Reviewer #2 (Public review):

Summary:

This study by Dorn et al. from Dr. Henrike Scholz's group investigates the function of serotonin signaling in state-dependent feeding control for protein and sugar intake. Using a dominant-negative serotonin transporter to block serotonin reuptake and optogenetics to activate serotoninergic neurons, the authors identified that serotonin released from a small group of Sert3-expressing neurons specifically reduces sucrose consumption of the fed files but not in the starved flies. Conversely, blocking serotonin reuptake in broad serotonergic neurons increases yeast consumption only in starved flies but does not affect fed flies. These results suggest prolonged serotonin signals may suppress sucrose appetite in fed flies while promoting protein intake in starved flies.

Although the phenotypes presented are intriguing and fundamental to animal fitness, the data in its current form is insufficient to support the proposed mechanisms underlying the state-dependent diet control by serotonin signals. Specifically, the authors should carefully analyze the requirement of serotonin by showing the efficiency of the serotonin reuptake blockade caused by the dominant-negative serotonin and validating the requirement of serotonin in the optogenetic activation of Sert3-expressing neurons. Additionally, the conclusions based on the overexpressed Sert3::gfp transgene should be retrieved as the overexpression affects sucrose consumption. Therefore, I recommend some alternative interpretations and approaches below for authors to verify the current form of conclusions.

Strengths:

The authors identified the state-dependent diet control for sucrose and yeast intake regulated by a restricted population of serotonin neurons expressing Sert3.

Weaknesses:

The data only partially supports most conclusions. Specifically, findings based on the use of the transgene Sert3::GFP lack sufficient rigor, as the authors overlooked potential overexpression effects.

Major issues

(1) The authors try to distinguish the motivation to feed on sucrose or protein in fed or starved conditions using "sucrose appetite" and "protein hunger", respectively. However, appetite and hunger should be synonymous in the current context. When specifying protein hunger, readers will expect the craving for protein in the protein-deprived situation. In the current study, starved flies were prepared by starvation on wet tissues so the flies are supposed to be hungry for sugar and protein. To avoid confusion, "sucrose appetite in fed flies" and "protein appetite in starved flies" are better descriptions.

(2) In Figure 1A-1I (lines 141-142), it remains unclear whether additional serotonergic neurons are required or if the serotonergic neurons labeled exclusively by R50H05-Gal4 and Tph-Gal4 are necessary to regulate yeast consumption in starved flies. The overlapping expressions of these two drivers with the Sert3-Gal4 make it hard to distinguish these two possibilities.

(3) The data in Figure 1L-1M suggests that the serotonin-dependent regulation in yeast consumption of starved flies is suppressed by sucrose supplementation. However, the neurons required for yeast consumption remain undefined due to the overlapping expression. This result implies that the neurons labeled by R50H05-Gal4 and Tph-Gal4 influence both sucrose and yeast consumption but not specific to yeast.

(4) The regulatory relationship between insulin receptors and serotonin signaling in sucrose appetite remains unclear. How do the authors interpret the result that both the constitutively active and dominant-negative forms of the insulin receptor (InR) reduce sucrose appetite in Figure 4? One possibility is that insulin receptors are involved in two parallel pathways to regulate sucrose consumption that converge to the same phenotype. However, the insulin receptor (InR) pathways can still be independent of the serotonin signaling pathway despite showing a comparable reduction of sucrose consumption in fed flies. This issue should be discussed further following lines 229-231.

(5) The quantification of Figure 5 should be revised. First, as the transgene Sert3::GFP affects sucrose consumption, quantifying the transgene signals may not explain its endogenous function. Second, the quantification lacks a Gal4 expression control using an untagged fluorescent marker, preferably a different color so that the authors can quantify it in the same individual as the comparison. Lastly, it is hard to be convinced that the distance between two layers represents the broad expression of Sert3::GFP in response to insulin receptor alterations. Quantifying the area size of each layer with fixed imaging conditions such as the intervals of brain sections and the laser intensity may be a better alternative approach.

(6) The conclusions drawn based on the Sert3::GFP transgene failed to explain the endogenous function of the serotonin transporter Sert3 in regulating sucrose consumption. Expressing the constitutive-active form of the insulin receptor in Sert3-expressing neurons reduces the total sucrose consumption of fed flies in Figure 4A, which appears inconsistent with the fly line with an additional Sert3::GFP expression shown in Figures 6F, where the suppression of sucrose consumption is not shown for the normalized sucrose intake. This inconsistency suggests that Sert3::GFP transgene itself affects sucrose consumption.

(7) In lines 324-326, the authors should investigate whether IR60b neurons are indeed the downstream of serotoninergic neurons SE1 to regulate sucrose consumption in fed flies. First, synaptic connections could be confirmed by additional approaches. Following this, the authors could demonstrate that the knockdown of serotonin receptors in IR60b neurons eliminates the suppression in sucrose consumption induced by the activation of Sert3-expressing neurons or by the expression of the dominant-negative serotonin transporter in fed flies.

Reviewer #2 (Public review):

Summary:

This manuscript reports high-resolution functional MRI data and MEG data revealing additional mechanistic information about an established paradigm studying how foveal regions of the primary visual cortex (V1) are involved in processing peripheral visual stimuli. Because of the retinotopic organization of V1, peripheral stimuli should not evoke responses in the regions of V1 that represent stimuli in the center of the visual field (the fovea). However, functional MRI responses in foveal regions do reflect the characteristics of peripheral visual stimuli - this is a surprising finding first reported in 2008. The present study uses fMRI data with sub-millimeter resolution to study how responses at different depths in the foveal gray matter do or don't reflect peripheral object characteristics during 2 different tasks: one in which observers needed to make detailed judgments about object identity, and one in which observers needed to make more coarse judgments about object orientation. FMRI results reveal interesting and informative patterns in these two conditions. A follow-on MEG study yields information about the timing of these responses. Put together, the findings settle some questions in the field and add new information about the nature of visual feedback to V1.

Strengths:

(1) Rigorous and appropriate use of "laminar fMRI" techniques.

(2) The introduction does an excellent job of contextualizing the work.

(3) Control experiments and analyses are designed and implemented well

Weaknesses:

(1) While not necessarily a weakness, I do not fully agree with the description of the 2 kinds of feedback information as "low-order" and "high-order". I understand the motivation to do this - orientation is typically considered a low-level visual feature. But when it's the orientation of an entire object, not a single edge, orientation can only be defined after the elements of the object are grouped. Also, the discrimination between spikies and smoothies requires detecting the orientations of particular edges that form the identifying features. To my mind, it would make more sense to refer to discrimination of object orientation as "coarse" feature discrimination, and orientation of object identity as "fine" feature discrimination. Thus, the sentence on line 83, for example, would read "Interestingly, feedback with fine and coarse feature information exhibits different laminar profiles.".

(2) Figure 2 and text on lines 185, and 186: it is difficult to interpret/understand the findings in foveal ROIs for the foveal control task without knowing how big the ROI was. Foveal regions of V1 are grossly expanded by cortical magnification, such that the central half-degree can occupy several centimeters across the cortical surface. Without information on the spatial extent of the foveal ROI compared to the object size, we can't know whether the ROI included voxels whose population receptive fields were expected to include the edges of the objects.

(3) Line 143 and ROI section of the methods: in order for the reader to understand how robust the responses and analyses are, voxel counts should be provided for the ROIs that were defined, as well as for the number (fraction) of voxels excluded due to either high beta weights or low signal intensity (lines 505-511).

(4) I wasn't able to find mention of how multiple-comparisons corrections were performed for either the MEG or fMRI data (except for one Holm-Bonferonni correction in Figure S1), so it's unclear whether the reported p-values are corrected.

Reviewer #2 (Public review):

Summary:

This manuscript examined the impact of sulcal morphology on reading development. A very specific feature on the ventral surface of the brain was identified, namely the presence of an interruption in the posterior portion of the left occipitotemporal sulcus (pOTS). Compared to children with a continuous pOTS, children with an interruption at age 5 years had better reading ability at age 8. This was a large effect measured in 43 children. Surprisingly, this morphological feature was a better predictor of reading ability than measures of pre-literacy cognitive skills, such as phonological awareness. The effect was tested and reproduced across several different measures of reading ability. The authors hypothesised that the mechanism underlying this benefit related to greater local connectivity, which confers a computational advantage. This was demonstrated using analysis of diffusion-weighted imaging data in 29 of the children obtained at age 8.

Strengths:

The novelty of the manuscript is threefold: (i) the measure was made in children who were pre-literate (previous work was in older children and adults); (ii) longitudinal brain imaging and behavioural data were analysed; and (iii) diffusion data were analysed to test a hypothesis about the underlying mechanism.

The manuscript is exceptionally well written. The methods are detailed and easily reproduced. The approach is thoughtful and meticulous. All possible alternatives appear to have been considered. Where possible, further analyses have been done to address these alternatives. For example, the testing of the specificity of the sulcal interruption to left pOTS was an important addition. None predicted reading skills.

Weaknesses:

The correlation of the interruption with all kinds of literacy measures and in particular reading comprehension and then PIQ suggest this interruption might confer a more general cognitive advantage rather than specifically a reading one.

It would be interesting to know if the anatomical difference predicts any other cognitive ability or if there might be any cognitive cost (a negative correlation) of this sulcal interruption.<br /> The location of the interruption in the sulcus is quite variable and in some cases, there is more than one interruption. The sample size is probably not big enough to compare these different patterns or to evaluate the influence of the location of the sulcal interruption.

The sample is quite high-functioning and the generalisability of the findings outside of this specific population is inevitably limited.

Reviewer #3 (Public review):

This paper addresses a long-standing problem in microbiology: the evolution of bacterial cell shape. Bacterial cells can take a range of forms, among the most common being rods and spheres. The consensus view is that rods are the ancestral form and spheres the derived form. The molecular machinery governing these different shapes is fairly well understood but the evolutionary drivers responsible for the transition between rods and spheres is not. Enter Yulo et al.'s work. The authors start by noting that deletion of a highly conserved gene called MreB in the Gram-negative bacterium Pseudomonas fluorescens reduces fitness but does not kill the cell (as happens in other species like E. coli and B. subtilis) and causes cells to become spherical rather than their normal rod shape. They then ask whether evolution for 1000 generations restores the rod shape of these cells when propagated in a rich, benign medium.

The answer is no. The evolved lineages recovered fitness by the end of the experiment, growing just as well as the unevolved rod-shaped ancestor, but remained spherical. The authors provide an impressively detailed investigation of the genetic and molecular changes that evolved. Their leading results are:

(1) the loss of fitness associated with MreB deletion causes high variation in cell volume among sibling cells after cell division;<br /> (2) fitness recovery is largely driven by a single, loss-of-function point mutation that evolves within the first ~250 generations that reduces the variability in cell volume among siblings;<br /> (3) the main route to restoring fitness and reducing variability involves loss of function mutations causing a reduction of TPase and peptidoglycan cross-linking, leading to a disorganized cell wall architecture characteristic of spherical cells.

The inferences made in this paper are on the whole well supported by the data. The authors provide a uniquely comprehensive account of how a key genetic change leads to gains in fitness and the spectrum of phenotypes that are impacted and provide insight into the molecular mechanisms underlying models of cell shape.

Suggested improvements and clarifications include:<br /> (1) A schematic of the molecular interactions governing cell wall formation could be useful in the introduction to help orient readers less familiar with the current state of knowledge and key molecular players;<br /> (2) It remains unclear whether corrections for multiple comparisons are needed when more than one construct or strain is compared to the common ancestor, as in Supp Fig 19A (relative PG density of different constructs versus the SBW25 ancestor). The author's response did not clarify matters: was data for the WT obtained independently alongside each each strain/construct (justifying a paired t-test) or was a single set of data for the WT obtained and used to compare against all other strains/constructs (which would demand a correction for multiple comparisons)?<br /> (3) The authors refrain from making strong claims about the nature of selection on cell shape, perhaps because their main interest is the molecular mechanisms responsible. They identify sources of stabilizing selection favouring an intermediate cell size (lack of DNA in small cells and disorganized DNA in large cells). Their interpretation of stabilizing selection in the review is correct and entirely consistent with the mechanistic causes identified here. I think this is valuable and interesting, although I recognize it is not the focus of the paper.

Comments on revisions:

Please further clarify the experimental design and replication for the contrast between mutants and WT to address the issue of multiple comparisons.

Reviewer #2 (Public review):

Summary:

This study evaluated the aperiodic component in the medial prefrontal cortex (mPFC) using resting-state EEG recordings from 149 individuals with chronic pain and 115 healthy participants. The findings showed no significant differences in the aperiodic component of the mPFC between the two groups, nor was there any correlation between the aperiodic component and pain intensity. These results were consistent across various chronic pain subtypes and were corroborated by whole-brain analyses. The study's robustness was further reinforced by preregistration and multiverse analyses, which accounted for a wide range of methodological choices.

Strengths:

This study was rigorously conducted, yielding clear and conclusive results. Furthermore, it adhered to stringent open and reproducible science practices, including preregistration, blinded data analysis, and Bayesian hypothesis testing. All data and code have been made openly available, underscoring the study's commitment to transparency and reproducibility.

Weaknesses:

The aperiodic exponent of the EEG power spectrum is often regarded as an indicator of the excitatory/inhibitory (E/I) balance. However, this measure may not be the most accurate or optimal for quantifying E/I balance, a limitation that the authors might consider addressing in the future.

Comments on revisions:

All my comments have been well addressed.

Reviewer #2 (Public review):

Summary:

Bloch et al. studied the relationships between aerial foragers (lesser swifts) tracked using an automated radio telemetry system (Atlas) and their prey (flying insects) monitored using a small vertical-looking radar (BirdScan MR1). The aim of the study was to check whether swifts optimise their foraging according to the abundance of their prey. The results provide evidence that small swifts can increase their foraging rate when aerial insect abundance is high, but found no correlation between insect abundance and flight energy expenditure.

Key points:

This study fills gaps in fundamental knowledge of prey-predator dynamics in the air. It describes the coincidence between the abundance of flying insects and the characteristics derived from monitoring individual swifts.

Weaknesses:

The paper uses assumptions largely derived from optimal foraging theory, but mixes up the form of natural selection: parental energy, parental survival (predation risk), nestling foraging and reproductive success. The results are partly inconsistent, and confounding factors (e.g., the brooding phase versus the nestling phase) remained ignored. In conclusion, the analyses performed are insufficient to rigorously assess whether lesser swifts are optimising their foraging beyond making shorter foraging trips.<br /> The filters applied to the monitoring data are necessary but may strongly influence the characteristics derived based on maximum or mean values. Sensitivity tests or the use of characteristics that are less dependent on extreme values could provide more robust results.

Reviewer #2 (Public review):

Summary:

This theoretical paper examines genetic drift in scenarios deviating from the standard Wright-Fisher model. The authors discuss Haldane's branching process model, highlighting that the variance in reproductive success equates to genetic drift. By integrating the Wright-Fisher model with the Haldane model, the authors derive theoretical results that resolve paradoxes related to effective population size.

Strengths:

The most significant and compelling result from this paper is perhaps that the probability of fixing a new beneficial mutation is 2s/V(K). This is an intriguing and potentially generalizable discovery that could be applied to many different study systems.

The authors also made a lot of effort to connect theory with various real-world examples, such as genetic diversity in sex chromosomes and reproductive variance across different species.

Comments on revisions:

The author has addressed some of the concerns in my review, and I think the revised manuscript is more clear. I like the discussion about the caveats of the WFH model.

I hope the authors could also discuss the conditions needed for V(K)/Ne to be a reasonable approximation. It is currently unclear how the framework should be adopted in general.

The idea about estimating male-female V(K) ratios from population genetic data is interesting. Unfortunately, the results fell short. The accuracy of their estimators (derived using approximation Ne/V(K) approximation, and certain choice of theta, and then theta estimated with Watterson's estimator) should be tested with simulated results before applying to real data. The reliability of their estimator and their results from real data are unclear.

Arguments made in this paper sometimes lack precision (perhaps the authors want to emphasize intuition, but it seems more confusing than otherwise). For example: The authors stated that "This independence from N seems intuitively obvious: when an advantageous mutation increases to say, 100 copies in determining a population (depending mainly on s), its fixation would be almost certain, regardless of N.". Assuming large Ne, and with approximation, one could assume the probability of loss is e^(-2sn), but the writing about "100 copies" and "almost certain" is very imprecise, in fact, a mutation with s=0.001 segregating at 100 copies in a large Ne population is most probably lost. Whereas in a small population, it will be fixed. Yet the following sentence states "regardless of N. This may be a most direct argument against equating genetic drift, certainly no less important than 1/ N . with N, or Ne (which is supposed to be a function of N's)." I find this new paragraph misleading.

Some of the statements/wordings in this paper still seem too strong to me.

Reviewer #2 (Public review):

Summary:

In this paper, Lin and colleagues aim to understand the role of different salts on the phase behavior of a model protein of significant biological interest, Caprin1, and its phosphorylated variant, pY-Caprin1. To achieve this, the authors employed a variety of methods to complement experimental studies and obtain a molecular-level understanding of ion partitioning inside biomolecular condensates. A simple theory based on rG-RPA is shown to capture the different salt dependencies of Caprin1 and pY-Caprin1 phase separation, demonstrating excellent agreement with experimental results. The application of this theory to multivalent ions reveals many interesting features with the help of multicomponent phase diagrams. Additionally, the use of CG model-based MD simulations and FTS provides further clarity on how counterions can stabilize condensed phases.

Strengths:

The greatest strength of this study lies in the integration of various methods to obtain complementary information on thermodynamic phase diagrams and the molecular details of the phase separation process. The authors have also extended their previously proposed theoretical approaches, which should be of significant interest to other researchers. Some of the findings reported in this paper, such as bridging interactions, are likely to inspire new studies using higher-resolution atomistic MD simulations.

Reviewer #2 (Public review):

Summary:

This is a well written manuscript describing studies directed at identifying the cell type responsible for pacemaking in murine collecting lymphatics. Using state-of-the-art approaches, the authors identified a number of different cell types in the wall of these lymphatics and then using targeted expression of Channel Rhodopsin and GCaMP, the authors convincingly demonstrate that only activation of lymphatic muscle cells produces coordinated lymphatic contraction and that only lymphatic muscle cells display pressure-dependent Ca2+ transients as would be expected of a pacemaker in these lymphatics.

Strengths:

The use of targeted expression of channel rhodopsin and GCaMP to test the hypothesis that lymphatic muscle cells serve as the pacemakers in musing lymphatic collecting vessels.

Weaknesses:

The only significant weakness was the lack of quantitative analysis of most of the imaging data shown in Figures 1-11. In particular, the colonization analysis should be extended to show cells not expected to demonstrate colocalization as a negative control for the colocalization analysis that the authors present. These weaknesses have been resolved by revision and addition of new and novel RNAseq data, additional colocalization data and membrane potential measurements.

Reviewer #2 (Public Review):

Summary:

In this work, the authors combine diffusion MRI and high-resolution x-ray synchrotron phase-contrast imaging in monkey and mouse brains to investigate the 3D organization of brain white matter across different scales and species. The work is at the forefront of the anatomical investigation of the human connectome and aligns with several current efforts to bridge the resolution gap between what we can see in vivo at the millimeter scale and the complexity of the human brain at the sub-micron scale. The authors compare the 3D white matter organization across modalities within 2 small regions in one monkey brain (body of the corpus callosum, centrum semiovale) and within one region (splenium of the corpus callosum) in healthy mice and in one murine model of focal demyelination. The study compares measures of tissue anisotropy and fiber orientations across modalities, performs a qualitative comparison of fasciculi trajectories across brain regions and tissue conditions using streamlined tractography based on the structure tensor, and attempts to quantify the shape of fasciculi trajectories by measuring the tortuosity index and the maximum deviation for each reconstructed streamline. Results show measures of anisotropy and fiber orientations largely agree across modalities, especially for larger FOV data. The high-resolution data allows us to explore the fiber trajectories in relation to tissue complexity and pathology. The authors claim the study reveals new common organization principles of white matter fibers across species and scales, for which axonal fasciculi arrange into sheet-like laminar structures.

