating policy in response to new variants in the future.

Reviewer #3 (Public Review):

In this study, Dai and colleagues used genetic models combined to electrophysiological recordings and behavior as well as immunostaining and immunoblotting to investigate the role of trans-synaptic complexes involving presynaptic neurexins and cerebellins in shaping the function of central synapses. The study extends previous findings from the same authors as well as other groups showing an important role of these complexes in regulating the function of central synapses. Here, the authors sought to achieve two main objectives: (1) investigating whether their previous findings obtained at mature CA1-> subiculum synapses (Aoto et al., 2013; Dai et al., Neuron 2019; Dai et al., Nature 2021) extend to different synapse subtypes in the subiculum as well as to other central synapses including cortical and cerebellar synapses and (2) investigating whether Nrx-Cbln-GluD trans-synaptic complexes play a role in synapse formation as previously proposed by other groups.

Overall, the study provides interesting and solid electrophysiological data showing that different Nrxns and Cblns assemble trans-synaptic complexes that differently regulate AMPAR and NMDA-mediated synaptic transmission across distinct synaptic circuits (most likely through binding to postsynaptic GluD receptors).

However, the study has several important weaknesses:

(1) The novelty of the findings appears limited. Indeed, previous studies from the same authors with similar experimental paradigms and readouts already demonstrated the role of Nrxn-Cbln-GluD complexes in regulating AMPARs versus NMDARs in mature neurons (Aoto et al., Cell 2013; Dai et al., Neuron 2019; Dai et al., Nature 2021). Moreover, the absence of role of Cblns and GluD receptors in synapse formation was already suggested in previous studies from the same authors (Seigneur and Sudhof, J Neurosci 2018; Seigneur et al., PNAS 2018; Dai et al., Nature 2021).

(2) The conclusion made by the authors that the Nrxn-Cbln-GluD trans-synaptic complexes do not play a role in synapse formation/development is not sufficiently supported by their data, while previous studies suggest the opposite. Actually, this conclusion is essentially based on the two following measurements taken as a 'proxy' for synapse density: (1) 'the average vGluT1 intensity calculated from the entire area of subiculum' and (2) the 'synaptic proteins levels' assessed by immunoblotting. None of these measurements (only performed in the subiculum) allow to precisely assess synapse density on the neurons of interest. While the average vGluT1 intensity over large fields of view does not directly reflect the density of synapses and does not take into account the postsynaptic compartment, the immunoblotting data only reflects the overall expression of synaptic proteins without discriminating between intracellular, surface and synaptic pools and between cell types. In the subiculum from Cbln1+2 KO mice, the authors performed mEPSCs recordings and found an increase in frequency. However, this increase may reflect the unsilencing and/or potentiation of AMPAR-EPSCs above the detection threshold, irrespectively of the actual synapse number. Finally, the decrease in NMDAR-EPSCs is not discussed by the authors while it could actually reflect a decrease in synapse number.

(3) The authors do not provide sufficient data in order to interpret the increase in AMPAR-EPSCs and decrease in NMDAR-EPSCs amplitudes. Are the changes in AMPARs and NMDARs occurring at pre-existing synapses or do they result from alterations in the number of physical synapses and/or active synapses (see point#2)? In particular, the increase in AMPAR/NMDAR ratio accompanied by the increase in mEPSCs frequency might be well explained by the unsilencing of some synapses and/or by the fact that the available pool of AMPARs is distributed over a smaller number of synapses, resulting in higher quantal size. These effects could explain the blockade of LTP, i.e., through an occlusion mechanism.

(4) The authors did not demonstrate (or did not cite relevant studies) that the deletion of Cbln1 and/or Cbln2 does not affect the expression of the remaining Cblns isoforms (Cbln2 and/or Cbln4) or Nrxns1/3 and GluD1/2. This verification is important to preclude the emergence of any compensatory effect.

Reviewer #3 (Public Review):

This manuscript details a methodological approach for the characterisation of ligands based on nuclear receptor conformational ensembles. Using ancestral steroid receptor AncSR2 and atomistic MD simulations, the authors generated ensembles of the WT and mutants of the conserved Methionine residue at position 75. The mutation, as well as the ligands (3-ketosteroid hormones and estradiol), shifted the populations into distinct conformational clusters. These clusters were then well correlated to ligand activation, making use of the cell-based luciferase assay. Next, the binding affinities of the ligands to the WT, M75L, and M75I were probed by fluorescence polarization assay to understand the extraordinary activation of M75L by estradiol (inactive ligand). The decreased binding affinity of M25L for the ligands was further investigated using differential hydrogen-deuterium exchange (HDX). The deprotection pattern observed for the M25L mutant compared to WT and decreased binding affinity of the ligands for this mutant led to the conclusion that this specific mutation shifts the ensemble conformation to a ligand-bound state.

This approach can be useful for the prediction of ligand responses, understanding underlying mechanisms, and their detailed characterisation based on the population shifts of the nuclear receptor conformational ensembles. It is commendable that the results obtained from computational techniques are well supported by a range of biochemical and biophysical techniques. Logical correlation is established between the results and light is shed on the underlying molecular mechanism through in-depth discussion. The control of the mutants based on secondary structure, melting temperature, and purity through SDS-PAGE is appreciable. The techniques are well chosen and appropriate to reach the conclusions.

Reviewer #3 (Public Review):

The goal of Barendregt et al. is to extend the normative model of decision thresholds to changing environments. The immediate precursors of this work are Drugowitsch et al (2012) and Malhotra et al (2018), both of which derive optimal decision boundaries using dynamic programming. However, both those papers assumed a stationary environment. Barendregt et al. relax this assumption and show that non-stationary environments predict some very strange decision boundaries - decision boundaries can be non-monotonic or infinite, depending on the change in the environment. They consider two types of changes: change in reward and change in signal-to-noise ratio. Decision boundaries for a change in reward are particularly intriguing. To show empirical support for their theory, Barendregt et al. compare decision boundaries derived from their task with the Urgency Gating Model (UGM) and show their model shows a better fit to the data, at least under some conditions.

Here are my thoughts on the paper:

1. The theory of the paper is elegantly developed and clearly presented. While I can't be certain that there are no errors in the theory or simulation, the results presented based on this theory make intuitive sense.

2. The authors have developed the theory diligently and explored different predictions. They not only present some example thresholds for a few selected conditions but explore the space of possible types of thresholds (Figure 2C & 3C). They go further and explore the benefits of adopting this theory over UGM and constant thresholds (Figure 3) and they also show some evidence that participant behaviour is more in line with their model than UGM in a previous study (the "Tokens task").

3a. As much as I appreciate the authors' efforts (and the elegance of the theory) it seems to me that the notion of 'changing environments' explored by authors is quite limited. The decision thresholds are derived from a world in which an observer makes a (large) sequence of decisions and every decision has the exact same form of change. For example, in one of the reward-change tasks, the reward switches from low to high during every trial. In other words, the environment changes repeatedly in every trial (and in the exact same manner). There may be some circumstances in the natural world where such a setup is justified - the authors identify one where change is a function of the time of the day. But in many circumstances, the environment changes at an entirely different timescale - over the course of a sequence of trials. For example, a forging animal may make a sequence of decisions in a scarce environment, followed by another sequence of decisions in a plentiful environment. That is the statistics of the environment change over several trials. As far as I can see, the assumptions made by the authors mean that the results of the model cannot be applied to changes that occur at this timescale.

3b. One particular area where the integrate-to-threshold models have been particularly successful is perceptual decision-making. For example, in motion perception (Shadlen & Newsome, 1996) or brightness perception (Ratcliff, 2003). This is where we have evidence of something like an integration signal in the cortex. However, these decisions are typically really fast, occurring at sub-second intervals. Another area is lexical decision tasks (e.g. Wagenmakers et al, 2008), where mean reaction times are <1s, frequently a lot faster. It is difficult to imagine that the model developed by the authors has much bearing on these types of decisions - firstly because it is unlikely that the reward structure in natural environments fluctuates at these timescales and secondly because participants are unlikely to pick up on such changes over the course of a small sequence of trials.

3c. This does not mean that the model developed by Barendregt et al. is of no value. There will be situations (like the Tokens task) where the model will be the correct normative model. But these limitations are important to clarify for researchers in the field.

4. The weakest part of the paper is its empirical support. The authors apply their model to the Tokens task. First of all, this is by no means the modal task used to study decision-making. The model developed by the authors simply does not apply to most perceptual decision-making tasks (see 3b above). So the ideal case would have been to design a task based on predictions of the model. For example, there is a clear prediction about RTs in Figure 4D, but this has never been tested. (My own view is that this prediction will only bear out under some scenarios - e.g. when decision-making is slow - but not during others). There are also some highly unusual boundaries predicted by the model - e.g. Figure 2i, 2ii, 2iv. I really doubt if participants ever adopt a boundary like this. The authors could have tested this, but haven't. I don't want to ask the authors to design and run these studies at this stage (it seems like a lot of work) but, at the very least, it would be good if the authors discussed whether they predict these highly idiosyncratic boundaries to bear out in empirical data. For example, an "infinite" threshold (Figure 2i, 2ii) means that participants never make a decision in this interval, even if they receive highly informative cues during this interval. Or do the authors believe that participants adopt some heuristic boundaries that approximate these normative boundaries? Currently, the authors seem to be arguing against heuristic models. Or perhaps they have a different heuristic model in mind? It would be good to know.

5. One neat aspect of the paper is showing that there are some participants who show non-monotonic boundaries in the Tokens task. This task was specifically designed to justify the UGM. But the authors show that their model fits some participants better than UGM itself. To the best of my knowledge, this is the first demonstration of the fact that participants can show non-monotonic decision boundaries.