Strengths:

The aim of the study is of central importance within present efforts to bridge the gap between macroscopic structures observable in vivo in humans using conventional diffusion MRI and the microscopic organization of white matter tissue. Results obtained from this type of study are important to interpret data obtained in vivo, inform the development of novel methodologies, and expand our knowledge of the structural and thus functional organization of brain circuits.

Multi-scale data acquired across modalities within the same sample constitute extremely valuable data that is often hard to acquire and represent a precious resource for validation of both diffusion MRI tractography and microstructure methods.

The inclusion of multi-species data adds value to the study, allowing the exploration of common organization principles across species.

The addition of data from a murine cuprizone model of focal demyelination adds interesting opportunities to study the underlying biological changes that follow demyelination and how these impact tissue anisotropy and fiber trajectories. These data can inform the interpretation and development of diffusion MRI microstructure models.

[Editors' note: The Reviewing Editor considers that the authors addressed the reviewers' questions adequately. The original reviews are here: https://elifesciences.org/reviewed-preprints/94917/reviews]

Reviewer #2 (Public review):

Summary:

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

Comments on revisions:

The authors should be commended for being very responsive to comments and providing several further requested analyses, which have improved the paper. However, there is still some outstanding issues that make it difficult to fully support the provided interpretation.

The authors say within the response, "We would also like to stress that these perturbations were not designed so that responses are directly compared to each other ***(though of course there is an *indirect* comparison in the sense that we show influence of biases in one type of perturbation but not the other)***." They then state in the first paragraph of the discussion that "Remarkably, these resting postural force biases did not seem to have a detectable effect upon any component of active reaching but only emerged during the control of holding still after the movement ended. The results suggest a dissociation between the control of movement and posture." The main issue here is relying on indirect comparisons (i.e., significant in one situation but not the other), instead of relying on direct comparisons. Using well-known example, just because one group / condition might display a significant linear relationship (i.e., slope_1 > 0) and another group / condition does not (slope_2 = 0), does not necessarily mean that the two groups / conditions are statistically different from one another [see Figure 1 in Makin, T. R., & Orban de Xivry, J. J. (2019). Ten common statistical mistakes to watch out for when writing or reviewing a manuscript. eLife, 8, e48175.].

The authors have provided reasonable rationale of why they chose certain perturbation waveforms for different. Yet it still holds that these different waveforms would likely yield very different muscular responses making it difficult to interpret the results and this remains a limitation. From the paper it is unknown how these different perturbations would differentially influence a variety of classic neuromuscular responses, including short-range stiffness and stretch reflexes, which would be at play here.

Much of the results can be interpreted when one considers classic neuromuscular physiology. In Experiment 1, differences in resting postural bias in supported versus unsupported conditions can readily be explained since there is greater muscle activity in the unsupported condition that leads to greater muscle stiffness to resist mechanical perturbations (Rack, P. M., & Westbury, D. R. (1974). The short-range stiffness of active mammalian muscle and its effect on mechanical properties. The Journal of physiology, 240(2), 331-350.). Likewise muscle stiffness would scale with changes in muscle contraction with synergies. Importantly for experiment 2, muscle stiffness is reduced during movement (Rack and Westbury, 1974) which may explain why resting postural biases do not seem to be impacting movement. Likewise, muscle spindle activity is shown to scale with extrafusal muscle fiber activity and forces acting through the tendon (Blum, K. P., Campbell, K. S., Horslen, B. C., Nardelli, P., Housley, S. N., Cope, T. C., & Ting, L. H. (2020). Diverse and complex muscle spindle afferent firing properties emerge from multiscale muscle mechanics. eLife, 9, e55177.). The concern here is that the authors have not sufficiently considered muscle neurophysiology, how that might relate to their findings, and how that might impact their interpretation. Given the differences in perturbations and muscle states at different phases, the concern is that it is not possible to disentangle whether the results are due to classic neurophysiology, the hypothesis they propose, or both. Can the authors please comment.

The authors should provide a limitations paragraph. They should address 1) how they used different perturbation force profiles, 2) the muscles were in different states which would change neuromuscular responses between trial phase / condition, 3) discuss a lack of direct statistical comparisons that support their hypothesis, and 4) provide a couple of paragraphs on classic neurophysiology, such as muscle stiffness and stretch reflexes, and how these various factors could influence the findings (i.e., whether they can disentangle whether the reported results are due to classic neurophysiology, the hypothesis they propose, or both).

Reviewer #2 (Public review):

Summary:

The paper describes an effort to identify the factors responsible for intron retention and alternate exon splicing in a complex system known to be regulated by the O-GlcNAc cycling system. The CRISPR/Cas9 system was used to identify potential factors. The bioinformatic analysis is sophisticated and compelling. The conclusions are of general interest and advance the field significantly.

Strengths:

(1) Exhaustive analysis of potential splicing factors in an unbiased screen.

(2) Extensive genome wide bioinformatic analysis.

(3) Thoughtful discussion and literature survey.

Weaknesses:

(1) No firm evidence linking SFSWA to an O-GlcNAc specific mechanism.

(2) Resulting model leaves many unanswered questions.

Reviewer #2 (Public review):

Summary:

The authors generated three mouse lines harboring ASD, Schizophrenia, and Bipolar-associated variants in the TRIO gene. Anatomical, behavioral, physiological, and biochemical assays were deployed to compare and contrast the impact of these mutations in these animals. In this undertaking, the authors sought to identify and characterize the cellular and molecular mechanisms responsible for ASD, Schizophrenia, and Bipolar disorder development.

Strengths:

The establishment of TRIO dysfunction in the development of ASD, Schizophrenia, and Bipolar disorder is very recent and of great interest. Disorder-specific variants have been identified in the TRIO gene, and this study is the first to compare and contrast the impact of these variants in vivo in preclinical models. The impact of these mutations was carefully examined using an impressive host of methods. The authors achieved their goal of identifying behavioral, physiological, and molecular alterations that are disorder/variant specific. The impact of this work is extremely high given the growing appreciation of TRIO dysfunction in a large number of brain-related disorders. This work is very interesting in that it begins to identify the unique and subtle ways brain function is altered in ASD, Schizophrenia, and Bipolar disorder.

Weaknesses:

(1) Most assays were performed in older animals and perhaps only capture alterations that result from homeostatic changes resulting from prodromal pathology that may look very different.

(2) Identification of upregulated (potentially compensating) genes in response to these disorder-specific Trio variants is extremely interesting. However, a functional demonstration of compensation is not provided.

(3) There are instances where data is not shown in the manuscript. See "data not shown". All data collected should be provided even if significant differences are not observed.

I consider weaknesses 1 and 2 minor. While they would very interesting to explore, these experiments might be more appropriate for a follow-up study. I would recommend that the missing data in 3 should be provided in the supplemental material.

Reviewer #2 (Public review):

Summary:<br /> The authors use a genetic screen in C. elegans to investigate the physiological roles of polyunsaturated fatty acids (PUFAs). They screen for mutations that rescue fat-2 mutants, which have strong reductions in PUFAs. As a result, either mutations in fat-2 itself, or mutations in genes involved in the HIF-1 pathway, were found to rescue fat-2 mutants.

Strengths:<br /> As C. elegans can produce PUFAs de novo as essential lipids, the genetic model is well suited to study the fundamental roles of PUFAs, and the results are very interesting. The genetic screen finds mutations in convergent pathways, suggesting that it has reached near-saturation. The link between the HIF-1 pathway and lipid unsaturation is very interesting. As many of the mutations found to rescue fat-2 mutants are of gain-of-function, it is unlikely that similar discoveries could have been made with other approaches like genome-wide CRISPR screenings, making the current study distinctive.

Weaknesses:<br /> The authors make very important statements, but some are not sufficiently supported by data. In page 5, they conclude that membrane rigidity is a minor cause of fat-2 mutant defects, which is a relevant observation regarding why PUFAs are important. However, they use treatments that have rescued fluidity in another mutant (paqr-2), but do not test if they have the same fluidifying effects in fat-2 mutants.

The screening results seem to converge into the HIF-1 pathway, which is hypothetically correct according to the literature. However, the authors do not validate this hypothesis, which is a critical limitation, especially because many of the mutations they obtained seem to be of gain-of-function. Therefore, without experimental testing, it cannot be concluded that the mutations have the expected effect on the HIF-1 pathway.

In some of the mutants, the rescues in lipid compositions seem to be weak, and it is arguable whether phenotypic rescues are really via a restoration in lipid compositions.

The hypothesis linking iron homeostasis and the rescue of fat-2 mutants is interesting, but the data of rescue by iron repletion seem to be against it. The results might be due to the inefficiency in iron repletion, as the authors suggest, but this has not been formally addressed.

Therefore, the authors propose multiple very interesting and important hypotheses, but experimental validations remain limited.

Reviewer #2 (Public review):

Summary:

In this work, the authors wish to explore the metabolic support mechanisms enabling lamellocyte encapsulation, a critical antiparasitic immune response of insects. They show that S-adenosylmethionine metabolism is specifically important in this process through a combination of measurements of metabolite levels and genetic manipulations of this metabolic process.

Strengths:

The metabolite measurements and the functional analyses are generally very strong and clearly show that the metabolic process under study is important in lamellocyte immune function.

Weaknesses:

The gene expression data are a potential weakness. Not enough is explained about how the RNAseq experiments in Figures 2 and 4 were done, and the representation of the data is unclear. The paper would also be strengthened by the inclusion of some measure of encapsulation effectiveness: the authors show that manipulation of the S-adenosylmethionine pathway in lamellocytes affects the ability of the host to survive infection, but they do not show direct effects on the ability of the host to encapsulate wasp eggs.

Reviewer #2 (Public review):

Summary:

In this study, the authors hypothesize that "causal inferences about illness depend on content-specific semantic representations in the animacy network". They test this hypothesis in an fMRI task, by comparing brain activity elicited by participants' exposure to written situations suggesting a plausible cause of illness with brain activity in linguistically equivalent situations suggesting a plausible cause of mechanical failure or damage and non-causal situations. These contrasts identify PC as the main "culprit" in a whole-brain univariate analysis. Then the question arises of whether the content-specificity has to do with inferences about animates in general, or if there are some distinctions between reasoning about people's bodies versus mental states. To answer this question, the authors localize the mentalizing network and study the relation between brain activity elicited by Illness-Causal > Mech-Causal and Mentalizing > Physical stories. They conclude that inferring about the causes of illness partially differentiates from reasoning about people's states of mind. The authors finally test the alternative yet non-mutually exclusive hypothesis that both types of causal inferences (illness and mechanical) depend on shared neural machinery. Good candidates are language and logic, which justifies the use of a language/logic localizer. No evidence of commonalities across causal inferences versus non-causal situations is found.

Strengths:

(1) This study introduces a useful paradigm and well-designed set of stimuli to test for implicit causal inferences.

(2) Another important methodological advance is the addition of physical stories to the original mentalizing protocol.

(3) With these tools, or a variant of these tools, this study has the potential to pave the way for further investigation of naïve biology and causal inference.

Weaknesses:

(1) This study is missing a big-picture question. It is not clear whether the authors investigate the neural correlates of causal reasoning or of naïve biology. If the former, the choice of an orthogonal task, making causal reasoning implicit, is questionable. If the latter, the choice of mechanical and physical controls can be seen as reductive and problematic.

(2) The rationale for focusing mostly on the precuneus is not clear and this choice could almost be seen as a post-hoc hypothesis.

(3) The choice of an orthogonal 'magic detection' task has three problematic consequences in this study:<br /> (a) It differs in nature from the 'mentalizing' task that consists of evaluating a character's beliefs explicitly from the corresponding story, which complicates the study of the relation between both tasks. While the authors do not compare both tasks directly, it is unclear to what extent this intrinsic difference between implicit versus explicit judgments of people's body versus mental states could influence the results.<br /> (b) The extent to which the failure to find shared neural machinery between both types of inferences (illness and mechanical) can be attributed to the implicit character of the task is not clear.<br /> (c) The introduction of a category of non-interest that contains only 36 trials compared to 38 trials for all four categories of interest creates a design imbalance.

(4) Another imbalance is present in the design of this study: the number of trials per category is not the same in each run of the main task. This imbalance does not seem to be accounted for in the 1st-level GLM and renders a bit problematic the subsequent use of MVPA.

(5) The main claim of the authors, encapsulated by the title of the present manuscript, is not tested directly. While the authors included in their protocol independent localizers for mentalizing, language, and logic, they did not include an independent localizer for "animacy". As such, they cannot provide a within-subject evaluation of their claim, which is entirely based on the presence of a partial overlap in PC (which is also involved in a wide range of tasks) with previous results on animacy.

Reviewer #2 (Public review):

I must note that my comments pertain to the evolutionary interpretations rather than the study's technical results. The techniques appear to be appropriately applied and interpreted, but I do not feel sufficiently qualified to assess this aspect of the work in detail.

I was repeatedly puzzled by the use of the term "function." Part of the issue may stem from slightly different interpretations of this word in different fields. In my understanding, "function" should denote not just what a structure does, but what it has been selected for. In this context, where it is unclear if cfChPs have been selected for in any way, the use of this term seems questionable.

Similarly, the term "predatory genome," used in the title and throughout the paper, appears ambiguous and unjustified. At this stage, I am unconvinced that cfChPs provide any evolutionary advantage to the genome. It is entirely possible that these structures have no function whatsoever and could simply be byproducts of other processes. The findings presented in this study do not rule out this neutral hypothesis. Alternatively, some particular components of the genome could be driving the process and may have been selected to do so. This brings us to the hypothesis that cfChPs could serve as vehicles for transposable elements. While speculative, this idea seems to be compatible with the study's findings and merits further exploration.

I also found some elements of the discussion unclear and speculative, particularly the final section on the evolution of mammals. If the intention is simply to highlight the evolutionary impact of horizontal transfer of transposable elements (e.g., as a source of new mutations), this should be explicitly stated. In any case, this part of the discussion requires further clarification and justification.

In summary, this study presents important new findings on the behavior of cfChPs when introduced into a foreign cellular context. However, it overextends its evolutionary interpretations, often in an unclear and speculative manner. The concept of the "predatory genome" should be better defined and justified or removed altogether. Conversely, the suggestion that cfChPs may function at the level of transposable elements (rather than the entire genome or organism) could be given more emphasis.

Reviewer #2 (Public review):

This article elucidates the biochemical and cellular mechanisms by which the FHOD-family of formins, particularly FHOD3, contributes to sarcomere formation and contractility in cardiomyocytes. Formins are mainly known to nucleate and elongate actin filaments, with certain family members also exhibiting capping, severing, and bundling activities. Although FHOD3 has been well-established as essential for sarcomere assembly in cardiomyocytes, its precise biochemical functions and contributions to actin dynamics remain poorly understood.

In this study, the authors combine in vitro biochemical assays with cellular experiments to dissect FHOD3's roles in actin assembly and sarcomere formation. They demonstrate that FHOD3 nucleates actin filaments and acts as a transient elongator, pausing elongation after an initial burst of filament growth. Using separation-of-function mutants, they show that FHOD3's elongation activity - rather than its nucleation, capping, or bundling capabilities - is key for its sarcomeric function.

The experiments have been conducted rigorously and well-analyzed, and the paper is clearly written. The data presented support the authors' conclusions. I appreciate the detailed description and rationale behind the FHOD3 constructs used in this study.

However, I was somewhat surprised and a bit disappointed that while the authors conducted single-color TIRF experiments to observe the effects of FHOD3 on single filaments, they did not use fluorescently labeled FHOD3 to directly visualize its behavior. Incorporating such experiments would significantly strengthen their conclusions regarding FHOD3's bursts of elongation interspersed with capping activity. While I understand this might require a few additional weeks of experiments, these data would add considerable value by directly testing the proposed mechanism.

There is a typo in the word "required" in line number 30. The authors also use fit data to extract parameters in several panels (e.g., Figures 2b, 2d, 3a, and 3b). While these fit functions may be intuitive to actin experts, explicitly describing the fit functions in the figure legends or methods would greatly benefit the broader readership.

Reviewer #2 (Public review):

Seguchi and Izawa provide robust evidence for the role of vasopressin in modulating same-sex affiliative relationships. Especially striking is that these effects appear to be selective to key relationships within a triadic social context. Overall, this is an interesting and rich dataset with compelling results. I largely have some clarifying questions.

Experiment 1 Comments:

(1) The primary argument/finding in this experiment is that a triadic situation/environment facilitates the development of male-male reciprocal social relationships. Overall, this effect appears striking in that male-male affiliative bonds (defined as reciprocal allopreening) formed in 6 of the 8 triads tested. However, there is no comparison group of dyads to determine whether co-housing for 2 weeks could also support the formation of male-male social bonds. This lack of a comparison group makes it unclear to what extent the triad is the key aspect of the environment that supports social bonding.

(2) More specifically, the authors argue that it is not just that triads support affiliative male-male bonds, but that bonds form between the second "middle" (dominant/subordinate) and third "low" (subordinate/subordinate) individuals in each triad. However, it was difficult to assess this from the results.<br /> a) For example, in Figure 3B is each data point the average of two individuals, since in each triad there are two dominant and two subordinate individuals?<br /> b) For me, using more precise language beyond dominant and subordinate (e.g. middle and low), and more clearly displaying the results of allopreening for each pairwise dyad within a triad would improve the impact of the results and support the authors' argument.

(3) Experiment 2 Comments:<br /> The results here are quite striking, despite the low sample size. In Figure 4, it appears that in every instance of administration V1aRA low and high administration decreased allopreening for both dominant and subordinate individuals.

(4) Some methodological questions:<br /> a) Can you clarify whether the duration of the post-test was also 30 min?<br /> b) As in Experiment 1, how are individual birds represented in the triad? Was the second "Middle" bird (dominant/subordinate) tested as both a dominant and subordinate bird? My understanding is that the dominant and subordinate birds in Figure 4 are different individuals but that they are the same individuals represented between the affiliated dyad and unaffiliated dyad.

(5) Throughout the manuscript (Lines 57-67; 557-566) the authors argue that the role of VP in regulating gregariousness can be extrapolated to understand the role of same-sex affiliative bonding. Importantly, gregariousness does not necessarily reflect affiliative bonding. While allopreening is specifically associated with social bonding (e.g. monogamous pair bonds) independent of broader social systems, gregariousness in general, and specifically as defined in many of the references cited, is independent of social bonds - in fact, it is assessed primarily in novel social contexts.

(6) To clarify, adult prairie voles in the wild do not engage in same-sex affiliative behavior commonly. In fact one of the primary components of opposite-sex pair bonding is same-sex aggression. Thus, while mechanistic studies on the neurobiology of same-sex peer bonds are relevant for this work, I am less convinced that you can make comparisons between the ultimate function of same-sex affiliative relationships in prairie voles.

(17) The results here are consistent with VP having an anxiolytic effect, as has been suggested in birds, with the consequences on social behaviors being directly or indirectly related. This may be a useful point to draw on in the discussion when considering your findings.

Reviewer #2 (Public review):

Summary:

This study examines a novel role of the Hpo signaling pathway, specifically of wts-1/LATS and the downstream regulator of gene expression, yap, in age-related neurodegeneration in C. elegans touch-responsive mechanosensory neurons, ALM and PLM. The study shows that knockdown or deletion of wts-1/LATS causes age-associated morphological abnormalities of these neurons, accompanied by functional loss of touch responsiveness. This is further associated with enhanced, abnormal, microtubule stabilization in these neurons.