7. Some of the write-ups need to make better contact with existing literature on boundary shapes. Here are some studies that come to mind:<br /> 7a. Some early models to predict dynamic decision boundaries were proposed by Busemeyer & Rapoport (1988) and Rapoport & Burkheimer (1971) in the context of a deferred decision-making task.<br /> 7b. One of the earliest models to use dynamic programming to predict non-constant decision boundaries was Frazier & Yu (2007). Indeed some boundaries predicted by the authors (e.g. Fig 2v) are very similar to boundaries predicted by this model. In fact, the switch from high to low reward used to propose boundaries in Fig 2v can be seen as a "softer" version of the deadline task in Frazier & Yu (2007).<br /> 7c. Another early observation that time-varying boundaries can account for empirical data was made by Ditterich (2006). Seems highly relevant to the authors' predictions, but is not cited.<br /> 7d. The authors seem to imply that their results are the first results showing non-monotonic thresholds. This is not true. See, for example, Malhotra et al. (2018). What is novel here is the specific shape of these non-monotonic boundaries.

8. One of the more realistic scenarios is presented in Fig 2-Figure supplement 3, where reward doesn't switch at a fixed time, but uses a Markov process. But the authors do not provide enough details of the task or the results. Is m_R = R_H / R_L? Is it the dark line that corresponds to m_R=\inf (as indicated by legend) or the dotted line (as indicated by caption)? For what value of drift are these thresholds derived?

9. Figure 4F: It is not clear to me why UGM in 0 noise condition have RTs aligned to the time reward increases from R1 to R2. Surely, this model does not take RR into account to compute the thresholds, does it? In fact, looking at Figure 4B, Supplement 1, the thresholds are always highest at t=0. Perhaps the authors can clarify.

Reviewer #3 (Public Review):

In this manuscript, Kuwabara and colleagues use genetic ablation to reduce the number of fibroblasts resident to the heart. At baseline, the authors observe that fibroblast numbers stay proportionally low after ablation, but with very minimal effects to the structure or composition of the extracellular matrix. Fibroblast ablation prior to myocardial infarction is shown to be beneficial to cardiac function without affecting relative abundance of scar tissue, whereas in an Ang/PE model of fibrosis collagen deposition is impaired and systolic function is preserved.

Reviewer #3 (Public Review):

In this paper, Proux-Giraldeaux et al. develop evolutionary simulations to study how size control can emerge. In the first part of the paper, the authors initiate cell cycle simulations with a simple network that does not allow cell size sensing and ask what molecular networks can lead to size control after evolution. Results show that a wide range of network types allows size control, some of which are comparable to experimentally identified networks such as the dilution inhibitor model in budding yeast. In the second part of the paper, the authors use their framework to ask how the structure of the cell cycle, including the duration of G1 vs. S/G2/M and the form of size control in each of these phases (i.e. 'sizer' or 'adder'), affects the overall size control. While this is a very important question and the authors bring comprehensive and interesting answers, it is less clear that framing the findings in the context of evolution is meaningful. Indeed, the solutions for how the combination of strength of size control, noise levels, and respective duration of the phases can be found analytically/with simulations that are not 'evolving' the cell cycle structure. Additionally, the finding that a sizer in G1 can lead to an overall adder if it is followed by a timer in S/G2/M is only true if a significant amount of noise is added during the timer phase. At present, this finding is discussed as a result of 'evolution' which is confusing and the dependency of this conclusion on the level of noise during S/G2 does not appear very clearly.

With more cautiously formulated conclusions and a better discussion of already established theoretical and experimental work, this paper will become more accessible to experimentalists and will be a very valuable contribution to the field of cell size control.

Major suggestions:

1) Fig 4-5. While the use of the evolution simulation seems interesting to identify which underlying network(s) can result in size control, the use of the same framework to compare the result of sizer+timer vs. timer+sizer is less easy to interpret. Previous analytical/simulation approaches have explored how noise & duration of the timer phase can alter the 'sizer' or 'adder' signature (see doi.org/10.1016/j.celrep.2020.107992, doi.org/10.3389/fcell.2017.00092, for example) and what evolutionary simulations add to this question is unclear.<br /> - What is the authors' interpretation of why the optimization of Pareto vs. number of divisions yield different size control results (Fig. 4A)? Is it possible that these different fitness parameters allow for the evolution of different levels of noise/duration of the timer phase?<br /> - In the conclusion: 'G1 control is more conducive to the evolution of adders, while G2 control is more conducive to sizers', do the authors really believe that this is an evolutionary acquired trait, or are their observations instead the natural consequence of having a noise-adding phase (timer + multiplicative noise) after a phase with size control?<br /> - A perfect sizer in G1, followed by a timer (with exponential growth) in S/G2/M would simply give an overall 'noisy sizer' (i.e. the slope of final volume vs. initial volume would still be 0 but with some variability around the slope). Only beyond a certain level of noise added in S/G2/M, would the sizer signature be lost. Would it be possible for the authors to perform simulations with different levels of noise (on the timer in S/G2) to help understand this conclusion better? This conclusion could be one of the most valuable to experimentalists studying different organisms.

2) Some aspects of the mathematical formalism were unclear:<br /> - Working with the hypothesis that growth is exponential and at a constant rate is reasonable. However, the description of the scenario where growth modulation contributes to size homeostasis is incorrect. E.g. the statement 'cells further from the optimum size grow slower' is not accurate. If size control occurs via growth regulation, what is expected is a negative correlation between size and growth rate (big cells grow slow, small cells grow fast).<br /> - 'the quantity I is produced with a rate proportional to volume, degraded at a constant rate, diluted by cell growth': why is I diluted? Concentration should be constant if I increases at the same rate as volume. 'the quantity of I does not initially depend in any way on the volume'. Does the quantity of I not increase with volume (since concentration is constant)?

3) Fig. 2, The rescaling of the variables to tau and Veq was difficult to understand. Fig. 2A: If T_S/G2/M is at ~0.5 of the doubling time tau, how relevant is it to look at the behaviour of T_(Vc) for values of T_(Vc)/tau above 0.5 (and beyond 1)? Fig 2B: for which value of T(Vc) is the prediction made?

4) Discussion:<br /> - Including a discussion of previous theoretical work that explored the consequences of varying the relative duration of the timer and sizer phases would be valuable.<br /> - A reason commonly evoked to explain why cells might show sizer vs. adder behaviour is the role of the growth mode: S. pombe is a sizer but is thought to grow linearly, E. coli behaves like a sizer when it grows slower than usual (see Walden et al. 2015). It would be helpful to mention this when discussing S. pombe and remind the reader that the findings of this paper are limited to exponential growth mode.<br /> - The paper seems to be focusing on the noise of the size control mechanism (i.e. probability of transitioning through G1/S based on levels if I) but does not address the question of other sources of noise (i.e. asymmetry at division). What do the authors think about the role of such sources of noise as selective pressure on size control mechanisms evolution?

Reviewer #3 (Public Review):

This paper addresses whether the sequences of neural activity that are believed to underlie song production in songbirds emerge as a result of experience-dependent tutoring or rather preceded tutored song production. The primary approach relies on calcium imaging in HVC in untutored zebra finches. The key results include the detection of neural sequences in untutored birds, and that after late tutoring the sequences associated with the tutored song can be partially attributed to pre-existing sequences. This is a short paper that addresses an important question and seems to provide significant support for the notion that neural sequences in HVC emerge independent of tutored song, and that rather than being created by tutoring, learning exploits the presence of pre-existing sequences for song generation. The results of the paper rely in large part on the extraction of neural sequences in an unsupervised fashion, while the method used does require some assumptions (such as sequence length) the conclusions seem well supported by the data.

Reviewer #3 (Public Review):

Truman et al. investigated the contribution and remodeling of individual larval neurons that provide input and output to the Drosophila mushroom body through metamorphosis. Hereto, they used a collection of split-GAL4 lines targeting specific larval mushroom body input and output neurons, in combination with a conditional flip-switch and imaging, to follow the fates of these cells.

Interestingly, most of these larval neurons survive metamorphosis and persist in the adult brain and only a small percentage of neurons die. The authors also elegantly show that a substantial number of neurons actually trans-differentiate and exert a different role in the larval brain, compared to their final adult functionality (similar to their role in hemimetabolous insects). This process is relatively understudied in neuroscience and of great interest.

Using the ventral nerve cord as a proxy, the authors claim that the larval state of the neuron would be their derived state, while their adult identity is ancestral. While the authors did not show this directly for the mushroom body neurons under study, it is a very compelling hypothesis. However, writing the manuscript from this perspective and not from the perspective of the neuron (which first goes through a larval state, metamorphosis, and finally adult state), results in confusing language and I would suggest the authors adjust the manuscript to the 'lifeline' of the neuron.

In general, this manuscript does not explain how the larval brain has evolved as the title suggests but instead describes how the larval brain is remodeled during metamorphosis. It thus generates perspectives on the evolution of metamorphosis, rather than the larval state. Additionally, this manuscript would benefit from major rearrangements in both text and figures for the story to be better comprehended.

The introduction is very focused on the temporal patterning of the insect nervous system, while none of the data collected incorporate this temporal code. Temporal patterning comes back in the discussion but is purely speculative.

Furthermore, the second part of the introduction describes one strategy for remodeling and why that strategy is not likely but does not present an alternative hypothesis. The first section of the results might serve as a better introduction to the paper instead, as it places the results of the paper better and concludes with the main findings. The accompanying Figure 1 would also benefit from a schematic overview of the larval and adult mushroom bodies as presented in Fig. 2A (left).