Strengths:

This study examines a novel role of the Hpo signaling pathway, specifically of wts-1/LATS and the downstream regulator of gene expression, yap, in age-related neurodegeneration in C. elegans touch-responsive mechanosensory neurons, ALM and PLM. The study shows that knockdown or deletion of wts-1/LATS causes age-associated morphological abnormalities of these neurons, accompanied by functional loss of touch responsiveness. This is further associated with enhanced, abnormal, microtubule stabilization in these neurons. Strong pharmacological and especially genetic manipulations of MT-stabilizing or severing proteins show a strong genetic link between yap and regulation of MTs stability. The study is strong and uses robust approaches, especially strong genetics. The demonstrations on the aging-related roles of the Hpo signaling pathway, and the link to MTs, are novel and compelling. Nevertheless, the study also has mechanistic weaknesses (see below).

Weaknesses:

Specific comments:

(1) The study demonstrates age-specific roles of the Hpo pathway, specifically of wts-1/LATS and yap, specifically in TRN mechanosensory neurons, without observing developmental defects in these neurons, or effects in other neurons. This is a strong demonstration. Nevertheless, the study does not address whether there is a correlation of Hpo signaling pathway activity decline specifically in these neurons, and not other neurons, and at the observed L4 stage and onwards (including the first day of adulthood, 1DA stage). Such demonstrations of spatio-temporal regulation of the Hpo signaling pathway and its activation seem important for linking the Hpo pathway with the observed age-related neurodegeneration. Can this age-related response be correlated to indeed a decline in Hpo signaling during adulthood? Especially at L4 and onwards? It will be informative to measure this by examining the decline in wts1 as well as yap levels and yap nuclear localization.

(2) The Hpo pathway eventually activates gene expression via yap. Although the study uses robust genetic manipulations of yap and wts-1/LATS, it is not clear whether the observed effects are attributed to yap-mediated regulation of gene expression (see 3).

(3) The observations on the abnormal MT stabilization, and the subsequent genetic examinations of MT-stability/severing genes, are a significant strength of the study. Nevertheless, despite the strong genetic links to yap and wts-1/LATS, it is not clear whether MT-regulatory genes are regulated by transcription downstream of the Hpo pathway, thus not enabling a strong causal link between MT regulation and Hpo-mediated gene expression, making this strong part of the study mechanistically circumstantial. Specifically, it will be good to examine whether the genes addressed herein, for example, Spastin, are transcriptionally regulated downstream of the Hpo pathway. This comment is augmented by the finding that in the wts-1/ yap-1 double mutants, MT abnormality, and subsequent neuronal morphology and touch responses are restored, clearly indicating that there is an associated transcriptional regulation

Other comments:

(1) The TRN-specific knockdown of wts-1 and yap-1 is a clear strength. Nevertheless, these do not necessarily show cell-autonomous effects, as the yap transcription factor may regulate the expression of external cues, secreted or otherwise, thus generating non-cell autonomous effects. For example, it is known that yap regulates TGF-beat expression and signaling.

(2) Continuing from comment (3) above, it seems that many of the MT-regulators chosen here for genetic examinations were chosen based on demonstrated roles in neurodegeneration in other studies. It would be good to show whether these MT-associated genes are directly regulated by transcription by the Hpo pathway.

(3) The impairment of the touch response may not be robust: it is only a 30-40% reduction at L4, and even less reduction at 1DA. It would be good to offer possible explanations for this finding.

Reviewer #2 (Public Review):

-Summary of the Authors' Aims:<br /> The authors aimed to investigate the role of calcitonin gene-related peptide (CGRP) neurons in the parabrachial nucleus (PBN) in modulating defensive behaviors in response to threats. They sought to determine whether these neurons, previously shown to be involved in passive freezing behavior, also play a role in active defensive behaviors, such as fleeing, when faced with imminent threats.

-Major Strengths and Weaknesses of the Methods and Results:<br /> The authors utilized an innovative approach by employing a predator-like robot to create a naturalistic threat scenario. This method allowed for a detailed observation of both passive and active defensive behaviors in mice. The combination of electrophysiology, optogenetics, and behavioral analysis provided a comprehensive examination of CGRP neuron activity and its influence on defensive behaviors. The study's strengths lie in its robust methodology, clear results, and the multi-faceted approach that enhances the validity of the findings.

No notable weakness found.

-Appraisal of Aims and Results:<br /> The authors successfully achieved their aims by demonstrating that CGRP neurons in the PBN modulate both passive and active defensive behaviors. The results clearly show that activation of these neurons enhances fear memory and promotes conditioned fleeing behavior, while inhibition reduces these responses. The study provides strong evidence supporting the hypothesis that CGRP neurons act as a comprehensive alarm system in the brain.

-Impact on the Field and Utility of Methods and Data:<br /> This work has significant implications for the field of neuroscience, particularly in understanding the neural mechanisms underlying adaptive defensive behaviors. The innovative use of a predator-like robot to simulate naturalistic threats adds ecological validity to the findings and may inspire future studies to adopt similar approaches. The comprehensive analysis of CGRP neuron activity and its role in defensive behaviors provides valuable data that could be useful for researchers studying fear conditioning, neural circuitry, and behavior modulation.

-Additional Context:<br /> The study builds on previous research that primarily focused on the role of CGRP neurons in passive defensive responses, such as freezing. By extending this research to include active responses, the authors have provided a more complete picture of the role of these neurons in threat detection and response. The findings highlight the versatility of CGRP neurons in modulating different types of defensive behaviors based on the perceived intensity and immediacy of threats.

Overall, this manuscript makes a significant contribution to our understanding of the neural basis of defensive behaviors and offers valuable methodological insights for future research in the field.

Reviewer #2 (Public review):

Summary:

Luo et. al. use SHAPE-MaP to find suitable RNA targets in Porcine Epidemic Diarrhoea Virus. Results show that dynamic and transient structures are good targets for small molecules, and that exposed strand regions are adequate targets for siRNA. This work is important to segment the RNA targeting.

Strengths:

This work is well done and the data supports its findings and conclusions. When possible, more than one technique was used to confirm some of the findings.

Weaknesses:

The study uses a cell line that is not porcine (not the natural target of the virus).

Reviewer #2 (Public review):

Summary:

RNAs can function across cell borders and animal generations as sources of epigenetic information for development and immunity. The specific mechanistic pathways how RNA travels between cells and progeny remains an open question. Here, Shugarts, et al. use molecular genetics, imaging, and genomics methods to dissect specific RNA transport and regulatory pathways in the C. elegans model system. Larvae ingesting double-stranded RNA is noted to not cause continuous gene silencing throughout adulthood. Damage of neuronal cells expressing double-stranded target RNA is observed to repress target gene expression in the germline. Exogenous short or long double-stranded RNA required different genes for entry into progeny. It was observed that the SID-1 double-stranded RNA transporter showed different expression over animal development. Removal of the sid-1 gene caused upregulation of two genes, the newly described sid-1-dependent gene sdg-1 and sdg-2. Both genes were observed to be negatively regulated by other small RNA regulatory pathways. Strikingly, loss then gain of sid-1 through breeding still caused variability of sdg-1 expression for many, many generations. SDG-2 protein co-localizes with germ granules, intracellular sites for heritable RNA silencing machinery. Collectively, sdg-1 presents a model to study how extracellular RNAs can buffer gene expression in germ cells and other tissues.

Strengths:

(1) Very cleaver molecular genetic methods and genomic analyses, paired with thorough genetics, were employed to discover insights into RNA transport, sdg-1 and sdg-2 as sid-1-dependent genes, and sdg-1's molecular phenotype.

(2) The manuscript is well cited, and figures reasonably designed.

(3) The discovery of the sdg genes being responsive to the extracellular RNA cell import machinery provides a model to study how exogenous somatic RNA is used to regulate gene expression in progeny. The discovery of genes within retrotransposons stimulates tantalizing models how regulatory loops may actually permit the genetic survival of harmful elements.

Weaknesses:

(1) The manuscript is broad, making it challenging to read and consider the data presented. Of note, since the original submission, the authors have improved the clarity of the writing and presentation.

Comments on revised version:

This reviewer thanks the authors for their efforts in revising the manuscript. In their rebuttal, the authors acknowledged the broad scope of their manuscript. I concur. While I still think the manuscript is a challenge to read due to its expansive nature, the current draft is substantially improved when compared to the previous one. This work will contribute to our general knowledge of RNA biology, small RNA regulatory pathways, and RNA inheritance.

Reviewer #2 (Public review):

Summary:

The authors describe elevated GSDMD expression in psoriatic skin, and knock-out of GSDMD abrogates psoriasis-like inflammation.

Strengths:

The study is well conducted with transgenic mouse models. Using mouse-models with GSDMD knock-out showing abrogating inflammation, as well as GSDMD fl/fl mice without neutrophils having a reduced phenotype.

My major concern would be the involvement of other inflammasome and GSDMD bearing cell types, esp. Keratinocytes (KC), which could be an explanation why the experiments in Fig 4 still show inflammation.

Comments on revisions:

The authors have sufficiently addressed my questions.

Reviewer #2 (Public review):

Summary:

Unlike previous traditional protein fusion protocols, the author claims their proposed new method is fast, simple, specific, reversible, and results in a complete 1:1 fusion. A multi-disciplinary approach from cloning and purification, biochemical analyses, and proteomic mass spec confirmation revealed fusion products were achieved.

Strengths:

The author provides convincing evidence that an alternative to traditional protein fusion synthesis is more efficient with 100% yields using connectase. The author optimized the protocol's efficiency with assays replacing a single amino acid and identification of a proline aminopeptidase, Bacilius coagulans (BcPAP), as a usable enzyme to use in the fusion reaction. Multiple examples including Ubiquitin, GST, and antibody fusion/conjugations reveal how this method can be applied to a diverse range of biological processes.

Weaknesses:

Though the ~100% ligation efficiency is an advancement, the long recognition linker may be the biggest drawback. For large native proteins that are challenging/cannot be synthesized and require multiple connectase ligation reactions to yield a complete continuous product, the multiple interruptions with long linkers will likely interfere with protein folding, resulting in non-native protein structures. This method will be a good alternative to traditional approaches as the author mentioned but limited to generating epitope/peptide/protein tagged proteins, and not for synthetic protein biology aimed at examining native/endogenous protein function in vitro.

Reviewer #2 (Public review):

Summary:

This manuscript investigates how neural cell development is affected in Lowe syndrome. Using neural cultures differentiated from human iPSCs carrying either an LS mutation or a genetically engineered mutation in OCRL, the authors show a depletion of mitochondrial DNA and a decrease in mitochondrial activities that correlate with an increased formation of astrocytes at the expense of neurons. Similar effects on mitochondria and on astrocyte development were observed in an LS mouse model. Moreover, these mutant brain cells are less likely to be ciliated and show a reduction in Sonic Hedgehog signalling.

Strengths/Weaknesses:

The study derives strength from the analyses of two different models of Lowe syndrome, both reaching similar conclusions. However, the observed changes in mitochondrial defects, neuronal/astrocytic development, and primary cilia are only correlated, with no attempt to investigate a causal relationship. Moreover, the mouse model is only analysed at the adult stage providing no insights into the development of the defects. Different brain regions are analysed with immunostainings and qRT-PCR making it challenging to draw clear correlations between these findings. The quality of the corresponding figures is often poor and the selection of markers is frequently inappropriate. Taken together, these limitations complicate the interpretations of the data and significantly limit the conclusions that can be drawn from the study.

Reviewer #2 (Public review):

Summary:

In this manuscript, the authors employ theoretical analysis of an elastic membrane model to explore membrane vesiculation pathways in clathrin-mediated endocytosis. A complete understanding of clathrin-mediated endocytosis requires detailed insight into the process of membrane remodeling, as the underlying mechanisms of membrane shape transformation remain controversial, particularly regarding membrane curvature generation. The authors compare constant area and constant membrane curvature as key scenarios by which clathrins induce membrane wrapping around the cargo to accomplish endocytosis. First, they characterize the geometrical aspects of the two scenarios and highlight their differences by imposing coating area and membrane spontaneous curvature. They then examine the energetics of the process to understand the driving mechanisms behind membrane shape transformations in each model. In the latter part, they introduce two energy terms: clathrin assembly or binding energy, and curvature generation energy, with two distinct approaches for the latter. Finally, they identify the energetically favorable pathway in the combined scenario and compare their results with experiments, showing that the constant-area pathway better fits the experimental data.

Strengths:

The manuscript is well-written, well-organized, and presents the details of the theoretical analysis with sufficient clarity.<br /> The calculations are valid, and the elastic membrane model is an appropriate choice for addressing the differences between the constant curvature and constant area models.<br /> The authors' approach of distinguishing two distinct free energy terms-clathrin assembly and curvature generation-and then combining them to identify the favorable pathway is both innovative and effective in addressing the problem.<br /> Notably, their identification of the energetically favorable pathways, and how these pathways either lead to full endocytosis or fail to proceed due to insufficient energetic drives, is particularly insightful.

Weaknesses:

Membrane remodeling in cellular processes is typically studied in either a constant area or constant tension ensemble. While total membrane area is preserved in the constant area ensemble, membrane area varies in the constant tension ensemble. In this manuscript, the authors use the constant tension ensemble with a fixed membrane tension, σe. However, they also use a constant area scenario, where 'area' refers to the surface area of the clathrin-coated membrane segment. This distinction between the constant membrane area ensemble and the constant area of the coated membrane segment may cause confusion.

As mentioned earlier, the theoretical analysis is performed in the constant membrane tension ensemble at a fixed membrane tension. The total free energy E_tot of the system consists of membrane bending energy E_b and tensile energy E_t, which depends on membrane tension, σe. Although the authors mention the importance of both E_b and E_t, they do not present their individual contributions to the total energy changes. Comparing these contributions would enable readers to cross-check the results with existing literature, which primarily focuses on the role of membrane bending rigidity and membrane tension.

The authors introduce two different models, (1,1) and (1,2), for generating membrane curvature. Model 1 assumes a constant curvature growth, corresponding to linear curvature growth, while Model 2 relates curvature growth to its current value, resembling exponential curvature growth. Although both models make physical sense in general, I am concerned that Model 2 may lead to artificial membrane bending at high curvatures. Normally, for intermediate bending, ψ > 90, the bending process is energetically downhill and thus proceeds rapidly. the bending process is energetically downhill and thus proceeds rapidly. However, Model 2's assumption would accelerate curvature growth even further. This is reflected in the endocytic pathways represented by the green curves in the two rightmost panels of Fig. 4a, where the energy steeply increases at large ψ. I believe a more realistic version of Model 2 would require a saturation mechanism to limit curvature growth at high curvatures.

Reviewer #2 (Public review):

Summary:

In this manuscript, Al Asafen, Clark et al., use fluorescence correlation spectroscopy (FCS) to quantitatively analyze the mobility of Dl along the DV axis of the early Drosophila embryo. Dl is essential for dorsal-ventral (DV) patterning and its gradient initiates the activation of several genes and thereby orchestrates the formation of the Drosophila body plan. While the mechanisms underlying the formation of the Dl gradient have been extensively studied by this group and others, there are some observations for which there is not yet a mechanistic explanation. For example, the peak of the Dl gradient grows continuously during nuclear cycles 10-14. This is likely due to Cact-dependent Dl diffusion and Dl binding to DNA. However, the biophysical parameters governing Dl nuclear dynamics that would support these claims have not been previously measured. In this work, the authors provide evidence that GFP-tagged Dl may be separated into a mobile pool and an immobile pool. Interestingly, the fraction of immobile Dl is position-dependent along the DV axis, revealing more binding to DNA in the ventral than in the dorsal nuclei. This is either due to higher binding affinity in ventral locations (due to Toll-dependent Dl phosphorylation) or to higher Dl-Cact binding in dorsal nuclei that would prevent Dl from binding to DNA. Using dl-mutant alleles, the authors support the latter hypothesis.

Strengths:

The manuscript is well written and their conclusions are convincingly supported by their methodology and analysis. As a quantitative study, the biophysical analysis seems rigorous, in general.

Although this is not the first study that employs FSC to investigate the dynamics of a morphogen, it further exemplifies how these quantitative tools can be used to uncover mechanistic aspects of morphogen dynamics during development. In particular, the manuscript reports novel biophysical parameters of Dl dynamics that will be helpful in future hypotheses-driven modeling studies.

Weaknesses:

In my opinion, the main weakness of the manuscript is that the main biological implication of the study, namely that the asymmetry in the fraction of immobile Dl is a result of nuclear Dl-Cact binding which prevents Dl from binding DNA (Figure 5), occurs in a region of the embryo where there is very little Dl anyways (Figure 1A, 5A). While it is interesting that the fraction of immobile Dl increases (just a little, but significantly) in dorsal nuclei in mutants expressing a form of Dl with reduced Cact binding it is unclear what is the biological impact of this effect in a location where Dl is nearly absent. As can be seen in Figure 3F, the fraction of immobile is unaffected in Dl-mutant forms with reduced DNA binding, because it is already very low. It is unlikely that Dl binding to Cact in dorsal nuclei would affect shuttling as well since the fraction is very low anyway.

While the authors have a very clear understanding of the biology of the Dl gradient, I feel that the manuscript is more written as a 'tools' paper (i.e., to exemplify how FSC methods and analysis can be used for biological discovery). This is ok, but I think that the authors should discuss further what are the biological implications of these findings other than the contribution to uncovering the biophysical parameters. For example, I think that the implications of the rejected hypothesis (i.e., that Toll-dependent Dl phosphorylation does not seem to have an impact on Dl binding affinities to DNA) are important and should be further discussed (even if no additional experiments are performed). What is then the role of Dl phosphorylation? Perhaps it could have an impact on patterning robustness in lateral regions. The authors should report in Figure 5 also what happens to the fraction of Dl bound to DNA in lateral regions in the reduced Cact binding and reduced Toll phosphorylation mutants.

The way that position along the DV axis is reported using the nuclear-cytoplasmic-ratio (NCR) in Figures 1-3 is not incorrect, but I wonder if it is the best way of doing it. The reason is that it spreads out a relatively small region of the embryo (the ventral-most locations) and shrinks a relatively large region of the embryo (lateral and dorsal regions), see Figure 1A. Perhaps reporting the NCR in log_2 units would be more appropriate.

Reviewer #2 (Public review):

Summary

In this study, Bisen et al. characterized the state-dependency of insulin-producing cells in the brain of Drosophila melanogaster. They successfully established that IPC activity is modulated by the nutritional state and age of the animal. Interestingly, they demonstrate that IPCs respond to the ingestion of glucose, rather than to perfusion with it, an observation reminiscent of the incretin effect in mammals. The study is well conducted and presented and the experimental data convincingly support the claims made.

Strengths

The study makes great use of the tools available in *Drosophila* research, demonstrating the effect that starvation and subsequent refeeding have on the physiological activity of IPCs as well as on the behavior of flies to then establish causal links by making use of optogenetic tools.<br /> It is particularly nice to see how the authors put their findings in context to published research and use for example TDC2 neuron activation or DH44 activity to establish baselines to relate their data to.

Reviewer #2 (Public review):

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

My concerns have been addressed. And the quality of the manuscript is improved significantly.

Reviewer #2 (Public review):

Summary:

The authors build a gene expression model based on histone post-translational modifications, and find that H3K27ac is correlated with gene expression. They proceed to perturb H3K27ac at 13 gene promoters in two cell types, and measure gene expression changes to test their model.

Strengths:

The combination of multiple methods to model expression, along with utilizing 6 histone datasets in 13 cell types allowed the authors to build a model that correlates between 0.7-0.79 with gene expression. They use dCas9-p300 fusions to perturb H3K27ac and monitor gene expression to test their model. Ranked correlations of the HEK293 data showed some support for the predictions after perturbation of H3K27ac.

Weaknesses:

The perturbation of 5 genes in K562 with perturb-seq data shows a modest correlation of ~0.5 and isn't included in the main figures. The authors are then left to speculate reasons why the outcome of epigenome editing doesn't fit their predictions, which highlights the limited value in the current version of this method.