In the second results section, the authors show the post-metamorphic fates of mushroom body input and output neurons and introduce the concept of trans-differentiation. Readers might benefit from a short explanation of this process. I also encourage the authors to revisit this part of the text since it gives the impression that the neurons themselves undergo active migration (instead of axon remodeling).

The discussion starts with a very comprehensive overview of the different strategies that neurons could use during metamorphosis (here too, re-writing the text from the neurons' perspective would increase the reflection of what actually happens to them).

The discussion covers multiple topics concerning trans-differentiation, metamorphosis, memory, and evolution and is often disconnected from the results. It could be significantly shortened to discuss the results of the paper and place them in current literature. Generally, the figures supporting the discussion are hard to comprehend and often do not reflect what the text is saying they are showing.

Reviewer #3 (Public Review):

The manuscript by Huelsz-Prince et al. studies the fate of intestinal crypt cells in organoids and, to some extent, in vivo, through a combination of live cell tracking (in organoids), static in vivo lineage tracing, and mathematical modelling. They find through live imaging that the vast majority of divisions in the crypt are symmetric with respect to the proliferative potential of daughter cells (something that has previously been shown indirectly). Furthermore, they show that fate outcomes depend on the distance of the mother cell from Paneth cells, but not on the position of daughter cells relative to the latter, and the fluctuations of numbers of proliferating cells are much less than would be expected from a naive cell fate model. They suggest a two-compartment model where one compartment represents the niche with a high propensity for divisions with two proliferating daughter cells and another compartment with a high propensity of divisions with two non-proliferating daughter cells, which is consistent with the data and the observed small fluctuations.

The work is very interesting and solid and establishes its main claims through a variety of measurements supported by mathematical modelling. The methodology is strong, using cutting-edge imaging, statistical and image analysis, and mathematical modelling. The methods firmly establish that cell divisions in the crypt are predominantly symmetric and that the propensity towards proliferating divisions increases with the proximity of the mother cell (but not of the daughter cells) to Paneth cells, a mechanism that maintains homeostatic control. Their theoretical finding that such a mechanism minimises fluctuations in cell numbers is nice but has already been reported in the authors' previous work (Kok et al. bioRxiv 2022). My only concern is that while their two-compartment model is consistent with the data, other models cannot be excluded. Most models with symmetric divisions and contact inhibition, or niche crowding control (negative feedback), where cells are expelled from a crowded niche via a differentiation rate that increases with cell numbers, would lead to similar results. The presented model can rightly be seen as a simplified paradigmatic representative of such model types, and it is a valid approach to use a simplified model to demonstrate qualitative features of this mechanism but to describe the real mechanism one should not take the two-compartment aspect too literally. Instead, the direct measurements presented in this work, showing that the propensity towards divisions with non-proliferating daughters increases with the distance of mother cells from Paneth cells, show that a model where the proliferative potential decreases continuously rather than abruptly is probably better suited to describe that mechanism.

Apart from that, the findings are very solid and certainly of high interest to any developmental biologist working on adult stem cell fate. While here the authors only establish this mechanism for intestinal cells, it can be reasonably suggested that a similar mechanism of homeostatic control is also present in other tissues, as the prevalence of symmetric divisions has been shown for many mammalian tissues.

Reviewer #3 (Public Review):

This study highlights the functional consequences of combined genomic losses of CIC and ERF which results in the activation of ETV1, in the absence of the canonical fusion event involving TMPRSS2 in a subset of prostate cancer. ETV1 is an oncogenic driver of cell growth and metastatic behaviour in many cancer types including prostate cancer. The experiments performed provided tantalizing evidence on the biological and functional consequences of combined losses of CIC and ERF and appeared to support the findings of the mined publicly available cancer genomic datasets.

The manuscript could be improved by providing evidence of proteomic interactions between CIC and ERF proteins in the form of immune-precipitation and Western protein blots. The authors had provided predominantly genomic, transcriptomic, and functional data. In most parts, the manuscript is logical and thorough and leveraged available genomic data. This is followed by genomic-functional experimentations. Given the postulate of co-operativity between CIC and ERF, it would be logical to investigate their potential proteomic interactions.

Reviewer #3 (Public Review):

The authors study mammalian heart regeneration and study the connection between Yap and β-adrenergic receptor (β-AR) blockade. Interestingly, metoprolol robustly enhanced cardiomyocyte proliferation and promoted cardiac regeneration post myocardial infarction, resulting in reduced scar formation and improved cardiac function. The conclusion was also supported by genetic deletion of Gnas. CMs had an immature cell state with enhanced activity of Hippo-effector YAP. They also find that increased YAP activity is modulated by RhoA.

Overall, the data are supportive of the conclusions and this may provide new insight into treating heart disease. The final mechanisms connecting Hippo signaling to Rho activity remain incompletely defined.

Reviewer #3 (Public Review):

This study utilizes 46 species of Drosophila and 4 closely related species to try and determine the relative role of specific hydrocarbons on desiccation resistance. The use of many species of Drosophila that have variations in hydrocarbon profiles and variations in natural desiccation resistances allowed the researchers to draw conclusions about the relative role of specific hydrocarbons contributing to preventing water loss through the cuticle. By using a statistical package they were able to conclude that methyl-branched hydrocarbons are the most important in those species that were more desiccation resistant. This is not surprising since a previous study has shown that 2 methyl-branched hydrocarbons have the highest melting temperatures. In addition, it seems that desiccation resistance also involves other factors since some species that had lower desiccation rates had similar amounts of methyl branched hydrocarbons. It is also difficult to extrapolate to other insects that have a variety of lipids on their cuticular surface. Probably most insects will have hydrocarbons but some have a variety of other lipids on the cuticular surface that will contribute to preventing desiccation. The use of Drosophila species in this study is fortuitous because apparently only hydrocarbons are found on the cuticular surface.

Reviewer #3 (Public Review):

In the study "Spatiotemporal properties of glutamate input support direction selectivity in the dendrites of retinal starburst amacrine cells", Srivastava, deRosenroll, and colleagues study the role of excitatory inputs in generating direction selectivity in the mouse retina. Computational and anatomical studies have suggested that the "space-time-wiring" model contributes to direction-selective responses in the mammalian retina. This model relies on temporally distinct excitatory inputs that are offset in space, thereby yielding stronger responses for motion in one versus the other direction. Conceptually, this is similar to the Reichardt detector of motion detection proposed many decades ago. So far, however, there is little functional evidence for the implementation of the space-time-wiring model.

Here, Srivastava, deRosenroll and colleagues use local glutamate imaging in the ex-vivo mouse retina combined with biophysical modeling to test whether temporally distinct and spatially offset excitatory inputs might generate direction-selective responses in starburst amacrine cells (SACs). Consistent with the space-time-wiring model, they find that glutamatergic inputs at proximal SAC dendrites are more sustained than inputs at distal dendrites. This finding was consistent across different sizes of stationary, flashed stimuli. They further linked the sustained input component to the genetically identified type 7 bipolar cell and showed that the difference in temporal responses across proximal and distal inputs was independent of inhibition, but rather relied on excitatory interactions. By estimating vesicle release rates and building a simple biophysical model, the authors suggest that next to already established mechanisms like asymmetric inhibition, excitatory inputs with distinct kinetics contribute to direction-selective responses in SACs for slow and relatively large stimuli.

In general, this study is well-written, the data is clearly presented and the conclusion that (i) the temporal kinetics of excitatory inputs varies along SAC dendrites and that (ii) this might then contribute to direction selectivity is supported by the data. The study addresses the important question of how excitation contributes to the generation of direction-selective responses. There have been several other studies published on this topic recently, and I believe that the results will be of great interest to the visual neuroscience community.

However, the authors should address the following concerns:<br /> - They should demonstrate that differences in response kinetics between proximal and distal dendrites are unrelated to differences in signal-to-noise ratio.<br /> - To demonstrate consistency across recordings/mice, the authors should indicate data points from different recordings (e.g. Fig. 2C).<br /> - The authors mention in the introduction that the space-time-wiring model is conceptually similar to other correlation-type motion detectors that have been experimentally verified in different species. It would be great to expand on the similarity and differences of the different mechanisms in the Discussion, especially focusing on Drosophila where experimental evidence at the synaptic level exists.<br /> - The authors use stationary spot stimuli of different sizes to characterize the response kinetics of excitatory inputs to SACs. I suggest the authors add an explanation for choosing only stationary stimuli for studying the role of excitatory inputs in direction selectivity/motion processing. In addition, the authors use simulated moving edges to stimulate the model bipolar cells. They should provide details about the size of the stimulus and the rationale behind using this size, given their previous results.<br /> - Using the biophysical model, the authors show that converting sustained bipolar cell inputs to transient ones reduces direction selectivity in SACs. I suggest the authors also do the opposite manipulation/flip the proximal and distal inputs or provide a rationale why they performed this specific manipulation.<br /> - In each figure, the authors should note whether traces show single trial responses or mean across how many trials. If the mean is presented (e.g. Suppl. Fig. 2a), the authors should include a measure of variability - either show single ROIs in addition and/or add an s.d. shading to the mean traces.