As mentioned before, testing genes that were not expressed being most activated by dCas9-p300 weaken the correlations vs. looking at a broad range of different gene expression as the original model was trained on.<br /> If the authors want this method to be used to predict outcomes of epigenome editing, expanding to dCas9-KRAB and other CRISPRa methods (SAM and VPR) would be useful. Those datasets are published and could be analyzed for this manuscript.<br /> The authors don't compare their method to other prediction methods.

Reviewer #2 (Public review):

Summary:

This article reviews the studies on the relationship between slow oscillation (SO)-spindle (SP) coupling and memory consolidation. It innovatively employs non-normal circular linear correlations through a Bayesian meta-analysis. A systematic analysis of the retrieved studies highlighted that co-coupling of SO and the fast SP's phase and amplitude at the frontal part better predicts memory consolidation performance. I only have a few comments that I recommend are addressed.

Major Comments:

Regarding the Moderator of Age: Although the authors discuss the limited studies on the analysis of children and elders regarding age as a moderator, the figure shows a significant gap between the ages of 40 and 60. Furthermore, there are only a few studies involving participants over the age of 60. Given the wide distribution of effect sizes from studies with participants younger than 40, did the authors test whether removing studies involving participants over 60 would still reveal a moderator effect?

Reviewer #2 (Public review):

Summary:

The authors explored the importance of data quality and representation for ligand-based virtual screening approaches. I believe the results could be of potential benefit to the drug discovery community, especially to those scientists working in the field of machine learning applied to drug research. The in silico design is comprehensive and adequate for the proposed comparisons.

This manuscript by Chong A. et al describes that it is not necessary to resort to the use of sophisticated deep learning algorithms for virtual screening, since based on their results considering conventional ML may perform exceptionally well if feeded by the right data and molecular representations.

The article is interesting and well-written. The overview of the field and the warning about dataset composition are very well thought-out and should be of interest to a broad segment of the AI in drug discovery readership. This article further highlights some of the considerations that need to be taken into consideration for the implementation of data-centric AI for computer-aided drug design methods.

Strengths:

This study contributes significantly to the field of machine learning and data curation in drug discovery. The paper is, in general, well-written and structured. However, in my opinion, there are some suggestions regarding certain aspects of the data analyses.

Weaknesses:

The conclusions drawn in the study are based on the analysis of a two dataset. The authors chose BRAF as an example in this study, and expanded with BACE-1 dataset; however a benchmark with several targets would be suitable to evaluate reproducibility or transferability of the method. One concern could be the applicability of the method in other targets.

Reviewer #2 (Public review):

In this manuscript, Menegas et al. classify the "control" behavior of captive marmosets. They combine behavioral screening from video recordings with audio and neural recordings (from the striatum) to better define what can be considered a typical behavioral repertoire for captive marmoset monkeys. A range of analyses is presented, investigating various aspects of behavior, such as social interactions and the detection of atypical individuals.

The manuscript is compelling in many respects, especially due to the richness of the dataset and the breadth of analyses presented. However, a significant issue with the manuscript lies in its writing: the results are conveyed in an overly succinct and superficial manner, and the "Methods" section is nearly absent. Key concepts are often undefined, and the mathematical details underlying the figures are not explained, leaving readers to guess the authors' approach.

Another issue is the vague use of the term "natural behavior." All data presented here appear to have been collected in small cages with limited climbing opportunities and enrichment. Thus, the authors should refrain from using "natural" to describe these conditions.

Below, we elaborate further on the lack of methodological detail. Based on these issues, we believe the manuscript, in its current form, does not meet the scientific standards necessary for proper review. We strongly encourage the authors to undertake an extensive revision.

Major Revision Points:

The methods and results require significantly more detail. A scientific publication should provide readers with enough information to reproduce the study. Here, the detail level is far too low to fully understand, or reproduce, the study, and in many instances, readers are left to guess how the figure panels were produced. Below is a non-exhaustive list of examples illustrating these issues:

(1) "we temporarily placed horizontal cage dividers to reduce the total cage size during data collection": What were the resulting (and initial) cage dimensions?

(2) "After training the network, we hierarchically clustered the latent space": What is the latent space? Based on Figure 2a, it appears related to the network's recurrent layer, but this is not clarified in the text.

(3) Alpha and perplexity parameters: Please define these terms. Since these concepts appear fundamental, readers should not have to consult external references.

(4) "We then traced cluster identities across hierarchical levels": What are hierarchical levels?

(5) "To understand how the input time series data was weighed in the bottleneck layer of the model": What is the bottleneck layer?

(6) "we measured the average attention allocation to previous time points": The authors should define "attention allocation."

(7) "we compared each neuron's firing rate distribution to shuffled data based on the overall frequency of each behavior during the session": This description is insufficient to understand the analysis.

(8) "we hierarchically clustered neurons according to their firing rate enrichment maps": No mathematical explanation is provided for neuron clustering, nor is the concept of a "firing rate enrichment map" clarified.

(9) "Cluster 4 showed higher activity when neurons were 'alone' or 'active'": This is vague and uses unclear jargon (e.g., "neurons alone"). Additionally, no mathematical explanation is provided for assigning neuronal activity to behavioral states.

(10) Figure 3f, right-side panels: The analysis seems to involve cage mate positioning, yet no description is provided.

(11) "we used motion watches to measure activity across all hours": Are these motion-sensitive watches physically attached to the animals? The methodology should be described, including data analysis details.

This list could continue, but we trust the authors understand the point. There is a wealth of analyses and information in this study, but the descriptions are too superficial. We understand that fully describing each analysis may require significant rewriting, including supplementary figures, and will likely make the manuscript longer. This is entirely acceptable, as the ideas presented here are worth the added rigor.

"Natural behavior": Typically, the term "natural" suggests that the dataset reflects the range of behaviors exhibited by animals in the wild. Here, however, recordings were made in a small cage with limited climbing opportunities and enrichment. Under these conditions, it's hard to justify describing the behavior as "natural". In a project aimed at classifying the behavioral repertoire of marmoset monkeys and making this dataset accessible to other laboratories, it would be helpful to include more detailed information about the animals' housing conditions. This might include cage sizes, temperature, humidity, and details on food quantities, quality, and feeding times.

Correlation versus causation: In the section titled "Large-scale data collection reveals variability across days and correlation between cagemates," the authors conclude: "Overall, these results indicate that measurements of animals' behavioral traits depend heavily on their social environment." This interpretation seems incorrect. We know that animal behavior varies throughout the day, with activity peaks typically occurring in the morning and afternoon. Such factors, or other external influences, could induce correlations between animals that are not caused by social interactions.

Figure 4g: What are we intended to conclude from this analysis?

Figure 5: Please specify the type of calls analyzed. For example, did you analyze only long-distance calls (aka 'loud phees' or 'shrills')? In "We split the audio data into 5-minute (non-continuous) segments and found that the average call rate in these segments varied from 0 calls per minute to 60 calls per minute (Fig. 5d-e)," does the call rate refer to individual animals or the entire cage?

"This implies that a high rate of calls in a room can interrupt animals during social resting states and cause them to preferentially exhibit more active/attentive states." Does it? This could simply indicate that more active animals produce more calls.

"We recorded neural activity in the striatum because it is known to contain diverse signals related to movement and social interactions." While I understand that the authors intend to publish neural data separately, a brief discussion of the striatum's role here would be helpful.

Reviewer #2 (Public review):

Summary:

The manuscript by Hu et. al presents a clearly-designed examination of the role of tachykinin1-expressing neurons in the parasubthalamic nucleus of the lateral posterior hypothalamus (PTSN) in active avoidance learning. These glutamatergic neurons have previously been implicated in responding to negative stimuli. This manuscript expands the current understanding of PTSNTac1 neurons in learned responses to threats by showing their role in encoding and mediating the active avoidance response. The authors first use bulk fiber photometry imaging to show the encoding of the active avoidance procedure, followed by cell-type specific manipulations of PTSNTac1 neurons during active avoidance. Finally, they show that encoding and mediation of active avoidance in a downstream target of PTSNTac1 neurons, the PVT/intermediodorsal nuclei of the dorsal thalamus (IMD), has the same effect as what was discovered in the cell body. This contrasts other output regions of the PTSN, such as the PBN and CeA, which were not found to promote active avoidance learning. The experiments presented were well-designed to support the conclusions of the authors, however, the manuscript is missing several key control experiments and supplemental information to support their main findings.

Strengths:

The manuscript provides information on a brain region and downstream target that mediates active avoidance learning. The manuscript provides valuable information via necessity and sufficiency experiments to show the role of the population of interest (PTSNTac1 neurons) in active avoidance learning. The authors also performed most behavior experiments in male and female mice, with adequate power to address potential sex differences in the control of active avoidance by PTSNTac1 neurons. Finally, the manuscript provides valuable information about the specificity of the PTSNTac1 downstream target in regulating active avoidance learning, identifying the PVT/intermediodorsal nuclei of the dorsal thalamus as the key target and ruling out the PBN and CeA.

Weaknesses:

However, several main conclusions of the paper must be interpreted carefully due to missing or inadequate control experiments and histological verification.

(1) Inadequate presentation of viral localization. The authors state that expression was "largely restricted within PSTN" however there is no quantification of the amount of viral expression beyond the target region. Given that Tac1 is expressed in neighboring regions, it is critical to show the viral expression and fiber implant location data for all animals included in the figures. Furthermore, criteria for inclusion and exclusion based on mistargeting should be delineated. This should also be clearly outlined for the experiments in Figure S5, where "behavioral effects of activation of sparsely Tac1-expressing neurons in two adjacent areas of PSTN" was tested but the location of viral expression in those cases is unclear.

(2) Lack of motion artifact correction with isosbestic signal for GCamp recordings. It is appreciated that the authors included a separate EGFP-expressing group to compare to the GCamp-expressing group, however, additional explanation is required for the methods used to analyze the raw fluorescent signal. Namely, were fluorescent signals isosbestic-corrected prior to calculating ΔF/F? If no isosbestic signal was used to correct motion artifacts within a recording session, additional explanation is needed to explain how this was addressed. The lack of motion artifacts in the EGFP signal in a separate cohort is inadequate to answer this caveat as motion artifacts are within-animal.

(3) Missing control experiment demonstrating intact locomotor performance in caspase ablation experiments. The authors use caspase ablation of PTSNTac1 neurons prior to active avoidance learning to appraise the necessity of this cell population. However, a control experiment showing intact locomotor ability in ablated mice was not performed.

(4) Missing control experiment demonstrating [lack of] valence with PTSN silencing manipulations. The authors performed a real-time and conditioned place preference experiments for ChR2-expressing mice (Fig 3M) and found stimulation to be negatively-valenced and generate an aversive memory, respectively. Absent this control experiment with silencing, an alternative conclusion remains possible that optogenetic silencing via GtACR2 created nonspecific location preferences in the active avoidance apparatus, confounding the interpretation of those results.

(5) Incomplete analysis of sex differences. Data in female mice is conspicuously missing from inhibition experiments. The rationale for exclusion from this dataset would be useful for the interpretation of the other noted sex differences.

Reviewer #2 (Public review):

Summary:

The authors sequence 45 new samples of S. Gallinarum, a commensal Salmonella found in chickens, which can sometimes cause disease. They combine these sequences with around 500 from public databases, determine the population structure of the pathogen, and coarse relationships of lineages with geography. The authors further investigate known anti-microbial genes found in these genomes, how they associate with each other, whether they have been horizontally transferred, and date the emergence of clades.

Strengths:

- It doesn't seem that much is known about this serovar, so publicly available new sequences from a high burden region are a valuable addition to the literature.<br /> - Combining these sequences with publicly available sequences is a good way to better contextualise any findings.<br /> - The genomic analyses have been greatly improved since the first version of the manuscript, and appropriately analyse the population and date emergence of clades.<br /> - The SNP thresholds are contextualised in terms of evolutionary time.<br /> - The importance and context of the findings are fairly well described.

Weaknesses:

- There are still a few issues with the genomic analyses, although they no longer undermine the main conclusions:

(1) Although the SNP distance is now considered in terms of time, the 5 SNP distance presented still represents ~7yrs evolution, so it is unlikely to be a transmission event, as described. It would be better to use a much lower threshold or describe the interpretation of these clusters more clearly. Bringing in epidemiological evidence or external references on the likely time interval between transmissions would be helpful.

(2) The HGT definition has not fundamentally been changed and therefore still has some issues, mainly that vertical evolution is still not systematically controlled for. Using a 5kb window is not sufficient, as LD may extend across the entire genome. As the authors have now run gubbins correctly, they could use the results from this existing analysis to find recent HGT. To definite mobilisation, perhaps a standard pipeline such (e.g. https://github.com/EBI-Metagenomics/mobilome-annotation-pipeline) would be more convincing.

(3) The invasiveness index is better described, but the authors still did not provide convincing evidence that the small difference is actually biologically meaningful (there was no statistical difference between the two strains provided in response Figure 6). What do other Salmonella papers using this approach find, and can their links be brought in? If there is still no good evidence, a better description of this difference would help make the conclusions better supported.

In summary, the analysis is broadly well described and feels appropriate. Some of the conclusions are still not fully supported, although the main points and context of the paper now appear sound.

Reviewer #2 (Public review):

In this version of manuscript, the author clarified many details and rewrote some sections. This substantially improved the readability of the paper. I also recognized that the author spent substantial efforts in the Appendix to answer the potential questions.

Unfortunately, I am not currently convinced by the theory proposed in this paper. In the next section, I will first recap the logic of the author and explain why I am not convinced. Although the theory fits many experimental results, other theories on overflow metabolism are also supported by experiments. Hence, I do not think based on experimental data we could rule in or rule out different theories.

Recap: To explain the origin of overflow metabolism, the author uses the following logic:

(1) There is a substantial variability of single-cell growth rate<br /> (2) The flux (J_r^E) and (J_f^E) are coupled with growth rate by Eq. 3<br /> (3) Since growth rate varies from cells to cells, flux (J_r^E) and (J_f^E) also varies<br /> (4) The variabilities of above fluxes in above create threshold-analog relation, and hence overflow metabolism.

My opinion:

The logic step (2) and (3) have caveats. The variability of growth rate has large components of cellular noise and external noise. Therefore, variability of growth rate is far from 100% correlated with variability of flux (J_r^E) and (J_f^E) at the single-cell level. Single-cell growth rate is a complex, multivariate functional, including (Jr^E) and (J_f^E) but also many other variables. My feeling is the correlation could be too low to support the logic here.

One example: ribosomal concentration is known to be an important factor of growth rate in bulk culture. However, the "growth law" from bulk culture cannot directly translate into the growth law at single-cell level [Ref1,2]. This is likely due to other factors (such as cell aging, other muti-stability of cellular states) are involved.

Therefore, I think using Eq.3 to invert the distribution of growth rate into the distribution of (Jr^E) and (J_f^E) is inapplicable, due to the potentially low correlation at single-cell level. It may show partial correlations, but may not be strong enough to support the claim and create fermentation at macroscopic scale.

Overall, if we track the logic flow, this theory implies overflow metabolism is originated from variability of k_cat of catalytic enzymes from cells to cells. That is, the author proposed that overflow metabolism happens macroscopically as if it is some "aberrant activation of fermentation pathway" at the single-cell level, due to some unknown partially correlation from growth rate variability.

Compared with other theories, this theory does not involve any regulatory mechanism and can be regarded as a "neutral theory". I am looking forward to seeing single cell experiments in the future to provide evidences about this theory.

[Ref1] https://www.biorxiv.org/content/10.1101/2024.04.19.590370v2<br /> [Ref2] https://www.biorxiv.org/content/10.1101/2024.10.08.617237v2

Reviewer #2 (Public review):

Summary:

This study investigates the impact of mother-child neural synchronization and the quality of parent-child relationships on the development of Theory of Mind (ToM) and social cognition. Utilizing a naturalistic fMRI movie-viewing paradigm, the authors analyzed inter-subject neural synchronization in mother-child dyads and explored the connections between neural maturity, parental caregiving, and social cognitive outcomes. The findings indicate age-related maturation in ToM and social pain networks, emphasizing the importance of dyadic interactions in shaping ToM performance and social skills, thereby enhancing our understanding of the environmental and intrinsic influences on social cognition.

Strengths:

This research addresses a significant question in developmental neuroscience, by linking social brain development with children's behaviors and parenting. It also uses a robust methodology by incorporating neural synchrony measures, naturalistic stimuli, and a substantial sample of mother-child dyads to enhance its ecological validity. Furthermore, the SEM approach provides a nuanced understanding of the developmental pathways associated with Theory of Mind (ToM).

Weaknesses:

(1) Upon reviewing the introduction, I feel that the first goal - developmental changes of the social brain and its relation to age - seems somewhat distinct from the other two goals and the main research question of the manuscript. The authors might consider revising this section to enhance the overall coherence of the manuscript. Additionally, the introduction lacks a clear background and rationale for the importance of examining age-related changes in the social brain.

(2) The manuscript uses both "mother-child" and "parent-child" terminology. Does this imply that only mothers participated in the fMRI scans while fathers completed the questionnaires? If so, have the authors considered the potential impact of parental roles (father vs. mother)?

(3) There is inconsistent usage of the terms ISC and ISS in the text and figures, both of which appear to refer to synchronization derived from correlation analysis. It would be beneficial to maintain consistency throughout the manuscript.

(4) Of the 50 dyads, 16 were excluded due to data quality issues, which constitutes a significant proportion. It would be helpful to know whether these excluded dyads exhibited any distinctive characteristics. Providing information on demographic or behavioral differences-such as Theory of Mind (ToM) performance and age range between the excluded and included dyads would enhance the assessment of the findings' generalizability.

(5) The article does not adhere to the standard practice of using a resting state as a baseline for subtracting from task synchronization. Is there a rationale for this approach? Not controlling for a baseline may lead to issues, such as whether resting state synchronization already differs between subjects with varying characteristics.

(6) The title of the manuscript suggests a direct influence of mother-child interactions on children's social brain and theory of mind. However, the use of structural equation modeling (SEM) may not fully establish causal relationships. It is possible that the development of children's social brain and ToM also enhances mother-child neural synchronization. The authors should address this alternative hypothesis of the potential bidirectional relationship in the discussion and exercise caution regarding terms that imply causality in the title and throughout the manuscript.

(7) I would appreciate more details about the 14 Theory of Mind (ToM) tasks, which could be included in supplemental materials. The authors score them on a scale from 0 to 14 (each task 1 point); however, the tasks likely vary in difficulty and should carry different weights in the total score (for example, the test and the control questions should have different weights). Many studies have utilized the seven tasks according to Wellman and Liu (2004), categorizing them into "basic ToM" and "advanced ToM." Different components of ToM could influence the findings of the current study, which should be further examined by a more in-depth analysis.

Reviewer #2 (Public review):

Summary:

The past five years have seen the publication of both new (Witvliet et al., 2021) and newly analyzed (Cook et al., 2019; Moyle et al., 2021; Brittin et al., 2021) data for the C. elegans connectome. The increase in data availability for a single species allows researchers to examine variability due to both stochastic events and changes over development. The quantity of these data is huge. To help the community make these data more accessible, the authors present a new online tool that allows the examination of 3D models for C. elegans neurons in the central neuropil across development. In addition to visualizing the overall structure of the neuronal processes and locations of synapses, the NeuroSCAN tool also allows users to probe into the C-PHATE visualization results, which this group previously pioneered to describe similarities in neuron adjacency (Moyle et al., 2021).

Strengths:

The ability to visualize the data from both a connectomics and contactomics perspective across developmental time has significant power. The original C. elegans connectome (White et al., 1986) presented their circuits as line drawings with chemical and electrical synapses indicated through arrows and bars. While these line drawings remain incredibly useful, they were also necessary simplifications for a 2D publication and they lack details of the complex architecture seen within each EM image. Koonce et al take advantage of segmented image data of each neuronal process within the nerve ring to create a web interface where users can visualize 3D models for their neuron of choice. The C-PHATE visualization allows users to explore similarities among different neurons in terms of adjacency and then go directly to the 3D model for these neurons. The 3D models it generates are beautiful and will likely be showing up in many future presentations and publications. The tool doesn't require any additional downloading and is open source.

Weaknesses:

While it's impossible to create one tool that will satisfy all potential users, I found myself wanting to have numbers associated with the data. For example, knowing the number of connections or the total surface area of contacts between individual neurons wasn't possible through the viewer, which limits the utility of taking deep analytical dives. While connectivity data are readily accessible through other interfaces such as Nemanode and WormWiring, a more thorough integration may be helpful to some users.

There were several issues with the user interface that made it a bit clunky to use. For example, as I added additional neurons to the filter search box, the loading time got longer and longer. I ran an experiment uploading all of the amphid neurons, one pair at a time. Each additional neuron pair added an additional 5-10 seconds to the loading. By the time I got to the last pair, it took over a minute to load. Issues like these, some of which may be unavoidable given the size of the data, could be conveyed through better documentation. I did not find the tutorial very helpful and the supplementary movies lacked any voiceover, so it wasn't always clear what they were trying to show.

Reviewer #2 (Public review):

Summary:

There are two accounts in the literature that propose that expectations suppress the activity of neurons that are (a) not tuned to the expected stimulus to increase the signal-to-noise ratio for expected stimuli (sharpening model) or (b) tuned to the expected stimulus to highlight novel information (dampening model). One recent account, the opposing process theory, brings the two models together and suggests that both processes occur, but at different time points: initial sharpening is followed by later dampening of the neural activity of the expected stimulus. In this study, the authors aim to test the opposing process theory in a statistical learning task by applying multivariate EEG analyses and finding evidence for the opposing process theory based on the within-trial dynamics.

Strengths:

This study addresses a very timely research question about the underlying mechanisms of expectation suppression. The applied EEG decoding approach offers an elegant way to investigate the temporal characteristics of expectation effects. A major strength of the study lies in the experimental design that aims to control for repetition effects, one of the common confounds in prediction suppression studies. The reported results are novel in the field and have the potential to substantially improve our understanding of expectation suppression in visual perception.

Weaknesses:

The strength in controlling for repetition effects by introducing a neutral (50% expectation) condition also adds a weakness to the current version of the manuscript, as this neutral condition is not integrated into the behavioral (reaction times) and EEG (ERP and decoding) analyses. This procedure remained unclear to me. The reported results would be strengthened by showing differences between the neutral and expected (valid) conditions on the behavioral and neural levels. This would also provide a more rigorous check that participants had implicitly learned the associations between the picture category pairings.

It is not entirely clear to me what is actually decoded in the prediction condition and why the authors did not perform decoding over trial bins in prediction decoding as potential differences across time could be hidden by averaging the data. The manuscript would generally benefit from a more detailed description of the analysis rationale and methods.

Finally, the scope of this study should be limited to expectation suppression in visual perception, as the generalization of these results to other sensory modalities or to the action domain remains open for future research.

Reviewer #2 (Public review):

Summary:

Measurements of the reward positivity, an electrophysiological component elicited during reward evaluation, have previously been used to understand how self-benefitting effort expenditure influences the processing of rewards. The present study is the first to complement those measurements with electrophysiological reward after-effects of effort expenditure during prosocial acts. The results provide solid evidence that effort adds reward value when the recipient of the reward is the self but discounts reward value when the beneficiary is another individual.

Strengths:

An important strength of the study is that the amount of effort, the prospective reward, the recipient of the reward, and whether the reward was actually gained or not were parametrically and orthogonally varied. In addition, the researchers examined whether the pattern of results generalized to decisions about future efforts. The sample size (N=40) and mixed-effects regression models are also appropriate for addressing the key research questions. Those conclusions are plausible and adequately supported by statistical analyses.

Weaknesses:

Although the obtained results are highly plausible, I am concerned whether the reward positivity (RewP) and P3 were adequately measured. The RewP and P3 were defined as the average voltage values in the time intervals 300-400 ms and 300-440 ms after feedback onset, respectively. So they largely overlapped in time. Although the RewP measure was based on frontocentral electrodes (FC3, FCz, and FC4) and the P3 on posterior electrodes (P3, Pz, and P4), the scalp topographies in Figure 3 show that the RewP effects were larger at the posterior electrodes used for the P3 than at frontocentral electrodes. So there is a concern that the RewP and P3 were not independently measured. This type of problem can often be resolved using a spatiotemporal principal component analysis. My faith in the conclusions drawn would be further strengthened if the researchers extracted separate principal components for the RewP and P3 and performed their statistical analyses on the corresponding factor scores.

Reviewer #2 (Public review):

Summary:

The manuscript: "Synergistic effect of inhibiting CHK2 and DNA replication on cancer cell growth" successfully demonstrates that the compounds BKC and IBC found in Psoralea corylifolia act synergistically to inhibit cancer cell proliferation, using a wide range of well-chosen methodologies. Moreover, the authors characterized the mechanisms of action of both drugs, which result in inhibition of cell proliferation. The use of multiple cell lines and the mice models makes the study robust and complete.

Significance:

The manuscript presents a well written study that offers new insights and contributions to the field. Although the inhibitors described have been known in science, the authors present convincingly their mode of action, which is either better characterized (for BKC) or inhibiting a different than previously suggested enzyme (for IBC). Authors also nicely pinpoint and explain the narrow window of concentrations when these two compounds act synergistically rather than additively. The analyses in multiple cell lines, mouse models and in combination with other cancer treatments, make this study of interest not only for fundamental researchers but also for translational scientists and industry.

Reviewer #2 (Public review):

Summary:

Ngo et al. use AlphaFold2 and Rosetta to model closed, open, and inactive states of the human ion channel hERG. Subsequent MD simulations and comparisons with experiments support the plausibility of their models.

Strengths:

This is thorough work studied from many different angles. It provides a self-consistent picture of how conformational changes in hERG may affect its function and binding to different targets.

Weaknesses:

Though this work claims the methodologies can be generalized to other systems, it is not obvious how. Many modeling choices seem arbitrary and also seem to have required extensive expert knowledge of the system. This limits the applicability of the modeling strategy.

Reviewer #2 (Public review):

Summary:

Kume et al. found for the first time that Semaphorin 4A (Sema4A) was downregulated in both mRNA and protein levels in L and NL keratinocytes of psoriasis patients compared to control keratinocytes. In peripheral blood, they found that Sema4A is not only expressed in keratinocytes but is also upregulated in hematopoietic cells such as lymphocytes and monocytes in the blood of psoriasis patients. They investigated how the down-regulation of Sema4A expression in psoriatic epidermal cells affects the immunological inflammation of psoriasis by using a psoriasis mice model in which Sema4A KO mice were treated with IMQ. Kume et al. hypothesized that down-regulation of Sema4A expression in keratinocytes might be responsible for the augmentation of psoriasis inflammation. Using bone marrow chimeric mice, Kume et al. showed that KO of Sema4A in non-hematopoietic cells was responsible for the enhanced inflammation in psoriasis. The expression of CCL20, TNF, IL-17, and mTOR was upregulated in the Sema4AKO epidermis compared to the WT epidermis, and the infiltration of IL-17-producing T cells was also enhanced.

Strengths:

Decreased Sema4A expression may be involved in psoriasis exacerbation through epidermal proliferation and enhanced infiltration of Th17 cells, which helps understand psoriasis immunopathogenesis.

Weaknesses:

The mechanism of decreased Sema4A expression in psoriasis is not clear, although this does not affect the strength of this research.

Reviewer #2 (Public review):

Summary:

In this study, the authors discovered that the chemoresistance in RCC cell lines correlates with the expression levels of the drug transporter ABCA1 and the EMT-related transcription factor Snail. They demonstrate that Snail induces ABCA1 expression and chemoresistance, and that ABCA1 inhibitors can counteract this resistance. The study also suggests that Snail disrupts the cholesterol-sphingomyelin (Chol/SM) balance by repressing the expression of enzymes involved in very long-chain fatty acid-sphingomyelin synthesis, leading to excess free cholesterol. This imbalance activates the cholesterol-LXR pathway, inducing ABCA1 expression. Moreover, inhibiting cholesterol esterification suppresses Snail-positive cancer cell growth, providing potential lipid-targeting strategies for invasive cancer therapy.

Strengths:

This research presents a novel mechanism by which the EMT-related transcription factor Snail confers drug resistance by altering the Chol/SM balance, introducing a previously unrecognized role of lipid metabolism in the chemoresistance of cancer cells. The focus on lipid balance, rather than individual lipid levels, is a particularly insightful approach. The potential for targeting cholesterol detoxification pathways in Snail-positive cancer cells is also a significant therapeutic implication.

Weaknesses:

The study's claim that Snail-induced ABCA1 is crucial for chemoresistance relies only on pharmacological inhibition of ABCA1, lacking additional validation. The causal relationship between the disrupted Chol/SM balance and ABCA1 expression or chemoresistance is not directly supported by data. Some data lack quantitative analysis.

Reviewer #2 (Public review):

Overview

In this manuscript, the authors use deep mutational scanning to assess the effect of ~6,600 protein-coding variants in MC4R, a G protein-coupled receptor associated with obesity. Reasoning that current deep mutational scanning approaches are insufficiently precise for some drug development applications, they focus on articulating new, more precise approaches. These approaches, which include a new statistical model and innovative reporter assay, enable them to probe molecular phenotypes directly relevant to the development of drugs that target this receptor with high precision and statistical rigor.

They use the resulting data for a variety of purposes, including probing the relationship between MC4R's sequence and structure, analyzing the effect of clinically important variants, identifying variants that disrupt downstream MC4R signaling via one but not both pathways, identifying loss of function variants are amenable to a corrector drug and exploring how deep mutational scanning data could guide small molecule drug optimization.

Strengths

The analysis and statistical framework developed by the authors represent a significant advance. In particular, the study makes use of barcode-level internally replicated measurements to more accurately estimate measurement noise.

The framework allows variant effects to be compared across experimental conditions, a task that is currently hard to do with rigor. Thus, this framework will be applicable to a large number of existing and future deep mutational scanning experiments.

The authors refine their existing barcode transcription-based assay for GPCR signaling, and develop a clever "relay" new reporter system to boost signaling in a particular pathway. They show that these reporters can be used to measure both gain of function and loss of function effects, which many deep mutational scanning approaches cannot do.

The use of systematic approaches to integrate and then interrogate high-dimensional deep mutational scanning data is a big strength. For example, the authors applied PCA to the variant effect results from reporters for two different MC4R signaling pathways and were able to discover variants that biased signaling through one or the other pathway. This approach paves the way for analyses of higher dimensional deep mutational scans.

The authors use the deep mutational scanning data they collect to map how different variants impact small molecule agonists activate MC4R signaling. This is an exciting idea, because developing small-molecule protein-targeting therapeutics is difficult, and this manuscript suggests a new way to map small-molecule-protein interactions.

Weaknesses

The authors derive insights into the relationship between MC4R signaling through different pathways and its structure. While these make sense based on what is already known, the manuscript would be stronger if some of these insights were validated using methods other than deep mutational scanning.

Likewise, the authors use their data to identify positions where variants disrupt MC4R activation by one small molecule agonist but not another. They hypothesize these effects point to positions that are more or less important for the binding of different small molecule agonists. The manuscript would be stronger if some of these insights were explored further.

Impact

In this manuscript, the authors present new methods, including a statistical framework for analyzing deep mutational scanning data that will have a broad impact. They also generate MC4R variant effect data that is of interest to the GPCR community.

Reviewer #2 (Public review):

Summary:

This work highlights a novel role for platelet-derived growth factor (PDGF) in mitigating cellular senescence associated with age-related and painful intervertebral disc degeneration. Prior literature has demonstrated the importance of the accumulation of senescent cells in mediating many of the pathological effects associated with the degenerate disc joint such as inflammation and tissue breakdown. In this study, the authors treat clinically relevant human nucleus pulposus and annulus fibrosus cells from patients undergoing discectomy with recombinant PDGF-AB/BB for 5 days and then deep phenotyped the outcomes using bulk RNA sequencing. In addition, they irradiated healthy human disc cells which they subsequently treated with PDGF-AB/BB examining the expression of SASP-related markers and also PDGFRA receptor gene expression. Overall PDGF was able to down-regulate many senescent-associated pathways and the degenerate phenotype in IVD cells. Altered pathways were associated with neurogenesis, mechanical stimuli, metabolism, cell cycle, reactive oxygen species, and mitochondrial dysfunction. Overall the authors achieved their aims and the results by and large support their conclusions although improvements could be made to enhance the rigor of the study and findings.

Strengths:

A major strength of this study is the use of human cells from patients undergoing discectomy for disc herniation as well as access to healthy human cells. Investigating the role of PDGF regarding cellular senescence in the degenerate disc joint is a novel and underexplored area of research which is a significant contribution to the field of spine. This study highlights a potential target for addressing cellular senescence where most of the prior focus has been on senolytic drugs. Such studies have broad implications for other age-related diseases where senescence plays a major role. The use of transcriptomics and therefore an unbiased approach to investigating the role of PDGF is also considered a strength as are the follow-up studies involving irradiating healthy human disc cells and treating these cells with PDGF. The combined assessment of both nucleus pulposus and annulus fibrosus cells in the context of these studies adds to the impact.

Weaknesses:

A weakness of these studies lies in the lack of experimental details provided in the methodology including the rationale for such methods/conditions. Many details such as the specific culture models utilized, substrates, cell density, and media components are missing which impacts rigor. Such details would strengthen the manuscript and the ability to replicate and build on such work/findings. An additional weakness relates to qualitative data presented such as the B-galactosidase assay and immunofluorescence of senescence-associated proteins such as P21 and P16. Quantification of such data sets would greatly strengthen the studies and lend further support to the hypotheses. The study in its current form could be strengthened by the inclusion of mechanistic studies probing the downstream PDGF receptor-associated pathways for example specifically targeting or modulating the activity of the PDGF receptor PDGFRA including validation of the gene data for PDGFRA with protein level data to determine if the transcripts are being translated to protein. The claim that in annulus fibrosus cells, PDGF do not mediate their effects via the PDGFRA does not appear to be supported by the current data as only gene expression for the receptor was assessed with no functional or mechanistic studies being performed. Further discussion, interpretation, and direct comparison of the nucleus pulposus and annulus fibrosus data sets would be helpful for the readers. The magnitude of changes related to the effects of PDGF-BB on the S-phase in irradiated NP and AF cells between control and treated groups seem small making interpretation of these findings challenging.

Reviewer #2 (Public review):

Summary:

The manuscript offers an important contribution to the field of virology, especially concerning NNV entry mechanisms. The major strength of the study lies in the identification of MmMYL3 as a functional receptor for RGNNV and its role in macropinocytosis, mediated by the IGF1R-Rac1/Cdc42 signaling axis. This represents a significant advance in understanding NNV entry mechanisms beyond previously known receptors such as HSP90ab1 and HSC70. The data, supported by comprehensive in vitro and in vivo experiments, strongly justify the authors' claims about MYL3's role in NNV infection in marine medaka.

Strengths:

(1) The identification of MmMYL3 as a functional receptor for RGNNV is a significant contribution to the field. The study fills a crucial gap in understanding the molecular mechanisms governing NNV entry into host cells.

(2) The work highlights the involvement of IGF1R in macropinocytosis-mediated NNV entry and downstream Rac1/Cdc42 activation, thus providing a thorough mechanistic understanding of NNV internalization process. This could pave the way for further exploration of antiviral targets.

Reviewer #2 (Public review):

Summary:

This work investigates transcriptional responses to varying levels of transcription factors (TFs). The authors aim for gradual up- and down-regulation of three transcription factors GFI1B, NFE2, and MYB in K562 cells, by using a CRISPRa- and a CRISPRi line, together with sgRNAs of varying potency. Targeted single-cell RNA sequencing is then used to measure gene expression of a set of 90 genes, which were previously shown to be downstream of GFI1B and NFE2 regulation. This is followed by an extensive computational analysis of the scRNA-seq dataset. By grouping cells with the same perturbations, the authors can obtain groups of cells with varying average TF expression levels. The achieved perturbations are generally subtle, not reaching half or double doses for most samples, and up-regulation is generally weak below 1.5-fold in most cases. Even in this small range, many target genes exhibit a non-linear response. Since this is rather unexpected, it is crucial to rule out technical reasons for these observations.

Strengths:

The work showcases how a single dataset of CRISPRi/a perturbations with scRNA-seq readout and an extended computational analysis can be used to estimate transcriptome dose responses, a general approach that likely can be built upon in the future.

Weaknesses:

(1) The experiment was only performed in a single replicate. In the absence of an independent validation of the main findings, the robustness of the observations remains unclear.

(2) The analysis is based on the calculation of log-fold changes between groups of single cells with non-targeting controls and those carrying a guide RNA driving a specific knockdown. How the fold changes were calculated exactly remains unclear, since it is only stated that the FindMarkers function from the Seurat package was used, which is likely not optimal for quantitative estimates. Furthermore, differential gene expression analysis of scRNA-seq data can suffer from data distortion and mis-estimations (Heumos et al. 2023 (https://doi.org/10.1038/s41576-023-00586-w), Nguyen et al. 2023 (https://doi.org/10.1038/s41467-023-37126-3)). In general, the pseudo-bulk approach used is suitable, but the correct treatment of drop-outs in the scRNA-seq analysis is essential.

(3) Two different cell lines are used to construct dose-response curves, where a CRISPRi line allows gene down-regulation and the CRISPRa line allows gene upregulation. Although both lines are derived from the same parental line (K562) the expression analysis of Tet2, which is absent in the CRISPRi line, but expressed in the CRISPRa line (Figure S3A) suggests substantial clonal differences between the two lines. Similarly, the PCA in S4A suggests strong batch effects between the two lines. These might confound this analysis.

(4) The study uses pseudo-bulk analysis to estimate the relationship between TF dose and target gene expression. This requires a system that allows quantitative changes in TF expression. The data provided does not convincingly show that this condition is met, which however is an essential prerequisite for the presented conclusions. Specifically, the data shown in Figure S3A shows that upon stronger knock-down, a subpopulation of cells appears, where the targeted TF is not detected anymore (drop-outs). Also Figure 3B (top) suggests that the knock-down is either subtle (similar to NTCs) or strong, but intermediate knock-down (log2-FC of 0.5-1) does not occur. Although the authors argue that this is a technical effect of the scRNA-seq protocol, it is also possible that this represents a binary behavior of the CRISPRi system. Previous work has shown that CRISPRi systems with the KRAB domain largely result in binary repression and not in gradual down-regulation as suggested in this study (Bintu et al. 2016 (https://doi.org/10.1126/science.aab2956), Noviello et al. 2023 (https://doi.org/10.1038/s41467-023-38909-4)).

(5) One of the major conclusions of the study is that non-linear behavior is common. This is not surprising for gene up-regulation, since gene expression will reach a plateau at some point, but it is surprising to be observed for many genes upon TF down-regulation. Specifically, here the target gene responds to a small reduction of TF dose but shows the same response to a stronger knock-down. It would be essential to show that his observation does not arise from the technical concerns described in the previous point and it would require independent experimental validations.

(6) One of the conclusions of the study is that guide tiling is superior to other methods such as sgRNA mismatches. However, the comparison is unfair, since different numbers of guides are used in the different approaches. Relatedly, the authors point out that tiling sometimes surpassed the effects of TSS-targeting sgRNAs, however, this was the least fair comparison (2 TSS vs 10 tiling guides) and additionally depends on the accurate annotation of TSS in the relevant cell line.

(7) Did the authors achieve their aims? Do the results support the conclusions?: Some of the most important conclusions are not well supported because they rely on accurately determining the quantitative responses of trans genes, which suffers from the previously mentioned concerns.

(8) Discussion of the likely impact of the work on the field, and the utility of the methods and data to the community:<br /> Together with other recent publications, this work emphasizes the need to study transcription factor function with quantitative perturbations. Missing documentation of the computational code repository reduces the utility of the methods and data significantly.