Reviewer #3 (Public Review):

In invertebrates, learning-dependent plasticity was reported to take place predominantly in presynaptic neurons. In Drosophila appetitive olfactory learning, cholinergic synapses between presynaptic Kenyon cells and postsynaptic MBONs undergo behaviourally relevant associative plasticity, and it was shown to reside largely in Kenyon cell output sites. This study provided several lines of evidence for postsynaptic plasticity in MBONs. The authors nicely showed the requirement of Kenyon cell output during training, strongly suggesting that behaviourally relevant associative plasticity also resides downstream of Kenyon cell output. This is further supported by impaired appetitive memory by downregulating nAChR subunits (a2, a5) and scaffold protein Dlg in specific MBONs. Live imaging experiments demonstrated that the learning-dependent depression in M4-MBON was reduced upon knocking down the a2 nAChR subunit. Using in-vivo FRAP experiments, the authors showed recovery rates of nAChR-a2::GFP were altered by the co-application of olfactory stimulation and DA. All these lines of evidence point to the significance of nAChR subunits in MBONs for postsynaptic plasticity.

On the technical side, this study achieved a very high standard, such as the measurement of low-expressed receptor mobility by in-vivo FRAP. The authors conducted a wide array of experiments for collecting data supporting postsynaptic mechanisms. The downside of this multitude is somewhat compromised coherence. To give an example, the authors duplicated many behaviour and imaging experiments in different MBONs for non-associative learning (Fig. 7 and 8), which is primarily out of the scope of this paper (cf. title).

Reviewer #3 (Public Review):

The manuscript by Krshnan et al. reports a cellular mechanism akin to the endoplasmic reticulum-associated degradation (ERAD) that degrades SUN2, a nuclear inner membrane protein. The authors previously identified the Asi ubiquitin ligase complex that mediates the degradation of inner nuclear membrane proteins in budding yeast. In this manuscript, they identified the SCF β TrCP, and SCF as another ligase that regulates the ubiquitination and degradation of SUN2 in mammalian cells. The key findings include the identification of a substrate recognition motif that appears to undergo casein kinase (CK) dependent phosphorylation. Mutagenesis studies show that mutants defective in phosphorylation are stabilized while a phosphor-mimetic mutant is more unstable. They further show that the degradation of SUN2 requires the AAA ATPase p97, which allows them to draw the analogy between SUN2 degradation and Vpu-induced degradation of CD4, which occurs on the ER membrane via the ERAD pathway. Lastly, they show that the stability of endogenous SUN2 is regulated by a phosphatase and that over-expression of a non-degradable SUN2 variant disrupts nuclear envelope morphology, cell cycle kinetics, and DNA repair efficiency. Overall, the study dissects another example of inner nuclear envelope protein turnover and the involvement of a pair of kinase and phosphatase in this regulation. The data are of extremely high quality and the manuscript is clearly written. That being said, the following questions should be addressed to improve the robustness of the conclusions and to avoid potential misinterpretation of the data.

1. Since SUN2 is normally incorporated into a SUN2-SYNE2-KASH2 LINC heterohexamer complex, the authors should be cautious with the use of over-expressed SUN2 in this study. Over-expressed SUN2 is expected to stay mostly as unassembled molecules and thus is likely degraded by a protein quality control mechanism that targets unassembled proteins. Consistent with this possibility, CK2 has been implicated in the regulated turnover of aggregation-prone proteins (Watabe, M. et al., JCS 2011). This mechanism would be potentially distinct from the one proposed for endogenous SUN2 degradation.<br /> 2. Certain conclusions appear to be an overstatement. This is particularly the case for the title, which implies that SUN2 is a protein that undergoes regulated turnover (under certain physiological conditions). Given that CK2 is a constitutive kinase and that the authors have not identified the conditions under which the activity of CTDNEP1 is regulated, it is premature to make such a conclusion.<br /> 3. Likewise, the demonstration of the impact of SUN2 accumulation on different cellular pathways mainly relies on the over-expression of a non-degradable SUN2 mutant. Whether similar defects could be seen when the degradation of endogenous SUN2 is blocked remains an open question.

Reviewer #3 (Public Review):

The goal of this paper is to describe how newly synthesized histones are imported into the nucleus.

Prior biochemical purifications suggest that H3-H4 dimers fold in the cytoplasm, are regulated by the sNASP histone chaperone, and translocate to the nucleus in association with the ASF1 histone chaperone and the importin-4 (Imp4) karyopherin. However, using an imaging-based approach, the authors previously showed that histones H3 and H4 can be imported into the nucleus as monomers.

Here, the authors show that new, cytoplasmic H3.1 and H4 monomers are bound by HSPA8 and importin-5 (Imp5). Imp5 then translocates monomeric histones into the nucleus and transfers H3.1 to sNASP. They further propose that the previously observed cytosolic H3-H4 dimers are not new histones but rather old nucleosomal histones that diffuse into the cytoplasm, which are then re-imported via Imp4. Therefore, folding of H3-H4 dimers exclusively occurs in the nucleus.

The authors certainly provide compelling evidence that monomeric histones are imported into the nucleus via Imp5. Constitutively monomeric histone mutants co-purified with Imp5 and the association was recapitulated in vitro. A wide range of exciting techniques is used to address how monomeric histones are handled in cells (i.e., biochemical, FRAP, imaging of cytoplasmic tethered and released histones, proximity-dependent protein labeling, etc). The aim of finding how monomeric histones are imported into the nucleus is certainly attained. More data could however support some of the conclusions regarding the association of histones to ASF1 and Imp4 and whether they truly exclusively represent evicted nucleosomal histones that diffused out of the nucleus.

Otherwise, the data shown here is certainly important for the field, as it provides an explanation of how monomeric histones are handled in the cytoplasm.

Reviewer #3 (Public Review):

The authors show miR-23a and miR-27a as an important regulator of bone homeostasis. They observed that miR 23a and miR27a regulates osteoclast function and loss of miR 23a and miR27a causes severe osteopenia conditions in mice without affecting osteoblast function. It has been already reported that miR27a regulates osteoclast function and inhibits osteoclast mediated bone resorption and F action formation (Guo L, et al). But the novelty of this manuscript is that single deletion of miR27a causes severe osteoporosis without affecting cortical bone. Reports suggest that p62 is an important regulator of osteoclastogenesis and deficiency of p62 impaired osteoclast differentiation. In paper, authors established a link between miR27a and p62 in osteoclast cells which could be a potential target for treatment of bone related disorders. Importantly, the mechanism of miR27a-p62 is not well explored in osteoclast cells.

Reviewer #3 (Public Review):

The work is of general interest to audiences of public policy and public health. The data found some evidence that mobile health interventions may be affected by the type of mobile used but failed to substantiate the claim conclusively on how the lack of mobile ownership may hinder their rollout process. The claim about gender or geographic inequality must be elaborated in detail and many countries in developing countries are now connecting more users in rural areas through unconventional methods such as village phones instead of just mobile ownership.

Strengths:

The main strength of this paper is the usage of the cross-sectional data from the R7 Afrobarometer survey which is a newly available dataset and contains comprehensive data from more than 50 African countries. The usage of the Bayesian Logistic Regression (BLR) model produced some useful findings.

Weakness:

1) The authors have generalized a lot of things in a very simple manner. For example, they have assumed if participants have access to the internet means they own a smartphone and if they don't then they are basic phone users. It is possible a lot of smartphone owners do not have subscriptions to the internet due to the high cost of internet in African countries.

2) They have consistently talked about inequalities in gender, and rural-urban geographic regions based on the odds ratio derived from the BLR. A regression decomposition technique can quantify these differences more elaborately in detail.

3) They failed to explain why a lot of poor people own smartphones. This could be due to the usage of village phones (first implemented by Grameen Phone in Bangladesh). This has expanded in African countries as well where multiple users communicate through a community phone connecting more users in rural areas.

4) Basic phones may also be effective for mobile health interventions through voice-enabled systems and disseminating important messages to communities. (For e.g. there is extensive literature on how community-level messages, such as instructions on personal hygiene and usage of masks, were transmitted through basic phones during the beginning of covid19 in developing parts of Asia).

5) Further clarification of why lack of ownership of a mobile phone may propagate inequalities in health is needed beyond just simple associations. A latent factor may also cause these differences.

Reviewer #3 (Public Review):

Llobet-Rosell et al. use Drosophila to decipher the relationships between factors in the Wallerian degeneration pathway and the metabolite NMN, an activator of the central pathway enzyme dSarm. NMN had previously been proposed to be a crucial regulator of Sarm, but there was a shortage of good in vivo evidence, especially in the crucial Drosophila system. The authors addressed this here by generating optimized fly lines, including a strongly expressing transgenic line for the NMN-consuming enzyme NMN-deamidase (NMNd). This variant conferred extremely strong protection against degeneration both in morphological and functional studies, thus confirming the key role of NMN as an activator of the degeneration pathway. They also confirm that NMNd alters NMN/NAD metabolism using mass spec of Drosophila heads, and then use Drosophila genetics to show that dSarm is the crucial NMN target. In a reverse experiment, the authors also use overexpression of murine NAMPT, an NMN-producing enzyme, to speed up degeneration. As in mammals, NMNd delays degeneration induced by loss of Nmnat.

A clear strength of the fly system is the degree of rescue conferred by the optimized NMN-D reagent which essentially establishes NMN as a crucial regulator in the pathway. The rigor of experimentation is also very high. Essentially all reagents are optimized, and most conclusions are backed by complementary analyses. The manuscript also nicely describes a metabolomic analysis of NAD biosynthetic pathways from fly heads.

Reviewer #3 (Public Review):

In this manuscript, the authors investigate the behavioral and brain transcriptional alterations associated with short- and long-term partner separation in the monogamous male prairie vole. Male prairie voles continue to show affiliative behavior after short- (2 days) and long-term (4-weeks) partner separation, with similar effects for same and opposite-sex pairs. However, the transcriptional signature in the nucleus accumbens exhibits marked alterations after long-term separation.