Reviewer #2 (Public review):

Summary:

Soares et al characterize several P. falciparum exported proteins that localize to Maurer's Clefts (MCs), membrane structures formed in the host erythrocyte cytosol. MCs are thought to act as sorting stations that mediate the trafficking of effector proteins to the erythrocyte membrane, such as the surface adhesin and major virulence factor PfEMP1. While initially mobile within the host cytosol, MCs become anchored at the erythrocyte periphery around the time PfEMP1 appears on the RBC surface. While MC immobilization is thought to be important for the delivery of PfEMP1 onto the erythrocyte surface, this hypothesis has remained untested due to the lack of mutants that prevent anchoring. The study begins by determining the sequence features able to mediate the export of PF3D7_0830300 and MSRP6, both PEXEL-Negative Exported Proteins (PNEPs) with signal peptides. The authors show that in both proteins, a region downstream of the signal peptide is sufficient to mediate export, indicating the mature N-terminus is also important for the translocation of this type of PNEP, similar to other classes of exported proteins. Surprisingly, an additional C-terminal region of MSRP6 is also sufficient to mediate export when placed downstream of the signal peptide in the absence of other MSRP6 features. This region also mediates recruitment to MCs and was used as BioID bait to identify proximal MC proteins, several of which form a complex with MSRP6. Strikingly, disruption of certain MSRP6 interacting proteins (PeMP2, PIESP2, and Pf332) abolishes MC anchoring and in some cases also results in major changes in MC morphology. Surprisingly, neither PfEMP1 surface display nor cytoadhesion of infected RBCs is impacted in these mutants. This study features an impressive array of genetically modified parasites and will be of broad interest in providing the first functional analysis of MC anchoring, challenging the prevailing model for PfEMP1 trafficking within the infected RBC.

Strengths:

(1) The first section of the paper presents an in-depth dissection of the features that enable the export of signal peptide-containing PNEPs, confirming the mature N-terminus is sufficient for export across all known types of exported proteins. While it remains unknown how these features enable export, the results reinforce the universal importance of the mature N-terminus, whether generated by signal peptidase or Plasmepsin 5.

(2) The discovery that a C-terminal region of MSRP6 (MAD) is also sufficient for export is novel. The authors suggest this may be the result of piggybacking on another exported protein, although the discussion acknowledges there are challenges with this model since unfolding by PTEX would be expected to disrupt these interactions. An alternative might be considered: the related protein MSRP7 is also exported but consists essentially of a signal peptide and MSP7-like domain without the large N-terminal region found in MSRP6. Presumably, the mature N-terminus of MSRP7 mediates export. If MSRP6 is derived from an exported predecessor composed only of the MSP7-like domain (like MSRP7), the MAD domain might retain the ancestral export information near the beginning of the MSP7-like domain. If this were the case, then the MAD domain (3cd region) should only be sufficient to mediate export when positioned immediately after the signal peptide as in the experiment in Fig 3C (SP-3cd-GFP). It would be interesting to determine if an SP-GFP-3cd construct is exported.

(3) Disruption of PeMP2, PIESP2 or Pf332 is found to prevent MC anchoring. This is the most exciting part of the study as it provides the first set of mutants that interfere with anchoring, enabling the surprising observation that MC immobilization is not important for PfEMP1 surface display or cytoadhesion. The MC movement assay is a nice way to visualize anchoring and would be strengthened by a quantitative measure of colocalization between the time-lapse images (ie, Pearson correlation coefficient) to enable a statistical test. The use of SLI to specifically activate a var gene of choice is an exciting new approach that will be of great use to the PfEMP1 field together with the semi-automated binding assay that helps to increase throughput and reduce bias.

Weaknesses:

(1) At least two of the MSRP6 complex members were found to depend on other complex members for MC trafficking: PeMP3 depends on MSRP6 and Pf332 depends on PIESP2 (previously shown by Zhang et al 2018 and confirmed in the present study). While the authors disrupted all seven MSRP6 complex members, the impact on the trafficking of the other complex members was not systematically investigated. It would be particularly interesting to know which (if any) complex members are required for MC recruitment of PeMP2 since this protein is also needed for MC anchoring.

(2) Some images of exported puncta are interpreted as localization to the MCs without a co-marker. Since other compartments have been identified in the RBC cytosol in addition to MCs (ie, J dots), an MC co-marker would help to verify these actually correspond to MCs. For example, in Figure 5B, GEXP18 gives an exported punctate appearance but lack of co-localization with SBP1 in Fig S2B shows that this does not correspond to MCs.

(3) The authors show MAHRP2 localization is not impacted in their PIESP2 and Pf332 mutants and this is interpreted to indicate the tether structures are not disrupted. However, this conclusion requires actual analysis of the tether structures by electron microscopy since MAHRP2 association to MCs may not require tether integrity and could persist even if the tethers are altered or disrupted. Otherwise, this statement should be adjusted. Additionally, since T2A skipping efficiency can vary between constructs, it would be a good idea to perform a western blot to ensure that the SBP1-GFP and MAHRP2-mScarlet signals in Figure 8D,F reflect separated proteins.

(4) The trypsin assays to monitor PfEMP1 surface display would benefit from a more detailed explanation of how the results were interpreted. For instance, though perhaps less intense than in the PIESP2, Pf332, and MSRP6 mutants, a Var01-protected fragment is also seen in the SBP1 mutant. Additionally, a protected fragment is indicated for most of the SBP1N controls (asterisk). As per the author's experimental design (lines 956-957), does this indicate that the RBC membrane was partially compromised during the experiment? In line 505, the trypsin assay data in the mutants is interpreted relative to the parent IT4var01-HA line but no data is shown for the parent.

Reviewer #2 (Public review):

The study by Deganutti and co-workers is a methodological report on an adaptive sampling approach, multiple walker supervised molecular dynamics (mwSuMD), which represents an improved version of the previous SuMD.<br /> Case-studies concern complex conformational transitions in a number of G protein Coupled Receptors (GPCRs) involving long time-scale motions such as binding-unbinding and collective motions of domains or portions. GPCRs are specialized GEFs (guanine nucleotide exchange factors) of heterotrimeric Gα proteins of the Ras GTPase superfamily. They constitute the largest superfamily of membrane proteins and are of central biomedical relevance as privileged targets of currently marketed drugs.<br /> MwSuMD was exploited to address:

a) binding and unbinding of the arginine-vasopressin (AVP) cyclic peptide agonist to the V2 vasopressin receptor (V2R);<br /> b) molecular recognition of the β2-adrenergic receptor (β2-AR) and heterotrimeric GDP-bound Gs protein;<br /> c) molecular recognition of the A1-adenosine receptor (A1R) and palmotoylated and geranylgeranylated membrane-anchored heterotrimeric GDP-bound Gi protein;<br /> d) the whole process of GDP release from membrane-anchored heterotrimeric Gs following interaction with the glucagon-like peptide 1 receptor (GLP1R), converted to the active state following interaction with the orthosteric non-peptide agonist danuglipron.

The revised version has improved clarity and rigor compared to the original also thanks to the reduction in the number of complex case studies treated superficially.<br /> The mwSuMD method is solid and valuable, has wide applicability and is compatible with the most world-widely used MD engines. It may be of interest to the computational structural biology community.<br /> The huge amount of high-resolution data on GPCRs makes those systems suitable, although challenging, for method validation and development.<br /> While the approach is less energy-biased than other enhanced sampling methods, knowledge, at the atomic detail, of binding sites/interfaces and conformational states is needed to define the supervised metrics, the higher the resolution of such metrics is the more accurate the outcome is expected to be. Definition of the metrics is a user- and system-dependent process.

Reviewer #3 (Public review):

Summary:

Chang et al. investigated the mechanisms governing collagen fibrillogenesis, firstly demonstrating that cells within tail tendons are able to uptake exogenous collagen and use this to synthesize new collagen-1 fibrils. Using an endocytic inhibitor, the authors next showed that endocytosis was required for collagen fibrillogenesis and that this process occurs in a circadian rhythmic manner. Using knockdown and overexpression assays, it was then demonstrated that collagen fibril formation is controlled by vacuolar protein sorting 33b (VPS33b), and this VPS33b-dependent fibrillogenesis is mediated via Integrin alpha-11 (ITGA11). The authors also demonstrated increased expression of VPS33b and ITGA11 at the gene level in fibroblasts from patients with idiopathic pulmonary fibrosis (IPF), and greater expression of these proteins in both lung samples from IPF patients and in chronic skin wounds, indicating that endocytic recycling is disrupted in fibrotic diseases. Finally, the authors performed knockdown assays in patient derived IPF fibroblasts to confirm that silencing of VPS33b and ITGA11 results in a decrease in recycling of exogenous collagen-1

Strengths:

The authors have performed a comprehensive functional analysis of the regulators of endocytic recycling of collagen, providing compelling evidence that VPS33b and ITGA11 are crucial regulators of this process, and that this endocytic recycling becomes disrupted in fibrotic diseases.

Reviewer #2 (Public review):

Summary:

This important study provides a mechanism that can explain the rapid diversification of poison-antidote pairs (wtf genes) in fission yeast: recombination between existing genes.

Strengths:

The authors analyzed the diversity of wtf in S. pombe strains, and found pervasive copy number variations. They further detected signals of recurrent recombination in wtf genes. To address whether recombination can generate novel wtf genes, the authors performed artificial recombination between existing wft genes, and showed that indeed a new wtf can be generated: the poison cannot be detoxified by the antidotes encoded by parental wtf genes but can be detoxified by own antidote.

Weaknesses:

The study can benefit from demonstrating that the novel poison-antidote constructed by the authors can serve as a meiotic driver.

Reviewer #2 (Public review):

Summary:

Definition of the role of CdK5 in circadian locator activity and light induced neural activity in the mouse SCN in-vivo revealing its mode of action through PKA-CaMK-CREB signaling pathway.

Strengths:

The experimental approaches are carried from in-vivo, to cellular and molecular level and provide first evidence for the specific involvement of CdK5 in light-induced phase advance of the free-running rhythm.

Weaknesses:

The behavioral analyses are limited to some selected parameters.

Downstream effects on circadian oscillation of gene expression and physiological functions in other brain regions, organs is missing.

Comments on revisions:

I am happy with the manuscript in its present form.

Reviewer #2 (Public review):

Summary:

The manuscript by Murphy et al. titled "Change point estimation by the mouse medial prefrontal cortex during probabilistic reward learning" investigated the role of the mPFC in the exploitation of task structure. Previous work had shown that monkeys and humans exploit predictable task structures (e.g., switching rapidly when heavily trained a reversal learning task), but whether this was also the case for mice was not known. To test this, Murphy et al. trained head-fixed mice on a two-armed bandit task in which the contingencies reversed when mice met a performance criterion (10 trials choosing the better option) plus an additional random number of trials (referred to as Lrandom). They found that as the length of Lrandom increased, mice began to exhibit pre-emptive switching in their choices as if they were expecting and/or anticipating the reversal to occur. They report that unilateral lesions of the mPFC (ACC + MO) led to earlier pre-emptive switching (although I found this part of the manuscript the most challenging to understand) and faster post-reversal switching that they argue reflects an impairment in the proper estimation of the reversal. They also report that this requires inter-hemispheric coordination because bilateral lesions did not further impair this estimation. Optogenetic inhibition just prior to the mouse making a choice recapitulated some of the behavioral metrics observed in the mPFC lesioned animals. Finally, the authors developed a novel hybrid belief-choice kernel model to provide a computational approach to quantifying these behavioral differences.

Strengths:

The paper is extremely well written and was an absolute pleasure to read. The results are novel and provide exciting (although not surprising) evidence that mice exploit task structures to earn rewards. Moreover, the experiments were well-designed and included appropriate controls and/or control conditions that support their findings.

Weaknesses:

Some of the results need to be clarified and/or language changed to ensure that readers will understand. Restricting analyses to expert mice that show the predicted effect is problematic.

Reviewer #2 (Public review):

Summary:

This study analyzes protein abundance data from six VAMP-seq experiments, comprising over 31,000 single amino acid substitutions, to understand how different amino acids contribute to maintaining cellular protein levels. The authors develop substitution matrices that capture the average effect of amino acid changes on protein abundance in different structural contexts (buried vs. exposed residues). Their key finding is that these simple structure-based matrices can predict mutational effects on abundance with accuracy comparable to more complex physics-based stability calculations (ΔΔG).

Major strengths:

(1) The analysis focuses on a single molecular phenotype (abundance) measured using the same experimental approach (VAMP-seq), avoiding confounding factors present when combining data from different phenotypes (e.g., mixing stability, activity, and fitness data) or different experimental methods.

(2) The demonstration that simple structural features (particularly solvent accessibility) can capture a significant portion of mutational effects on abundance.

(3) The practical utility of the matrices for analyzing protein interfaces and identifying functionally important surface residues.

Major weaknesses:

(1) The statistical rigor of the analysis could be improved. For example, when comparing exposed vs. buried classification of interface residues, or when assessing whether differences between prediction methods are significant.

(2) The mechanistic connection between stability and abundance is assumed rather than explained or investigated. For instance, destabilizing mutations might decrease abundance through protein quality control, but other mechanisms like degron exposure could also be at play.

(3) The similar performance of simple matrix-based and complex physics-based predictions calls for deeper analysis. A systematic comparison of where these approaches agree or differ could illuminate the relationship between stability and abundance. For instance, buried sites showing exposed-like behavior might indicate regions of structural plasticity, while the link between destabilization and degradation might involve partial unfolding exposing typically buried residues. The authors have all the necessary data for such analysis but don't fully exploit this opportunity.

(4) The pooling of data across proteins to construct the matrices needs better justification, given the observed differences in score distributions between proteins (for example, PTEN's distribution is shifted towards high abundance scores while ASPA and PRKN show more binary distributions).

(5) Some key methodological choices require better justification. For example, combining "to" and "from" mutation profiles for PCA despite their different behaviors, or using arbitrary thresholds (like 0.05) for residue classification.

The authors largely achieve their primary aim of showing that simple structural features can predict abundance changes. However, their secondary goal of using the matrices to identify functionally important residues would benefit from more rigorous statistical validation. While the matrices provide a useful baseline for abundance prediction, the paper could offer deeper biological insights by investigating cases where simple structure-based predictions differ from physics-based stability calculations.

This work provides a valuable resource for the protein science community in the form of easily applicable substitution matrices. The finding that such simple features can match more complex calculations is significant for the field. However, the work's impact would be enhanced by a deeper investigation of the mechanistic implications of the observed patterns, particularly in cases where abundance changes appear decoupled from stability effects.

Reviewer #2 (Public review):

Summary:

In this manuscript, the authors report novel and exciting findings delineating a non-transcriptional mechanism whereby glucocorticoids desensitize CRH neurons to NE in response to somatic stress. The authors find that this desensitization induced by CORT 1. persists more than 18h, 2. reduces surface expression of AR1bR (NE receptors) by redirecting trafficking from rapid recycling to late endosomal pools and lysosomes, 3. is dependent on NE binding to the AR1bR, 4. involves cellular nitrosylation, 5. involves ubiquitination of beta-arrestin, and 5. involves interactions between glucocorticoid receptors and AR1bs, glucocorticoid receptors and ubiquitinated beta-arrestin, and AR1b and ubiquitinated beta-arrestin. While the authors do not directly provide evidence for a trimeric complex composed of these three proteins, their data that CORT causes translocation of these dimeric complexes to the cell nucleus suggests it is likely. Overall, these results are highly informative for understanding novel mechanisms mediating glucocorticoid regulation of GPCRs.

Strengths:<br /> - Good rationale for each experiment, which describes many parts of the CORT-NE desensitization mechanism<br /> - Great discussion of limitations of the approaches and the parts of the mechanism we do not fully understand yet<br /> - Appropriate approaches for questions being answered<br /> - Describes a highly novel CORT mechanism that non-transcriptionally switches GPCR trafficking dynamics, something that could have far reaching implications for other GPCRs involved in stress responses

Weaknesses:<br /> - Unclear how this mechanism would generalize to other stressor modalities. Restraint stress is a somatic stressor, but can also be considered a psychological stressor (model of depression-like behavior). A purely somatic stressor might increase the robustness of this phenomenon.<br /> - Remains unknown how nitrosylation plays into the mechanism in terms of specific proteins affected by CORT (GRK2, endophilin, clathrin possibilities)

Reviewer #2 (Public Review):

Campbell et al have described the dynamic pattern of two Bmps (Bmp5, Bmp4), one of their receptors (Acvr2a), putative joint inhibitors of the Bmp & Wnt pathways (sostdc1, apcdd1) and an effector of Bmp signaling phosph-Smad, in the experimentally tractable sterlet sturgeon to better understand the role of Bmp signaling in electroreceptor development. The role of Bmp signaling is poorly understood in the lateral line system. Furthermore, the development of electroreceptors in ampullary organs remains poorly understood as most recent analysis of lateral line development has focused on model organisms Xenopus and zebrafish, which the electroreceptors have been lost. They show that expression of these players is consistent with a role for Bmp signaling in electroreceptor development. Furthermore, they show that Bmp5 crispants have fewer ampullary organs. However, inhibition of Bmp signaling with the small molecule inhibitor DMH1 for 20 hours starting from stage 36 after hatching and before ampullary organ development results in supernumerary ampullary organ development. These strikingly different results lead the authors to conclude that Bmp signaling has opposing roles in ampullary organ development.

These observations are interesting and the conclusions are supported by the data presented and the study makes important contributions to our understanding of the role of Bmp signaling in electroreceptor development in lateral line development. However, the study opens and leaves unresolved a number of questions. While a definitive answer to these questions may be outside the scope of this paper, some additional experiments may help strengthen the paper.

Reviewer #2 (Public review):

Summary:

This study utilized two complimentary techniques (EEG and 7T MRI/MRS) to directly test a theory of dyslexia: the neural noise hypothesis. The authors report finding no evidence to support an excitatory/inhibitory balance, as quantified by beta in EEG and Glutamate/GABA ratio in MRS. This is important work and speaks to one potential mechanism by which increased neural noise may occur in dyslexia.

Strengths:

This is a well conceived study with in depth analyses and publicly available data for independent review. The authors provide transparency with their statistics and display the raw data points along with the averages in figures for review and interpretation. The data suggest that an E/I balance issue may not underlie deficits in dyslexia and is a meaningful and needed test of a possible mechanism for increased neural noise.

Weaknesses:

The researchers did not include a visual print task in the EEG task, which limits analysis of reading specific regions such as the visual word form area, which is a commonly hypoactivated region in dyslexia. This region is a common one of interest in dyslexia, yet the researchers measured the I/E balance in only one region of interest, specific to the language network.

Reviewer #2 (Public review):

Summary:

This study provides a valuable data set showing changes in the spatial organization of synaptic proteins at the retinogeniculate connection during a developmental period of active axonal and synaptic remodeling. The data collected by STORM microscopy is state-of-the-art in terms of the high-resolution view of the presynaptic components of a plastic synapse. The revision has addressed many, but not all, of the initial concerns about the authors interpretation of their data. However, with the revisions, the manuscript has become very dense and difficult to follow.

Strengths:

The data presented is of good quality and provides an unprecedented view at high resolution of the presynaptic components of the retinogeniculate synapse during active developmental remodeling. This approach offers an advance to the previous mouse EM studies of this synapse because the CTB label allows identification of the eye from which the presynaptic terminal arises.

Weaknesses:

From these data the authors conclude that eye-specific increase in mAZ synapse density occur over retinogeniculate refinement, that sAZ synapses cluster close to mAZ synapses over age, and that this process depends on spontaneous activity and proximity to eye-specific mAZ synapses. While the interpretation of this data set is much more grounded in this revised submission, some of the authors' conclusions/statements still lack convincing supporting evidence.<br /> This includes:

(1) The conclusion that multi-active zone synapses are loci for synaptic clustering. This statement, or similar ones (e.g., line 407) suggest that mAZ synapses actively or through some indirect way influence the clustering of sAZ synapses. There is no evidence for this. Clustering of retinal synapses are in part due to the fact that retinal inputs synapse on the proximal dendrites. With increased synaptogenesis, there will be increased density of retinal terminals that are closely localized. And with development, perhaps sAZ synapses mature into mAZ synapses. This scenario could also explain a large part of this data set.