Strengths:<br /> 1) A key strength of this manuscript is its use of the monogamous prairie vole to investigate transcriptional alterations associated with pair bonding and subsequent pair separation. This sort of behavior cannot be investigated in typical rodent model systems (e.g., mice, rats), and the choice of using prairie voles allows for dissection of potential mechanisms of social bonding with relevance to partner loss in humans.<br /> 2) Investigation of behavioral measures and transcriptional alterations at both short- and long-term time points after pairing and separation is a strength of the manuscript. These time points were selected based on previous studies in laboratory and wild prairie voles related to the time it takes to form a pair bond and for the male prairie vole to leave the nest after the loss of the female pair. The datasets generated will be of great use to the scientific community.<br /> 3) The authors investigate the behavior and transcriptional profiles after same-sex as well as opposite-sex pairing. This is considered a thoughtful decision on the authors' part which allows them to tease apart the effects of same vs. opposite sex.<br /> 4) The use of numerous behavioral measures to assess both affiliative and aggressive behaviors is a strength of the approach.<br /> 5) The authors use many biostatistical approaches (e.g., RRHO, WGCNA, Enrichr) to probe the transcriptomics data. These approaches allow the authors to move beyond simply assessing transcriptional profiles separately, but to look for patterns that are similar or different across datasets.<br /> 6) The authors use rigorous statistical methods to assess behavioral measures.<br /> 7) The TRAP approach in prairie voles is novel and will provide a great resource to the research community.

Weaknesses:<br /> 1) The methods state that prairie voles were treated differently in the behavioral and transcriptomics studies. Specifically, for the separation in the behavioral studies, prairie voles were separated by sight, but not necessarily by the smell from partners (i.e., partners were kept ~1 foot apart). However, prairie voles in the transcriptomics studies were separated by both sight and smell (i.e., partners were sacrificed after separation). Thus, it is possible that the lack of degradation of pair bond-related behavior after long-term separation might be due to these prairie voles being able to smell their partners after separation. This is considered a moderate flaw in the design of the studies which limits the integration of results between behavior and transcriptomics. This might be why the authors do not see a strong behavioral degradation of pair bond-related behavior after long-term separation but do see a strong transcriptional signature.<br /> 2) While RRHO is helpful to assess overall patterns of transcriptional signatures across datasets, its utility for determining the exact transcripts is limited. This is because of how RRHO determines the overlapping transcripts for its Venn diagram feature (by taking the point where the p-value is most significant and taking the list to the outside corner of that quadrant).<br /> 3) TRAP expression was verified in only one animal. Thus, the approach has not been appropriately confirmed.

Reviewer #3 (Public Review):

In this manuscript, Dodd et al. measure the internalization of exogenous fluorescently-labelled tau by cultured HEK cells and iPSC-derived neurons, as well as the aggregation of fluorescent fusion proteins of the repeat domain of tau with the P301S mutation (tau RD) expressed in these cells. They find that inhibition or reduction of V-ATPases and Rab5A reduces tau internalization and increases tau RD aggregation, as does culturing the cells at cold temperatures. The authors also find that exogenous fluorescently-labelled tau is internalized by HEK cell-derived GPMVs. All conditions are dependent on HSPGs, which presumably act as cell-surface attachment factors, similar to their role in the attachment of viruses to the cell surface. Based on the involvement of V-ATPases and Rab5A in endocytosis, the authors conclude that endocytosis of tau does not contribute to the aggregation of expressed tau. In addition, based on the lack of endocytosis in GPMVs, the authors conclude that tau can translocate across membranes and that this contributes to the aggregation of expressed tau.

The observation that conditions that decrease the overall internalization of exogenous tau can increase the aggregation of expressed tau suggests that multiple internalization routes exist, some of which are non-productive for the aggregation of expressed tau. This has important consequences for therapeutic strategies aiming to limit the internalization of tau. However, the conclusions that tau can translocate across membranes and that this contributes to the aggregation of expressed tau, whereas endocytosis of tau is non-productive for the aggregation of expressed tau, are not fully supported by the data.

Major comments:<br /> 1. There appear to be several alternative interpretations other than a reduction of endocytosis for the effects of perturbing V-ATPase and Rab5A function and culturing cells at cold temperatures. First, internalized tau was measured 4 h after the addition of exogenous tau to the cells. This seems like a long time for the study of endocytosis, which occurs in minutes. By 4 h, degradation of tau may have an effect on the amount of measurable internalized tau. This is important because, in addition to their roles in endocytosis, V-ATPases and Rab5A also have roles in protein degradation via the endolysosomal system. Similarly, culturing cells at cold temperatures for 4 h is expected to have many effects beyond the inhibition of endocytosis. In addition, the authors do not control for humidity and CO2 concentration, which could also affect their measurements. Perturbation of V-ATPases and Rab5A could also be exerting their effects by reducing the translocation of tau across endolysosomal membranes, instead of endocytosis. The authors found that the expression of dominant-negative dynamin increased the amount of internalized tau. Is this unexpected, given that dynamin is required for most forms of endocytosis and has been previously reported to be required for tau endocytosis (Wu et al. 2013. J. Biol. Chem. 288, 1856-1870; Falcon et al. 2018. J. Biol. Chem. 293, 2438-2451; Evans et al. 2018. Cell Rep. 22, 3612¬-3624)?

2. It is difficult to draw parallels between the experiments using cells and those using GPMVs. The authors use 25 nM tau for cell experiments, but 500 uM tau for GPMV experiments. This is a huge difference in concentration. The authors should carry out the GPMV experiments using the same concentration of tau as in the cell experiments. 500 uM is also a very high concentration and raises the question of if the GMPVs are completely sealed. GMPVs have recently been reported to be permeable to hydrophilic macromolecules (Skinkle et al. 2020. Biophys. J. 118, 1292-1300). Tau and the TAT peptide are more hydrophilic than the two negative controls used, transferrin and albumin.

3. It is not clear which molecular species of tau (monomers, oligomers, or fibrils) are being studied. The authors refer to tau fibrils, but the species of recombinant tau they are using are never characterised. Incubation of tau with heparin can be expected to result in a mixture of fibrils, oligomers, and monomers. Sonication may also change the distribution of tau species by liberating oligomers and monomers from fibrils. Similarly, key details about the immunoprecipitation are lacking, including neuropathological characterization of the human cases, the brain region, the amount of brain tissue, the lysis buffer, the epitope of the Tau B antibody, the amount of Dynabeads, and analysis of the immunoprecipitated sample to show what species of tau are present.

Reviewer #3 (Public Review):

Vignogna et al. used yeast genetics, experimental evolution and biochemistry to tackle human congenital disorders of glycosylation (CDG), a disease mostly caused by mutations in PMM2. They took advantage of the observation that the budding yeast gene SEC53 is almost identical to human PMM2, and used experimental evolution to find interactors of SEC53/PMM2. They found an overrepresentation of mutations in genes corresponding to other human CDG genes, including PGM1. Genetic and biochemical characterizations of the pgm1 mutations were carried out. This work is solid, although authors did not reveal why reduction of pgm1 activity could compensate for defects of a particular mutant allele of sec53.

Out of curiosity, if the authors were to simply focus on the preexisting mutations, would they have gotten the materials for most of the experiments in this article? In other words, how important is the experimental evolution?<br /> A strain table with full genotypes is needed.

Reviewer #3 (Public Review):

The authors report the structure of CPSF30 bound to 2 molecules of FIP1, as well as the structure of FIP1 bound to CSTF77. Their data supports a model in which two molecules of FIP1, are present in the mPSF subcomplex of CPSF, although only one PAP may be bound to this complex. TheCstF77 binding to Fip1, which likely inhibits polyadenylation since it interferes with PAP binding, would occur as the complete complex assembles on the substrate, and result in the active cleavage complex not containing PAP or active in polyadenylation, only becoming active in polyadenylation after cleavage and loss of CstF from the complex.

Reviewer #3 (Public Review):

The authors explored the net patterns of selection in cancers as measured from tumor:normal exome and whole genome sequencing data. They found that by stratifying tumors on total mutation load, tumors with a low mutation burden exhibited net diversifying selection on previously identified oncogenic driver genes and net purifying selection on non-driver genes. Somewhat counter-intuitively both of these patterns decayed with increasing total mutation burden to the point where for tumors with the highest mutation burden, no net selection signals were identifiable. These findings were replicated using two dN/dS based approaches (with distinct means of defining the null expectation) and also using structural rearrangements as an orthogonal approach. The findings seem well demonstrated.

The proposed explanation for these observations is that of Hill-Roberson interference, where the (almost) perfect linkage disequilibrium of the whole genome in a clonally expanding population of cells provides little opportunity to separate mutations of opposing fitness effects leading to the accumulation of deleterious mutations without opportunity for their removal by selection. An important implication of this conclusion is that tumors, particularly those with a high mutation load, carry a high burden of deleterious mutations.

The modelling of clonal evolution demonstrates that Hill-Robertson like processes can in principal explain the decay of selection signals wither a high mutation burden, though this modelling by the authors own admission has lax parameter constraints and are gross simplifications of reality. As a proof of principal this modelling seems sufficient, and the estimated fitness effects appropriately qualified as "highly provisional".

The authors present the up-regulation of heat-shock/chaperone/protein-degradation pathways as a plausible mechanism through which cancers could manage the accumulation of many deleterious mutations and provide correlative evidence for increased expression of such genes in tumors with higher mutation burdens (Fig 2G). By considering only one such scenario the authors are perhaps placing too much emphasis on that one mechanistic hypothesis for (amino acid changing) mutational tolerance. Other plausible mechanisms include suppression of epitope presentation (adaptive immune evasion), replication stress etc.