(2) The conclusion that, "clustering depends on spontaneous retinal activity" could be misleading to the reader given that the authors acknowledge that their data is most consistent with a failure of synaptogenesis in the mutant mice (in the rebuttal). Additionally clustering does occur in CTB+ projections around mAZ synapses.

(3). Line 403: "Since mAZ synapses are expected to have a higher release probability, they likely play an important role in driving plasticity mechanisms reliant on neurotransmission.":What evidence do the authors have that mAZ are expected to have higher release probability?

Reviewer #2 (Public review):

Summary:

This paper documents a compelling attempt to accurately determine the locations and boundaries of the anatomically and functionally defined layers in macaque primary visual cortex using voltage signals recorded from a high-density electrode array that spans the full depth of cortex with contacts at 20 um spacing. First, the authors attempt to use current source density (CSD) analysis to determine layer locations, but they report a striking failure because the results vary greatly from one electrode penetration to the next and because the spatial resolution of the underlying local field potential (LFP) signal is coarse compared to the electrical contact spacing. The authors therefore turn to examining higher frequency signals related to action potentials and provide evidence that these signals reflect changes in neuronal size and packing density, response latency and visual selectivity, which taken together can advance the state-of-the-art accuracy in making layer assignments from in vivo recordings.

Strengths:

There is a lot of nice data to look at in this paper that show interesting quantities as a function of depth in V1. Bringing all of these together offers the reader a rich data set: CSD, action potential shape, response power and coherence spectrum, and post-stimulus time response traces. Furthermore, data are displayed as a function of eye (dominant or non-dominant) and for achromatic and cone-isolating stimuli.

This paper takes a strong stand in pointing out weaknesses in the ability of CSD analysis to make consistent determinations about cortical layering in V1. Many researchers have found CSD to be problematic, and the observations here may be important to motivate other researchers to carry out rigorous comparisons and publish their results, even if they reflect negatively on the value of CSD analysis.

The paper provides a thoughtful, practical and comprehensive recipe for assigning traditional cortical layers based on easily-computed metrics from electophysiological recordings in V1, and this is likely to be useful for electrophysiologists who are now more frequently using high-density electrode arrays.

Weaknesses:

Considerable space is taken in pointing out features that are well known, for example, the latency difference associated with different retinogeniculate pathways, the activity level differences associated with input layers, and the action potential shape differences associated with white vs. gray matter. These have been used for decades as indicators of depth and location of recordings in visual cortex as electrodes were carefully advanced. High density electrodes allow this type of data to now be collected in parallel, but at discrete, regular sampling points. Perhaps more emphasis could be placed on developing a rigorous analysis of how variable vs. reproducible are quantitative metrics of these features across penetrations, as a function of distance or functional domain, and from animal to animal, but this paper certainly makes a substantial push in this direction.

Another important piece of information for assessing the ability to determine layers from spiking activity is to carry out post-mortem histological processing so that the layer determination made in vivo can be compared to anatomical layering. However, histological methods also suffer from distortion and noise, thus it remains to be seen how much can ultimately be gained by integrating histology with the physiological methods explored here.

Overall

Overall, this paper makes a compelling argument in favor of using action potentials and stimulus driven responses, instead of CSD measurements, to assign cortical layers to electrode contacts in V1. The rich presentation of data, combined with the authors' highly educated interpretation and speculation about how useful such measurements will be for layer assignment make this an important paper for many labs using high-density electrodes. It is easy to agree with much of what is postulated here and to hope that we will soon have reliable, quantitative methods to make layer assignments that will be meaningful in terms of the differentiated roles of single neurons in cortical computation. How much this will end up corresponding to the canonical layer numbering that has been used for many decades will be interesting to see.

Comments on revisions:

I found that the authors addressed my main concerns to the degree they were able. They improved the consistency of language and figures, and they added some useful quantification.

Reviewer #2 (Public review):

Summary:

This interesting paper examines the earliest steps in progesterone-induced frog oocyte maturation, an example of non-genomic steroid hormone signaling that has been studied for decades but is still very incompletely understood. In fish and frog oocytes it seems clear that mPR proteins are involved, but exactly how they relay signals is less clear. In human sperm, the lipid hydrolase ABHD2 has been identified as a receptor for progesterone, and so the authors here examine whether ABHD2 might contribute to progesterone-induced oocyte maturation as well. The main results are:

(1) Knocking down ABHD2 makes oocytes less responsive to progesterone, and ectopically expressing ABHD2.S (but not the shorter ABHD2.L gene product) partially rescues responsiveness. The rescue depends upon the presence of critical residues in the protein's conserved lipid hydrolase domain, but not upon the presence of critical residues in its acyltransferase domain.

(2) Treatment of oocytes with progesterone causes a decrease in sphingolipid and glycerophospholipid content within 5 min. This is accompanied by an increase in LPA content and arachidonic acid metabolites. These species may contribute to signaling through GPCRs. Perhaps surprisingly, there was no detectable increase in sphingosine-1-phosphate, which might have been expected given the apparent substantial hydrolysis of sphingolipids. The authors speculate that S1P is formed and contributes to signaling but diffuses away.

(3) Pharmacological inhibitors of lipid-metabolizing enzymes support, for the most part, the inferences from the lipidomics studies, although there are some puzzling findings. The puzzling findings may be due to uncertainty about whether the inhbitors are working as advertised.

(4) Pharmacological inhibitors of G-protein signaling support a role for G-proteins and GPCRs in this signaling, although again there are some puzzling findings.

(5) Reticulocyte expression supports the idea that mPRβ and ABHD2 function together to generate a progesterone-regulated PLA2 activity.

(6) Knocking down or inhibiting ABHD2 inhibited progesterone-induced mPRβ internalization, and knocking down ABHD2 inhibited SNAP25∆20-induced maturation.

Strengths:<br /> All in all, this could be a very interesting paper and a nice contribution. The data add a lot to our understanding of the process, and, given how ubiquitous mPR and AdipoQ receptor signaling appear to be, something like this may be happening in many other physiological contexts.

Weaknesses:

I have several suggestions for how to make the main points more convincing.

Main criticisms:

(1) The ABHD2 knockdown and rescue, presented in Fig 1, is one of the most important findings. It can and should be presented in more detail to allow the reader to understand the experiments better. E.g.: the antisense oligos hybridize to both ABHD2.S and ABHD2.L, and they knock down both (ectopically expressed) proteins. Do they hybridize to either or both of the rescue constructs? If so, wouldn't you expect that both rescue constructs would rescue the phenotype, since they both should sequester the AS oligo? Maybe I'm missing something here.

In addition, it is critical to know whether the partial rescue (Fig 1E, I, and K) is accomplished by expressing reasonable levels of the ABHD2 protein, or only by greatly overexpressing the protein. The author's antibodies do not appear to be sensitive enough to detect the endogenous levels of ABHD2.S or .L, but they do detect the overexpressed proteins (Fig 1D). The authors could thus start by microinjecting enough of the rescue mRNAs to get detectable protein levels, and then titer down, assessing how low one can go and still get rescue. And/or compare the mRNA levels achieved with the rescue construct to the endogenous mRNAs.

Finally, please make it clear what is meant by n = 7 or n = 3 for these experiments. Does n = 7 mean 7 independently lysed oocytes from the same frog? Or 7 groups of, say, 10 oocytes from the same frog? Or different frogs on different days? I could not tell from the figure legends, the methods, or the supplementary methods. Ideally one wants to be sure that the knockdown and rescue can be demonstrated in different batches of oocytes, and that the experimental variability is substantially smaller than the effect size.

(2) The lipidomics results should be presented more clearly. First, please drop the heat map presentations (Fig 2A-C) and instead show individual time course results, like those shown in Fig 2E, which make it easy to see the magnitude of the change and the experiment-to-experiment variability. As it stands, the lipidomics data really cannot be critically assessed.

[Even as heat map data go, panels A-C are hard to understand. The labels are too small, especially on the heat map on the right side of panel B. And the 25 rows in panel C are not defined (the legend makes me think the panel is data from 10 individual oocytes, so are the 25 rows 25 metabolites? If so, are the individual oocyte data being collapsed into an average? Doesn't that defeat the purpose of assessing individual oocytes?) And those readers with red-green colorblindness (8% of men) will not be able to tell an increase from a decrease. But please don't bother improving the heat maps; they should just be replaced with more-informative bar graphs or scatter plots.]

(3) The reticulocyte lysate co-expression data are quite important, and are both intriguing and puzzling. My impression had been that to express functional membrane proteins, one needed to add some membrane source, like microsomes, to the standard kits. Yet it seems like co-expression of mPR and ABHD2 proteins in a standard kit is sufficient to yield progesterone-regulated PLA2 activity. I could be wrong here-I'm not a protein expression expert-but I was surprised by this result, and I think it is critical that the authors make absolutely certain that it is correct. Do you get much greater activities if microsomes are added? Are the specific activities of the putative mPR-ABHD2 complexes reasonable?

Comments on revisions:

The authors have satisfied my concerns with their response letter and revisions.

Reviewer #2 (Public review):

Summary:

Sullivan and Bashaw delve into the mechanisms that drive neural circuit assembly, and specifically, into the regulation of cell surface proteins that mediate axon pathfinding. During nervous system development, axons must traverse a molecularly and physically complex extracellular milieu to reach their synaptic targets. A fundamental, conserved repulsive signaling pathway is initiated by the Slit-Robo ligand-receptor pair. Robo, expressed on axon growth cones, binds Slit, secreted by midline cells, to prevent "pre-crossing" and "re-crossing" of axons at the midline. To control this repulsion, Robo surface levels are tightly regulated. In Drosophila, Commissureless (Comm) downregulates Robo surface levels and is required for axon crossing at the midline. Several studies suggest that PY motifs in Comm are required to localize Robo to endosomes. PY motifs have been shown to bind WW-domain containing proteins including the ubiquitin ligase Nedd4 family, so the authors propose that Comm may regulate Robo through Nedd4 interactions. Previous studies have hinted at a role for Nedd4-mediated ubiquitination of Comm in regulation of Robo localization, but there have also been conflicting data. For example, Comm mutants that are unable to be ubiquitinated mimic wild-type Comm, suggesting that ubiquitination of Comm is not required for regulation of Robo. The current study utilizes a suite of genetic analyses in Drosophila to resolve discrepancies pertaining to the mode of Comm-dependent regulation of Robo1 and proposes that Comm acts as an adapter for the Nedd4 ubiquitin ligase to recognize Robo1 as a substrate. The authors also demonstrate that Nedd4 is indeed required for midline crossing.

Strengths:

While this work is more incremental rather than field-shifting, it is nonetheless an excellent example of a rigorous, thorough analysis that culminates in enriching our mechanistic understanding of how neurons regulate cell-surface receptors in a spatiotemporal manner to control fundamental steps of circuit wiring. The experimental approach is thorough, and the manuscript is extremely well-written.

Weaknesses:

Some key experiments (eg. complex formation) were performed in cell culture in an overexpression background. However, updated experiments demonstrated complex formation using immunoprecipitation in tissues overexpression the corresponding components. Also, there was a missed opportunity to bolster the model proposed by using Comm PY mutants in several experiments.

Comments on revised version:

The revised manuscript bolsters the authors' conclusions and now provides evidence for interactions in tissue. No additional experiments are needed.

Reviewer #2 (Public review):

Summary:

Gao et al. investigated the change of aggression strategies by the social experience and its biological significance by using Drosophila. Two modes of inter-male aggression in Drosophila are known: lunging, high-frequency but weak mode, and tussling, low-frequency but more vigorous mode. Previous studies have mainly focused on the lunging. In this paper, the authors developed a new behavioral experiment system for observing tussling behavior and found that tussling is enhanced by group rearing while lunging is suppressed. They then searched for neurons involved in the generation of tussling. Although olfactory receptors named Or67d and Or65a have previously been reported to function in the control of lunging, the authors found that these neurons do not function in the execution of tussling, and another olfactory receptor, Or47b, is required for tussling, as shown by the inhibition of neuronal activity and the gene knockdown experiments. Further optogenetic experiments identified a small number of central neurons pC1[SS2] that induce the tussling specifically. In order to further explore the ecological significance of the aggression mode change in group rearing, a new behavioral experiment was performed to examine territorial control and mating competition. Finally, the authors found that differences in the social experience (group vs. solitary rearing) are important in these biologically significant competitions. These results add a new perspective to the study of aggressive behavior in Drosophila. Furthermore, this study proposes an interesting general model in which the social experience-modified behavioral changes play a role in reproductive success.

Strengths:

A behavioral experiment system that allows stable observation of tussling, which could not be easily analyzed due to its low frequency, would be very useful. The experimental setup itself is relatively simple, just the addition of a female to the platform, so it should be applicable to future research. The finding about the relationship between the social experience and the aggression mode change is quite novel. Although the intensity of aggression changes with the social experience was already reported in several papers (Liu et al., 2011, etc), the fact that the behavioral mode itself changes significantly has rarely been addressed and is extremely interesting. The identification of sensory and central neurons required for the tussling makes appropriate use of the genetic tools and the results are clear. A major strength of the neurobiology in this study is the finding that another group of neurons (Or47b-expressing olfactory neurons and pC1[SS2] neurons), distinct from the group of neurons previously thought to be involved in low-intensity aggression (i.e. lunging), function in the tussling behavior. Further investigation of the detailed circuit analysis is expected to elucidate the neural substrate of the conflict between the two aggression modes.

Weaknesses:

The experimental systems examining the territory control and the reproductive competition in Figure 5 are novel and have advantages in exploring their biological significance. However, at this stage, the authors' claim is weak since they only show the effects of age and social experience on territorial and mating behaviors, but do not experimentally demonstrate the influence of aggression mode change itself. In the Abstract, the authors state that these findings reveal how social experience shapes fighting strategies to optimize reproductive success. This is the most important perspective of the present study, and it would be necessary to show directly that the change of aggression mode by social experience contributes to reproductive success.

In addition, a detailed description of the tussling is lacking. For example, the authors state that the tussling is less frequent but more vigorous than lunging, but while experimental data are presented on the frequency, the intensity seems to be subjective. The intensity is certainly clear from the supplementary video, but it would be necessary to evaluate the intensity itself using some index. Another problem is that there is no clear explanation of how to determine the tussling. A detailed method is required for the reproducibility of the experiment.

Reviewer #2 (Public Review):

Summary:

The manuscript claims to present a novel method for direct imaging of electric field networks from EEG data with higher spatiotemporal resolution than even fMRI. Validation of the EEG reconstructions with EEG/FMRI, EEG, and iEEG datasets are presented. Subsequently, reconstructions from a large EEG dataset of subjects performing a gambling task are presented.

Strengths:

If true and convincing, the proposed theoretical framework and reconstruction algorithm can revolutionize the use of EEG source reconstructions.

Weaknesses:

There is very little actual information in the paper about either the forward model or the novel method of reconstruction. Only citations to prior work by the authors are cited with absolutely no benchmark comparisons, making the manuscript difficult to read and interpret in isolation from their prior body of work.

Reviewer #2 (Public review):

Summary:

Host-derived lipids are an important factor during Mtb infection. In this study, using CRISPR knockouts of genes involved in fatty acid uptake and metabolism, the authors claim that a compromised uptake, storage, or metabolism of fatty acid restricts Mtb growth upon infection. Further, the authors claim that the mechanism involves increased glycolysis, autophagy, oxidative stress, pro-inflammatory cytokines, and nutrient limitation. The authors also claim that impaired lipid droplet formation restricts Mtb growth. However, promoting lipid droplet biogenesis does not reverse/promote Mtb growth.

Strengths:

The strength of the study is the use of clean HOXB8-derived primary mouse macrophage lines for generating CRISPR knockouts.

Weaknesses:

There are many weaknesses of this study, they are clubbed into four categories below

(1) Evidence and interpretations: The results shown in this study at several places do not support the interpretations made or are internally contradictory or inconsistent. There are several important observations, but none were taken forward for in-depth analysis. A<br /> a) The phenotypes of PLIN2-/-, FATP1-/-, and CPT-/- are comparable in terms of bacterial growth restriction; however, their phenotype in terms of lipid body formation, IL1B expression, etc., are not consistent. These are interesting observations and suggest additional mechanisms specific to specific target genes; however, clubbing them all as altered fatty acid uptake or catabolism-dependent phenotypes takes away this important point. b) Finding the FATP1 transcript in the HOXB8-derived FATP1-/- CRISPR KO line is a bit confusing. There is less than a two-fold decrease in relative transcript abundance in the KO line compared to the WT line, leaving concerns regarding the robustness of other experiments as well using FATP1-/- cells.<br /> c) No gene showing differential regulation in FATP-/- macrophages, which is very surprising.<br /> d) ROS measurements should be done using flow cytometry and not by microscopy to nail the actual pattern.

(2) Experimental design: For a few assays, the experimental design is inappropriate<br /> a) For autophagy flux assay, immunoblot of LC3II alone is not sufficient to make any interpretation regarding the state of autophagy. This assay must be done with BafA1 or CQ controls to assess the true state of autophagy.<br /> b) Similarly, qPCR analyses of autophagy-related gene expression do not reflect anything on the state of autophagy flux.

(3) Using correlative observations as evidence:<br /> a) Observations based on RNAseq analyses are presented as functional readouts, which is incorrect.<br /> b) Claiming that the inability to generate lipid droplets in PLIN2-/- cells led to the upregulation of several pathways in the cells is purely correlative, and the causal relationship does not exist in the data presented.

(4) Novelty: A few main observations described in this study were previously reported. That includes Mtb growth restriction in PLIN2 and FATP1 deficient cells. Similarly, the impact of Metformin and TMZ on intracellular Mtb growth is well-reported. While that validates these observations in this study, it takes away any novelty from the study.

(5) Manuscript organisation: It will be very helpful to rearrange figures and supplementary figures.

Reviewer #2 (Public review):

Summary:

It is generally believed that higher-order areas in the prefrontal cortex guide selection during working memory and attention through signals that selectively recruit neuronal populations in sensory areas that encode the relevant feature. In this work, Parto-Dezfouli and colleagues tested how these prefrontal signals influence activity in visual area V4 using a spatial working memory task. They recorded neuronal activity from visual area V4 and found that information about visual features at the behaviorally relevant part of space during the memory period is carried in a spatially selective manner in the timing of spikes relative to a beta oscillation (phase coding) rather than in the average firing rate (rate code). The authors further tested whether there is a causal link between prefrontal input and the phase encoding of visual information during the memory period. They found that indeed inactivation of the frontal eye fields, a prefrontal area known to send spatial signals to V4, decreased beta oscillatory activity in V4 and information about the visual features. The authors went one step further to develop a neural model that replicated the experimental findings and suggested that changes in the average firing rate of individual neurons might be a result of small changes in the exact beta oscillation frequency within V4. These data provide important new insights into the possible mechanisms through which top-down signals can influence activity in hierarchically lower sensory areas and can therefore have a significant impact on the Systems, Cognitive, and Computational Neuroscience fields.

Strengths:

This is a well-written paper with a well-thought-out experimental design. The authors used a smart variation of the memory-guided saccade task to assess how information about the visual features of stimuli is encoded during the memory period. By using a grating of various contrasts and orientations as the background the authors ensured that bottom-up visual input would drive responses in visual area V4 in the delay period, something that is not commonly done in experimental settings in the same task. Moreover, one of the major strengths of the study is the use of different approaches including analysis of electrophysiological data using advanced computational methods of analysis, manipulation of activity through inactivation of the prefrontal cortex to establish causality of top-down signals on local activity signatures (beta oscillations, spike locking and information carried) as well as computational neuronal modeling. This has helped extend an observation into a possible mechanism well supported by the results.