Understanding that tumors carry substantial deleterious mutation loads and some prelimiary quantitative estimates of that will be of broad interest to the cancer genomics and also wider fields. The preprint is already being cited and found to be useful. The work also raises an important question - what are the main mechanisms employed to tolerate that deleterious mutation load, if there are predominant mechanisms such as the proposed protein-misfolding response, they become interesting targets for therapeutic suppression in a broad spectrum of cancers.

Reviewer #3 (Public Review):

Tarasov et al have undertaken a very extensive series of studies in a transgenic mouse model (cardiomyocyte-specific overexpression of adenylyl cyclase type 8) that apparently resists the chronic stress of excessive cAMP signaling for around a year or so without overt heart failure. Based on the extensive analyses, including RNAseq and proteomic screening, the authors have hunted for potential "adaptive" or "protective" pathways. There is a wealth of information in this study and the experiments appear to have been carefully performed from a technical viewpoint. Many interesting pathways are identified and there is plenty of information where additional experiments could be designed.

General comments<br /> 1. Ultimately, this is a descriptive and hypothesis-generating study rather than providing directly proven mechanistic insights. T<br /> -Given several prior studies reporting a detrimental effect of chronically increased cAMP signaling, what is it that is different in this model? Is it something specific about AC8? Is it to do with when (in life) the stress commences?<br /> - Is the information herein relevant to stress adaptation in general or is it just something interesting in this specific mouse model?

2. None of the pathways that are apparently activated were directly perturbed so their mechanistic role requires further study.

Specific<br /> 1. The strain of the mice and their sex needs to be stated as well as the exact age at which the various assays were performed.<br /> 2. The hearts of the Tg mice have more cardiomyocytes but which are smaller. Since there is no observed increase in proliferation of cardiomyocytes, how (or when) did this increase in cell number occur?<br /> 3. While the mice do not show an increased mortality up to 12 months of age, HR/CO/EF are poor indices of contractile function. Data on end-systolic elastance or perhaps echo-based LV strain indices which will be relatively load-independent would be useful.<br /> 4. Quite a lot of conclusions are made relating to metabolism. However, this is entirely based on gene expression or protein levels. Given the substantial role of allosteric regulation in metabolic control, as well as the interconnectedness of metabolic pathways, ultimately any robust conclusions need to be based on an assessment of activity of key pathways.

Reviewer #3 (Public Review):

The manuscript adds useful information about how structural properties of the brain are related to individual differences in autobiographical memory. A novel metric is used to assess features of white matter in tracts that are important for information exchange between the hippocampus and other brain regions. In one of these, the parahippocampal bundle, a relationship between the MR g-ratio and autobiographical memory recall is identified. This represents new and interesting information. The authors interpret the results in line with the theory that speed of signal transmission is important for cognitive function.

Reviewer #3 (Public Review):

Krug et al. used emerging model species in biomedical research, Nothobranchius furzeri, to construct a triple mutant line that lacks all three major pigments found in fish (melanophores, iridophores, xanthophores). It demonstrates clearly that multiple genes can be inactivated simultaneously in this species, and that a new line can be a source of additional genetic manipulations. This is because their condition, vigour, and fecundity are standard compared to the wild type, which is convincingly demonstrated.

The introduction is appropriate and results generally correctly report what has been achieved, which is then adequately addressed in the discussion. Methods, as far as I can estimate, are sufficient to replicate the work.

The only substantial point I raise relates to the sexual selection (mate choice) part of the work. While it has no major effect on the overall conclusion, I think their interpretation needs to be reconsidered.

When reporting the results of mate choice experiment (L219ff), the authors state that males of wild and Klara type preferred wild-type females, because 75% of laid eggs belonged to wild-type females. However, another possibility is that Klara females had reduced fecundity, and the lower share of eggs had nothing to do with mate choice. In the same way, "90% of eggs were fertilized by wild-type males" (L223) is used to conclude that they were preferred by females (active mate choice). However, male success in N. furzeri is largely driven by male dominance (and not female mate choice) and it is more likely (and more precise to state) that wild-type males were more successful in male-male competition for access to females (and fertilize their eggs). This is especially so because wild-type males were larger (L. 322) and body size plays a major role in establishing dominance between N. furzeri males. This is then also pertaining to interpretation in discussion (L 318).

While I think this needs to be corrected to avoid misinterpretation, it has a minor impact on the overall high standard of the work or on general interpretation.

Reviewer #3 (Public Review):

This manuscript uses MEG data acquired from human participants to examine whether representations of competing memories are associated with different phases of the theta rhythm in the human hippocampus. In brief, the authors use a proactive interference task in which subjects are asked to associate a word with two competing images and then subsequently recall the most recent image. Using pattern classifiers on the MEG data, the authors are able to decode reactivated content of the target and competitor memories and find that these patterns appear locked to different phases of the hippocampal rhythm. They also show that those subjects with worse memory performance had fewer differences in the phases to which target and competitor memories are locked. Together, the data provide support for a computational model of competing memories which suggests that oscillatory inhibition can be leveraged to strengthen or weaken inhibition of target and competitor memories (oscillating interference resolution model). One of the main strengths of the manuscript is that this is a pre-registered study, and so the specific hypotheses tested here have previously been reported. The current manuscript does not deviate too significantly from the pre-registered hypotheses and plan and reports the results of those proposed analyses. As such, this manuscript, therefore, presents a valuable addition to the literature, since it reports the results of a clearly established set of hypotheses testing a very specific question regarding memory interference.

Reviewer #3 (Public Review):

In this manuscript, Jorgensen and colleagues elegantly used cutting-edge technologies to understand how different Ca entries lead to two different types of presynaptic release. They demonstrated that at the worm neuromuscular junctions two different classes of voltage-gated calcium channels, CaV2 and CaV1, mediate the release of distinct pools of synaptic vesicles. CaV2 channels are concentrated in densely packed clusters near the molecularly and EM-defined active zone structures. This type of release is dependent on synaptic vesicle priming protein UNC-13L. By contrast, they found that CaV1 channels are dispersed in synaptic varicosity and are coupled to internal calcium stores via the ryanodine receptor. CaV1 and ryanodine receptors mediate the fusion of vesicles docked broadly in synaptic varicosity and are colocalized with the vesicle priming protein UNC-13S.

The authors were able to direct their hypotheses because they have established powerful experimental methods such as rapid freezing EM coupled with neuronal stimulation. They used genetic null mutants for most of their experiments. They created endogenously labeled proteins to test the localization of proteins in live preparations. They used a combination and electrophysiological and behavioral assays. Since they worked with a system that has a small number of synaptic connections, they can reliably study the same set of synapses. The rigor of these experiments is extremely high.

The comprehensive approaches and the clear-cut results made this manuscript easily the top two or three papers I have read in the last couple of years of any journals.

Reviewer #3 (Public Review):

In this work, the authors employ a deep convolutional neural network approach to map protein sequence to function. The rationales are that (i) once trained, the neural network would offer fast predictions for new sequences, facilitating exploration and discovery without the need for extensive computational resources, (ii) that the embedding of protein sequences in a fixed-dimensional space would allow potential analyses and interpretation of sequence-function relationships across proteins, and (iii) predicting protein function in a way that is different from alignment-based approaches could lead to new insights or superior performance, at least in certain regimes, thereby complementing existing approaches. I believe the authors demonstrate i and iii convincingly, whereas ii was left open-ended.

A strength of the work is showing that the trained CNNs perform generally on par with existing alignment based-methods such as BLASTp, with a precision-recall tradeoff that differs from BLASTp. Because the method is more precise at lower recall values, whereas BLASTp has higher recall at lower precision values, it is indeed a good complement to BLASTp, as demonstrated by the top performance of the ensemble approach containing both methods.

Another strength of the work is its emphasis on usability and interpretability, as demonstrated in the graphical interface, use of class activation mapping for sub-sequence attribution, and the analysis of hierarchical functional clustering when projecting the high-dimensional embedding into UMAP projections.

However, a main weakness is the premise that this approach is new. For example, the authors claim that existing deep learning "models cannot infer functional annotation for full-length protein sequences." However, as the proposed method is a straightforward deep neural network implementation, there have been other very similar approaches published for protein function prediction. For example, Cai, Wang, and Deng, Frontiers in Bioengineering and Biotechnology (2020),<br /> the latter also being a CNN approach. As such, it is difficult to assess how this approach differs from or builds on previous work.

A second weakness is that it was not clear what new insights the UMAP projections of the sequence embedding could offer. For example, the authors mention that "a generalized mapping between sequence space and the space of protein functions...is useful for tasks other than those for which the models were trained." However, such tasks were not explicitly explained. The hierarchical clustering of enzymatic proteins shown in Fig. 5 and the clustering of non-enzymatic proteins in Fig. 6 are consistent with the expectation of separability in the high-dimensional embedding space that would be necessary for good CNN performance (although the sub-groups are sometimes not well-separated. For example, only the second level and leaf level are well-separated in the enzyme classification UMAP hierarchy). Therefore, the value-added of the UMAP representation should be something like using these plots to gain insight into a family or sub-family of enzymes.

The clear presentation, ease of use, and computationally accessible downstream analytics of this work make it of broad utility to the field.

Reviewer #3 (Public Review):

In this manuscript, Ibáñez-Solé et al aim to clarify the answer to a very basic and important question that has gained a lot of attention in the past ~5 years due to fast-increasing pace of research in the aging field and development/optimization of single-cell gene expression quantification techniques: how does noise in gene expression change during the course of cellular/tissue aging? As the authors clearly describe, there have been multiple datasets available in the literature but one could not say the same for the number of available analysis pipelines, especially a pipeline that quantifies membership of single cells to their assigned cell type cluster. To address these needs, Ibáñez-Solé et al developed: 1. a toolkit (named Decibel) to implement the common methods for the quantification of age-related noise in scRNAseq data; and 2. a method (named Scallop) for obtaining membership information for single-cells regarding their assigned cell-type cluster. Their analyses showed that previously-published aging datasets had large variability between tissues and datasets, and importantly the author's results show that noise-increase in aging could not be claimed as a universal phenotype (as previously suggested by various studies).

Comments:

1. In two relevant papers (doi.org/10.1038/s41467-017-00752-9 and doi.org/10.1016/j.isci.2018.08.011), previous work had already shown what haploid/diploid genetic backgrounds could show in terms of intercellular/intracellular noise. Due to the direct nature of age/noise quantification in these papers, one cannot blame any computational pipeline-related issues for the "unconventional" results. The authors should cite and sufficiently discuss the noise-related results of these papers in their Discussion section. These two papers collectively show how the specific gene, its protein half-life and ploidy can lead to similar/different noise outcomes.

2. While the authors correctly put a lot of emphasis on studying the same cell type or tissue for a faithful interpretation of noise-related results, they ignore another important factor: tracking the same cell over time instead of calculating noise from single-cell populations at supposedly-different age points. Obviously, scRNAseq cannot analyze the same cell twice, but inability to assess noise-in-aging in the same cell over time is still an important concern. Noise could/does affect the generation durations and therefore neighboring cells in the same cluster may not have experienced the same amount of mitotic aging, for example. Also, perhaps a cell has already entered senescence at early age in the same tissue. This caveat should be properly discussed.

3. Another weakness of this study is that the authors did not show the source/cause of decreasing/stable/increasing noise during aging. Understanding the source of loss of cell type identity is also important but this manuscript was about noise in aging, so it would have been nice if there could be some attempts to explain why noise is having this/that trend in differentially aged cell types in specific tissues.

4. In the discussion section, the authors say that "Most importantly, Scallop measures transcriptional noise by membership to cell type-specific clusters which is a re-definition of the original formulation of noise by Raser and O'Shea." It is not clear what the authors refer to by "the original formulation of noise by Raser and O'Shea". Intrinsic/extrinsic noise formulations?? Please be more specific.

Reviewer #3 (Public Review):

The paper emphasizes the importance of testing males and females in parallel when designing mice experiments as well as being consistent with age. In agreement with this, significant differences were observed between mice of different sexes and of varying ages. It also offers many insights into how DIA-PASEF workflows can improve performance in proteomics.

I would suggest to the authors they explain how experiments could be designed in a small scale in case there are time and financial constraints so that both female and male mice can be used simultaneously. It would also be beneficial to read over any challenges associated with the DIA-PASEF analysis. Enrich the discussion with performance comparison between DIA-PASEF and DDA-PASEF for mice proteomics data male versus female.<br /> Were there any unique proteins only found by DIA-PASEF?

Reviewer #3 (Public Review):

This timely manuscript describes the sex dimorphisms in neonatal development as it applies to muscle injury and denervation. More and more studies are identifying sex differences in skeletal muscle function and dysfunction. This is one more study to point out differences. A missing piece to the field and this study are the mechanistic links between skeletal muscle function/dysfunction and sex differences. This paper starts to point to a mechanism highlighting the non-canonical AKT pathway. This is a very well-written manuscript with a clear experimental plan and workflow. I have no major concerns.

My biggest question is the molecular mechanism linking sex differences and skeletal muscle function and dysfunction. However, this is perhaps a follow-up study to the already complete study the authors present.

Reviewer #3 (Public Review):

The paper uses a mixture of game-theoretical models and individual-based simulations to study the coevolution of manipulation and resistance to manipulation in social interactions. This is a very impressive piece of theoretical research that will likely open new directions for both theoretical and empirical work.

Reviewer #3 (Public Review):

The authors investigate range adaptation in the orbitofrontal cortex by taking advantage of an existing data set on willingness to gamble where two different groups experienced a wider or a narrower range of gains but the same range of losses. They find that sensitivity not only to gains but also to losses changes as a function of the gain range, such that for the part that was common to the two groups, people in the wide range group were less willing to gamble than people in the narrow range group. Moreover, a two-layer artificial network with Hebbian plasticity explains the behavioral effects of ranges and multivariate neural representations of value in the orbitofrontal cortex. The authors conclude that range adaptation occurs at the level of the integration layer rather than at the level of the attribute-specific input layer (where gains and losses are separate). The paper provides a welcome addition to the literature on how range adaptations may come about but would benefit from a couple of clarifications.

Major:<br /> 1) It appears like the Gaussian assumption may explain as much or even more of the variance as the plasticity assumption. However, the results do not really address this point. It would be good to provide some information about it for the behavioral findings, check whether the impression also holds for OFC and vmPFC activity, and discuss what the Gaussian assumption implies for the representation of value as such. After all, the monotonicity assumption pervades most previous research on value representation and seems to have been supported reasonably well so far (sometimes with the refinement that positive and negative coding monotonic signals/neurons may be intermixed). Relatedly, one may assume that the Gaussian assumption primarily holds for chosen value cells. But Figure 6 suggests that offer value units are more common in the model. Please explain.

2) The paper dismisses simplistic efficient coding scenarios that operate on neurons that transmit gain/loss information based on either finding common coding of gain and loss information but no difference between range groups or a difference between range groups but no common coding of gain and loss information. Did the authors also consider common coding of a) expected value, b) gains only, and differences between range groups in (a) and (b) signals, instead of looking at both gains and losses? Because the range manipulation primarily concerned gains rather than both gains and losses, there may be more power in looking at gains only. It may also be worth mentioning that at least for simple reward prediction error signals, a within-subject design, and regions other than the OFC, the simplistic analysis approach can find both effects (Kirschner et al., 2018, Brain). Of course, some of the mentioned or other differences may explain the difference in findings.

Reviewer #3 (Public Review):

The enhancer chromatin-modifying enzyme MLL3 functions as a tumor suppressor in multiple human cancers, however, the mechanisms underlying its tumor suppressive function remain unclear. The manuscript of Soto-Feliciano et al. focused on Myc-driven liver cancer and aimed to address and fill the gap. The authors used an elegant genetic design and approach to manipulate the overexpression of the Myc oncogene and knockout of the Mll3 tumor suppressor gene in mouse liver cancer models. Their genetic mouse models showed that loss of Mll3 constrains Myc-driven liver tumorigenesis, with tumors having a slightly later onset compared to mice with Myc overexpression in conjunction with p53 inactivation. Because MLL3 is a major histone-modifying enzyme for enhancer-associated H3K4 monomethylation and is responsible for enhancer activation and the following target gene transcription, they performed ChIP-seq analysis to study the roles of Mll3 in Myc-driven mouse liver cancer. Interestingly, their ChIP-seq studies revealed that loss of Mll3 preferentially limits Mll3 enrichments at promoters and thereby attenuates promoter-associated H3K4 trimethylation and target gene transcription, whereas the unchanged Mll3 genomic binding between the two genotypes (Myc;sgp53 and Myc;sgMll3) is largely located within enhancer (intergenic) regions. They further demonstrated that the cdkn2a locus is a genomic and transcriptional target of Mll3 in Myc-driven mouse liver cancer. Supporting their findings, genomic inactivations of MLL3 and CDKN2A displays mutual exclusivity in human liver cancer and many other cancer types. Furthermore, they described a possible mechanism for MLL3's role in MYC-driven liver cancer that MLL3 mediates MYC-induced apoptosis in a CDKN2A-dependent manner by manipulating Myc overexpression, Mll3 function, and Cdkn2a regulation in their genetic mice models. This manuscript describes a potential function of MLL3 in the control of tumor suppressor gene expression via modulating their promoter chromatin landscapes. More importantly, loss of normal function of MLL3 or the downstream effector CDKN2A may impair MYC-induced apoptosis, and in turn, lead to MYC-induced tumorigenesis.

Overall, the manuscript is well written, organized, and focused on an interesting topic, and with data presented supports the authors' claims.

Reviewer #3 (Public Review):

The manuscript by Inada et al. examines the role of hypothalamic oxytocin (OT) signaling in feeding behavior. They demonstrate that conditional knockout (KO) of OT in the adult paraventricular hypothalamic nucleus (PVH) increases body weight through increases in food intake, and that conditional knockout of the OT receptor in the posterior hypothalamus has a similar effect. The authors therefore conclude that OT signaling in the posterior hypothalamus, presumably through oxytocin produced in the PVH, contributes to energy balance control.

Strengths:<br /> There has been conflicting literature on the role of OT in feeding behavior. Although pharmacological and genetic approaches have suggested an anorexic effect of OT, knockout of OT or OT receptor has minimal effect on feeding. To address this apparent discrepancy, the authors use conditional knockout models to manipulate OT signaling. This allows not only temporal control of OT and OT receptor, but also allows investigation of signaling in different brain regions (versus, for example, whole body or organ). That the conditional knockout mice display hyperphagia and obesity begins to settle this conflict in the literature.

Weaknesses:

1) There is not much conceptual advance in the study. The data largely confirm what pharmacological and RNAi knockdown studies have previously demonstrated.

2) The finding that IP injection of OT partially rescues the phenotype of the KO mouse lacks rigor and proper controls. It is important to show that the dose of OT used does not influence body weight in wildtype mice in order to make the conclusion that it "rescues" the phenotype of the KP mouse.

3) There is little anatomical precision in the manipulation of OT receptors in the "posterior hypothalamus." Understanding which of these brain regions (e.g. ARH, VMH, LHA, DMH, others?) is involved in mediating these effects would be very informative.

Reviewer #3 (Public Review):

To investigate their role in B cell development and function, the authors conditionally delete of the structure-specific endonucleases GEN1 and MUS81 at early and late stages of B cell development. Using MB1-Cre, the authors find GEN1 and MUS81 play redundant and essential roles in B cell development, leading to an almost complete depletion of B cells in the pro-B and later stages that was rigorously shown. Conditional deletion of Mus81 in transitional B cells by CD23-cre circumvented this developmental delay, but led to a severe defect in germinal center formation in lymph nodes, Peyer's patches and the spleen specifically in double-deficient cells though total B cell numbers were similar to WT. Further characterization by in vitro stimulated cells revealed that loss of both Gen1 and Mus81 dramatically reduces cell proliferation, induces G2/M checkpoint activation, apoptosis and genome instability. The authors conclude that these defects are caused by MUS81/GEN1's shared role in processing recombination intermediates created by replication stress but do not show the cells experience replication stress. Further, there is no characterization of class switch recombination or IgH damage in the cells, which feels noticeably absent. Finally, the DNA damage analyses presented would benefit from being clarified and extended.

Overall this is an elegant and straightforward dissection of the role of GEN1 and MUS81 in B cell development, but in its current form the manuscript does not directly connect the observed phenotypes to the molecular role of GEN1/MUS81 in DSB repair.

Reviewer #3 (Public Review):

Lucas et al. expand upon their prior work using 2D high-resolution template-matching (2DTM) to localize macromolecules directly in cells. This clearly presented work contains multiple key highlights using the Saccharomyces cerevisiae 60S maturation process as an example. It demonstrates that focused ion beam (FIB)-milling preserves sufficient high-resolution (better than 4 Å) information for the 2DTM to effectively locate macromolecules in the dense cellular environment. In addition, it demonstrates that the classification of the detected macromolecules can be effectively determined by comparison of the signal-to-noise ratios obtained with 2DTM against templates with relatively minor differences. Furthermore, the authors detail a maximum likelihood approach to specify the confidence of the class assignment for a macromolecule within a mixed population. The authors take advantage of extensive prior knowledge of the 60S biogenesis process to thoroughly evaluate and demonstrate the utility of the 2DTM methodology and accompanying classification strategy.

2DTM has great potential to motivate a broader adoption of cryo-EM for those more interested in robust localization of macromolecules of known structure rather than de novo high-resolution structure determination through conventional averaging approaches. Conventional averaging approaches for cryo-EM data notably suffer at the level of classification for which the results can vary greatly based on choice of a multitude of parameters. The classification strategy presented here for 2DTM should be reproducible and the parameter choice (i.e., priors) more straightforward.

Reviewer #3 (Public Review):

Numerous studies have demonstrated that the neural dynamics on different brain areas encode elapsed time, yet it has proven challenging to examine how these population clocks emerge over the course of learning because most temporal tasks require many training sessions. In this manuscript the authors use a simple timing task that can be learned in a single day, and accompany the changes in neural dynamics in the mPFC and STR of the first and second day on the task. The most interesting finding is a switch in which the mPFC provides a better code than the STR for elapsed time on the first day, but the STR provides a better code than the mPFC on the second day. Consistent with the increased encoding of time in the mPFC early in training, muscimol inactivation of the mPFC impaired learning of the task, but not performance in trained animals. Overall this study provides a number of novel contributions to our understanding of temporal processing, and show the first example of learning-dependent switch from the dynamics of the mPFC to that of the STR encode time.

Reviewer #3 (Public Review):

In this work, Chen et al. measured the DNA binding dynamics of HIF transcription factors using single-particle tracking. In particular, they examined the impact of heterodimerization between the alpha and beta subunits, the integrity of the DNA binding domain and the nature of the transactivation domain in DNA binding. As expected, they found that the stoichiometry between the heterodimerization partners directly impacts the bound fraction of the beta subunit which is devoid of a DNA binding domain. More interestingly, using domain swaps between HIF-1alpha and HIF2-alpha they found that the transactivation domain of the alpha subunit plays a major role in determining the bound fraction of the beta subunit (and thus the heterodimer). This work is important because it increases our understanding of how TF search the genome, beyond the traditional conception of the "addressing tag" provided solely by the DNA binding domain. This work is thus of interest to the broad audience of scientists studying gene regulation.

Reviewer #3 (Public Review):

Fang et al. created an atlas for associations between the genetic liability of common risk factors or complex disorders and the abundance of small molecules as well as the characteristics of major apolipoproteins in blood. The whole study is well executed, and the statistical framework is sound. A clear strength of the study is the large array of common risk factors and disease analyzed by means of polygenic risk scores (PRS). Further, the development of an open access platform with appealing graphical display of study results is another strength of the work. Such a reference catalog can help to identify novel biomarkers for diseases and possible causative mechanisms. The authors further show, how such a systematic investigation can also help to distinguish cause from causation. For example, an inflammatory molecule readily measured by the NMR platform and strongly associated in observational studies, is likely to be a consequence rather than a cause for common complex diseases.

However, in its current form, the study suffers from some weakness that would need to be addressed to improve the applicability of the 'atlas'. This includes a distinction of locus-specific versus real polygenic effects, that is, to what extend are findings for a PRS driven by strong single genetic variants that have been shown to have dramatic impact on small molecule concentrations in blood. Further, it is unclear how much NMR spectroscopy adds over and above established clinical biomarkers, such as LDL-cholesterol or total triglycerides. This is in particular important, since the authors do not adequately distinguish between small molecules, such as amino acids, and characteristics of lipoprotein particles, e.g., the cholesterol content of VLDL, LDL or HDL particles, the latter presenting the vast majority of measures provided by the NMR platform. Finally, the study would benefit from more intriguing or novel examples, how such an atlas could help to identify novel biomarkers or potential causal metabolites, or lipoprotein measures other than the long-established markers named in the manuscript, such as creatinine or lipoproteins.

Reviewer #3 (Public Review):

In this study the authors investigated whether mountain gorillas of varying ages behave differently toward their siblings compared to non-siblings, and, how this bias varied based on whether individuals were full or maternal half-siblings vs. paternal siblings, opposite or same-sex siblings, and close or far apart in age (with age as a continuous variable).

This study has two major strengths:<br /> One is its long-term dataset. Authors document social interactions for 157 individuals over 14 years on wild mountain gorillas. This is amazing!

A second major strength is the opportunity this dataset and study system provides to test predictions about proposed mechanisms for kin recognition in primates. The authors do a good job of making these details about their study system and their predictions clear:

Kin selection is a proposed mechanism for the evolution of cooperative behavior. For it to operate, animals must have some mechanism by which to recognize their genetic kin and affiliate and cooperate differentially with these kin than with non-kin. However primatological studies have revealed that routes to kin recognition that are immediately clear. First, there are many examples of cooperation with non-kin. Second, in certain species, individuals bias affiliation and cooperation toward maternal but not paternal kin. Because these maternal-kin-biased species are ones with low male reproductive skew (many females mate with many males and many males father infants) and where mothers are sole caregivers of offspring, both the mating system and the familiarity of growing up together under the care of the same mother (especially if close in age) are proposed to drive affiliative and cooperative biases. Mountain gorillas provide a strong model to test these predictions because there is low male reproductive skew and individuals may live in cohesive groups with both maternal siblings and paternal siblings of all ages throughout their lives.

However, this study has two major weaknesses.

First, it lacks clarity in the actual measures of kin bias: that is - how dyadic social interactions and relationships manifest in mountain gorillas and how these change throughout life as relevant to the measures used.<br /> For example, the authors provide little information on the ages of the siblings involved in the study (only that the median was 9.7 years). How do these ages match to different developmental stages and dimensions of mountain gorilla social interaction? For instance, the frequency of play, one of the three social affiliative social measures employed, might vary considerably based on age. In many other species, it occurs more often between immature individuals or between a mature and immature individual rather than between mature ones.

Relatedly, siblings who affiliate frequently do not necessarily need to have reduced aggression. Studies of dyadic affiliative bonds in baboons and chimpanzees both indicate that in certain contexts individuals who affiliate more may also have increased conflict. What might distinguish certain more cooperative bonds from others, for example, is what happens after this conflict. This is not something the authors need to measure in this study but it would be helpful to have such nuances of relationships discussed, or at least to provide the reader with more context for interpreting the behavioral results of affiliation and aggression as assays for kin-bias and potential fitness benefits associated with this bias.

Second, relatedly - there was no basis provided for the evolutionary function of sibling affiliation - that is, how might affiliation as measured by proximity, grooming, and play, contribute to cooperation and/or improved fitness in mountain gorillas? The existence of some form of dyadic social bond benefit (such as alliances, or improved survival) is necessary for kin selection to be in play. What might the functions of sibling relationships be in mountain gorillas? What are modes of dyadic cooperation like alliances described in other species (e.g. alliances between cercopithecine monkey mothers and sisters)? Providing some theoretical justification/context for the existence of benefits that might be enabled by kin selection in mountain gorillas would strengthen the study considerably.

One example of where such a nuanced explanation of both social measures and relationship function was provided well is when the authors interpreted their finding that opposite-sex non-siblings showed heightened rates of aggression compared to opposite-sex siblings and same-sex siblings and same-sex non-siblings. Here, they discussed how an opposite-sex non-sibling relationship is one that has functional importance relevant to reproduction and that increased aggression might represent sexual coercion.