Weaknesses:

Although the authors provide support for their conclusions from different approaches, I found that the selection of some of the analyses and statistical assessments made it harder for the reader to follow the comparison between a rate code and a phase code. Specifically, the authors wish to assess whether stimulus information is carried selectively for the relevant position through a firing rate or a phase code. Results for the rate code are shown in Figures 1B-G and for the phase code are shown in Figure 2. Whereas an F-statistic is shown over time in Figure 1F (and Figure S1) no such analysis is shown for LFP power. Similarly, following FEF inactivation there is no data on how that influences V4 firing rates and information carried by firing rates in the two conditions (for positions inside and outside the V4 RF). In the same vein, no data are shown on how the inactivation affects beta phase coding in the OUT condition.

Moreover, some of the statistical assessments could be carried out differently including all conditions to provide more insight into mechanisms. For example, a two-way ANOVA followed by post hoc tests could be employed to include comparisons across both spatial (IN, OUT) and visual feature conditions (see results in Figures 2D, S4, etc.). Figure 2D suggests that the absence of selectivity in the OUT condition (no significant difference between high and low contrast stimuli) is mainly due to an increase in slope in the OUT condition for the low contrast stimulus compared to that for the same stimulus in the IN condition. If this turns out to be true it would provide important information that the authors should address.

There are also a few conceptual gaps that leave the reader wondering whether the results and conclusion are general enough. Specifically,

(1) the authors used microstimulation in the FEF to determine RFs. It is thus possible that the FEF sites that were inactivated were largely more motor-related. Given that beta oscillations and motor preparatory activity have been found to be correlated and motor sites show increased beta oscillatory activity in the delay period, it is possible that the effect of FEF inactivation on V4 beta oscillations is due to inactivation of the main source of beta activity. Had the authors inactivated sites with a preponderance of visual neurons in the FEF would the results be different?

(2) Somewhat related to this point and given the prominence of low-frequency activity in deeper layers of the visual cortex according to some previous studies, it is not clear where the authors' V4 recordings were located. The authors report that they do have data from linear arrays, so it should be possible to address this.

(3) The authors suggest that a change in the exact frequency of oscillation underlies the increase in firing rate for different stimulus features. However, the shift in frequency is prominent for contrast but not for orientation, something that raises questions about the general applicability of this observation for different visual features.

(4) One of the major points of the study is the primacy of the phase code over the rate code during the delay period. Specifically, here it is shown that information about the visual features of a stimulus carried by the rate code is similar for relevant and irrelevant locations during the delay period. This contrasts with what several studies have shown for attention in which case information carried in firing rates about stimuli in the attended location is enhanced relative to that for stimuli in the unattended location. If we are to understand how top-down signals work in cognitive functions it is inevitable to compare working memory with attention. The possible source of this difference is not clear and is not discussed. The reader is left wondering whether perhaps a different measure or analysis (e.g. a percent explained variance analysis) might reveal differences during the delay period for different visual features across the two spatial conditions.

The use of the memory-guided saccade task has certain disadvantages in the context of this study. Although delay activity is interpreted as memory activity by the authors, it is in principle possible that it reflects preparation for the upcoming saccade, spatial attention (particularly since there is a stimulus in the RF), etc. This could potentially change the conclusion and perspective.

For the position outside the V4 RF, there is a decrease in both beta oscillations and the clustering of spikes at a specific phase. It is therefore possible that the decrease in information about the stimuli features is a byproduct of the decrease in beta power and phase locking. Decreased oscillatory activity and phase locking can result in less reliable estimates of phase, which could decrease the mutual information estimates.

The authors propose that coherent oscillations could be the mechanism through which the prefrontal cortex influences beta activity in V4. I assume they mean coherent oscillations between the prefrontal cortex and V4. Given that they do have simultaneous recordings from the two areas they could test this hypothesis on their own data, however, they do not provide any results on that.

The authors make a strong point about the relevance of changes in the oscillation frequency and how this may result in an increase in firing rate although it could also be the reverse - an increase in firing rate leading to an increase in the frequency peak. It is not clear at all how these changes in frequency could come about. A more nuanced discussion based on both experimental and modeling data is necessary to appreciate the source and role (if any) of this observation.

Reviewer #2 (Public review):

Summary:

Padder et al. demonstrates that ATG5 mediates lysosomal repair via the recruitment of the retromer components during LLOMe-induced lysosomal damage and that mAtg8-ylation contributes to retromer-dependent cargo sorting of GLUT1. Although previous studies have suggested that during glucose withdrawal, classical autophagy contributes to retromer-dependent GLUT1 surface trafficking via interactions between LC3A and TBC1D5, the experiments here demonstrate that during basal conditions or lysosomal damage, ATGs that are not involved in mATG8ylation, such as FIP200, are not functionally required for retromer-dependent sorting of GLUT1. Overall, these studies suggest a unique role for ATG5 in the control of retromer function, and that conjugation of ATG8 to single membranes (CASM) is a partial contributors to these phenotypes.

Strengths:

(1) Overall, these studies suggest a unique non-autophagic role for ATG5 in the control of retromer function. They also demonstrate that conjugation of ATG8 to single membranes (CASM) is a partial contributors to these phenotypes. Overall, these data point to a new role for ATG5 and CASM-dependent mATG8ylation in lysosomal membrane repair and trafficking.

(2) Although the studies are overall supportive of the proposed model that the retromer is controlled by CASM-dependent mATG8-ylaytion, it is noteworthy that previous studies of GLUT1 trafficking during glucose withdrawal (Roy et al. Mol Cell, PMID: 28602638) were predominantly conducted in cells lacking ATG5 or ATG7, which would not be able to discriminate between a CASM-dependent vs. canonical autophagy-dependent pathway in the control of GLUT1 sorting. Is the lack of GLUT1 mis-sorting to lysosomes observed in FIP200 and ATG13KO cells also observed during glucose withdrawal? Notably, deficiencies in glycolysis and glucose-dependent growth have been reported in FIP200 deficient fibroblasts (Wei et al. G&D, PMID: 21764854) so there may be difference in regulation dependent on the stress imposed on a cell.

Comments on revisions:

My previous comments have been addressed.

Reviewer #2 (Public review):

Summary:

The authors investigate the problem of olfactory search in turbulent environments using artificial agents trained using tabular Q-learning, a simple and interpretable reinforcement learning (RL) algorithm. The agents are trained solely on odor stimuli, without access to spatial information or prior knowledge about the odor plume's shape. This approach makes the emergent control strategy more biologically plausible for animals navigating exclusively using olfactory signals. The learned strategies show parallels to observed animal behaviors, such as upwind surging and crosswind casting. The approach generalizes well to different environments and effectively handles the intermittency of turbulent odors.

Strengths:

(1) The use of numerical simulations to generate realistic turbulent fluid dynamics sets this paper apart from studies that rely on idealized or static plumes.

(2) A key innovation is the introduction of a small set of interpretable olfactory states based on moving averages of odor intensity and sparsity, coupled with an adaptive temporal memory.

(3) The paper provides a thorough analysis of different recovery strategies when an agent loses the odor trail, offering insights into the trade-offs between various approaches.

(4) The authors provide a comprehensive performance analysis of their algorithm across a range of environments and recovery strategies, demonstrating the versatility of the approach.

(5) Finally, the authors list an interesting set of real-world experiments based on their findings, that might invite interest from experimentalists across multiple species.

Weaknesses:

(1) The inclusion of Brownian motion as a recovery strategy, seems odd since it doesn't closely match natural animal behavior, where circling (e.g. flies) or zigzagging (ants' "sector search") could have been more realistic.

(2) Using tabular Q-learning is both a strength and a limitation. It's simple and interpretable, making it easier to analyze the learned strategies, but the discrete action space seems somewhat unnatural. In real-world biological systems, actions (like movement) are continuous rather than discrete. Additionally, the ground-frame actions may not map naturally to how animals navigate odor plumes (e.g. insects often navigate based on their own egocentric frame).

(3) The lack of accompanying code is a major drawback since nowadays open access to data and code is becoming a standard in computational research. Given that the turbulent fluid simulation is a key element that differentiates this paper, the absence of simulation and analysis code limits the study's reproducibility.

Reviewer #2 (Public review):

The paper by Nelson KA, et al. explored the collective migration, coalescence and positioning of the posterior signaling center (PSC) cells in Drosophila embryo. With live imaging, the authors observed the dynamic progress of PSC migration. Throughout this process, visceral mesoderm (VM), alary muscles (Ams) and cardioblasts (CBs) are in proximity of PSC. Genetic ablation of these tissues reveals the requirement for VM and CBs, but not AMs in this process. Genetic manipulations further demonstrated that Slit-Robo signaling was critical during PSC migration and positioning. While the genetic mechanisms of positioning the PSC were explored in much detail, including using live imaging, the functional consequence of mispositioning or (partial) absence of PSC cells has not been addressed, but would much increase the relevance of their findings. A few additional issues need to be addressed as well in this otherwise well-done study.

Previous major points:

(1) The only readout in their experiments is the relative correctness of PSC positioning. Importantly, what is the functional consequence if PSC is not properly positioned? This would be particularly important with robo-sli manipulations, where the PSC is present but some cells are misplaced. What is the consequence? Are the LGs affected, like specification of their cell types, structure and function? To address this for at least the robo-slit requirement in the PSC, it may be important to manipulate them directly in the PSC with a split Gal4 system, using Antp and Odd promoters.

(2) The densely, parallel aligned fibers in the lower part of Figure 1J seemed to be visceral mesoderm, but further up (dorsally) that may be epidermis. It is possible that the PSC migrate together with the epidermis? This should be addressed.

(3) Although the authors described the standards of assessing PSC positioning as "normal" or "abnormal", it is rather subtle at times and variable in the mutant or KD/OE examples. The criteria should be more clearly delineated and analyzed double-blind, also since this is the only readout. Further examples of abnormal positioning in supplementary figures would also help.

(4) Discussion is very lengthy and should shortened.

Comments on revised version:

Although the authors have responded to my concerns as they deemed suitable, these concerns still stand for the revised version.

Reviewer #3 (Public review):

The author presents a novel theory and computational model suggesting that grid cells do not encode space, but rather encode non-spatial attributes. Place cells in turn encode memories of where those specific attributes occurred. The theory accounts for many experimental results and generates useful predictions for future studies. The model's simplicity and potential explanatory power will interest others in the field. There are, however, a few weaknesses outlined below which undermine the theory.

Main criticisms:

(1) A crucial assumption of the model is that grid cells express grid-like firing patterns if and only if the content of experience is constant in space. It is difficult to imagine a real world example that satisfies this assumption. Odors and sounds are used as examples. While they are often more spatially diffuse than an object on the ground, odors and sounds have sources that are readily detectable and thus are not constant in space. Animals can easily navigate to a food source or to a vocalizing conspecific. This assumption is especially problematic because it predicts that all grid cells should become silent when their preferred non-spatial attribute (e.g. a specific odor) is missing. I'm not aware of any experimental data showing that grid cells become silent. On the contrary, grid cells are known to remain active across all contexts that have been tested, including across sleep/wake states. Unlike place cells, grid cells have never been shown to turn off. Since grid cells are active in all contexts, their preferred attribute must also be present in all contexts, and therefore they would not convey any information about the specific content of an experience. The author lists many attributes that could in theory be constant in a laboratory setting, but there is no data I'm aware of that shows this is true in practice. As it stands, this crucial assumption of the model remains mere speculation.

(2) The proposed novelty of this theory is that other models all assume that grid cells encode space. This is not quite true of models based on continuous attractor networks, the discussion of which is essentially absent. More specifically, attractor models focus on the importance of intrinsic dynamics within entorhinal cortex in generating the grid pattern. While this firing pattern is aligned to space during navigation and therefore can be used a representation of that space, the neural dynamics are preserved even during sleep. Similarly, it is because the grid pattern does not strictly encode physical space that grid-like signals are also observed in relation to other two-dimensional continuous variables.

(3) The use of border cells or boundary vector cells as the main (or only) source of spatial information in the hippocampus is not well supported by experimental data. Border cells in entorhinal cortex are not active in the center of an environment. Boundary-vector cells can fire farther away from the walls, but are not found in entorhinal cortex. They are located in the subiculum, a major output of the hippocampus. While the entorhinal-hippocampal circuit is a loop, the route from boundary-vector cells to place cells is much less clear than from grid cells. Moreover, both border cells and boundary-vector cells (which are conflated in this paper) comprise a small population of neurons compared to grid cells.

Minor comments:

(1) There is substantial theoretical and experimental work supporting the idea that grid cell modules instantiate continuous attractor networks, yet this class of models is largely ignored:

p. 7 "In contrast, most grid cell models (Bellmund et al., 2016; Bush et al., 2015; Castro & Aguiar, 2014; Hasselmo, 2009; Mhatre et al., 2012; Solstad et al., 2006; Sorscher et al., 2023; Stepanyuk, 2015; Widloski & Fiete, 2014) are domain specific models of spatial navigation"

The following references should be added:

McNaughton, B. L., Battaglia, F. P., Jensen, O., Moser, E. I. & Moser, M.-B. Path integration and the neural basis of the 'cognitive map'. Nat. Rev. Neurosci. 7, 663-678 (2006).

Fuhs, M. C. & Touretzky, D. S. A spin glass model of path integration in rat medial entorhinal cortex. J. Neurosci. 26, 4266-4276 (2006).

Burak, Y. & Fiete, I. R. Accurate path integration in continuous attractor network models of grid cells. PLoS Comput. Biol. 5, e1000291 (2009).

Guanella, A., Kiper, D. & Verschure, P. A model of grid cells based on a twisted torus topology. Int. J. Neural Syst. 17, 231-240 (2007).

Couey, J. J. et al. Recurrent inhibitory circuitry as a mechanism for grid formation. Nat. Neurosci. 16, 318-324 (2013).

(Note: the Bellmund et al. (2016) citation is likely a mistake and was intended to be Bellmund et al. (2018).)

(2) The author claims in two places that this model is the first to explain that grid cell population activity lies on a torus. While it may be the first explicit computational account of why grid cell activity is mapped onto a torus, these claims should be moderated for clarity, for example by adding "but see McNaughton et al. (2006) and others".

Box 1. Results Uniquely Explained by this Memory Model - the population code of grid cells lies on a torus

p.11 "In addition, this simplifying assumption allows the model to capture the finding that the population of grid cells lies on a torus (Gardner et al., 2022), although I note that the model was developed before this result was known."

(3) Lateral entorhinal cortex is largely ignored in this memory model. It should be considered that the predominance of spatial representations reported in the literature is due to historical reasons. Namely, the discovery of hippocampal place cells spurred interest in looking upstream for the source of spatial information, which was later abundantly clear in medial entorhinal cortex. Lateral entorhinal cortex is relatively understudied, but is known to encode odors, objects, and time in a way that medial entorhinal cortex does not. It is therefore confusing to assume that these attributes are instead encoded by grid cells.

Reviewer #2 (Public review):

Building on their detailed dissection of the role of Hox-Gbx genes in endomesodermal segmentation in Nematostella, He and colleagues attempt to understand the evolutionary conservation of this process in anthozoans. In a move that should be congratulated, the authors perform this work in the coral M. capitata, a species that is not well established in the lab. The authors show convincing expression data using both RNAseq and in-situ hybridization and discover the conserved expression of Hox-Gbx genes preceding the segmentation of the enodmesoderm. The authors further attempt to understand whether BMP signalling is playing a role in this process and present data that certainly points to this being the case.

Strength:

The overall quality of the data is very high and the authors show very convincing expression data for the Hox-Gbx genes as well as putting forward a well-thought-out hypothesis for segment evolution.

Weakness:

There are a number of weaknesses in the paper which I believe can be easily addressed:

(1) The authors in many cases claim to have provided functional evidence for the role of Hox-Gbx genes in M. capitata. This is not, however, the case, and although the expression data along with their previous work in Nematostella make their claims very likely I still believe it is necessary to set a higher bar for claiming to understand function. In the abstract, for example, they claim: "These findings demonstrate the existence of a functionally conserved Hox-Gbx module....", something which is not substantiated by the data presented. At the end of the introduction, they say they "systematically interrogate the molecular functions of Hox-Gbx genes" (line 75) which again is not what is presented in the manuscript. Finally, on line 289-291 the authors state: "Taken together, our findings strongly suggest that the heterochronic deployment of a conserved Hox-Gbx module contributes to the divergent adult body plans observed between Edwardsiidae and other anthozoans." I would remove "Strongly" given the absence of functional data. There are also other examples where functional understanding is implied and I would suggest the authors tone this down throughout the manuscript.

(2) On Line 185, the authors state "To determine the function of the Hox-Gbx network in M.capitata segmentation..." when introducing their BMP experiments. I would reword this since they are looking at BMP signalling and do not look directly at Hox-Gbx function.

(3) Although the BMP inhibitor experiments are very interesting I think there is a lack of basic understanding of BMP signalling in this system. Where are the BMP components expressed and how would this match with the hypothesis derived from the data? The authors present some expression patterns in Figure S3 but do not discuss them. In addition, the authors do not show pSMAD staining etc, and do not validate that the inhibitors have an effect on this. I entirely understand the difficulties in doing such experiments in a system like this and would not suggest the authors should now do them but an acknowledgment of this in the discussion would be very welcome.

(4) In both lines 88 and 294 the authors talk about the mechanism of gastrulation. It is not clear to me how they infer this from the figure. If the authors could include some more high-resolution images that show this it would be very helpful and interesting.

(5) On line 169/170 the authors state that two Anthox6 paralogs, McAnthox6 and McAnthox6.1, were specifically expressed at the time of settlement. This is not what I see in the images. I see that McAnthox6 is expressed at 14 hpf more strongly than at the later time point. The authors should clarify this point.

(6) On lines 259-261 the authors state "How temporally and spatially coordinated gene expression can be achieved in this scenario remains an interesting and open question." This seems like a strange statement to include given that they have shown that there is no spatial and temporal collinearity in cnidarians. Surely it is not an open question to ask how it would work if there is none. I would simply remove this.

(7) The authors should cite the sources of information contained in Fig. S2 including how orthology was assigned.

Reviewer #2 (Public review):

Summary:

In this study, Ye et al. have developed a theoretical model of osmotic pressure adaptation by osmolyte production and wall synthesis.

Strengths:

They validate their model predictions of a rapid increase in growth rate on osmotic shock experimentally using fission yeast. The study has several interesting insights which are of interest to the wider community of cell size and mechanics.

Weaknesses:

Multiple aspects of this manuscript require addressing, in terms of clarity and consistency with previous literature. The specifics are listed as major and minor comments.

Major comments:

(1) The motivation for the work is weak and needs more clarity.

(2) The link between sections is very frequently missing. The authors directly address the problem that they are trying to solve without any motivation in the results section.

(3) The parameters used in the models (symbols) need to be explained better to make the paper more readable.

(4) Throughout the paper, the authors keep switching between organisms that they are modelling. There needs to be some consistency in this aspect where they mention what organism they are trying to model, since some assumptions that they make may not be valid for both yeast as well as bacteria.

(5) The extent of universality of osmoregulation i.e the limitations are not very well highlighted.

(6) Line 198-200: It is not clear in the text what organisms the authors are writing about here. "Experiments suggested that the turgor pressure induce cell-wall synthesis, e.g., through mechanosensors on cell membrane [45, 46], by increasing the pore size of the peptidoglycan network [5], and by accelerating the moving velocity of the cell-wall synthesis machinery [31]". This however is untrue for bacteria as shown by the study (reference 22 is this paper:  E. Rojas, J. A. Theriot, and K. C. Huang, Response of escherichia coli growth rate to osmotic shock, Proceedings of the National Academy of Sciences 111, 7807 (2014).

(7) The time scale of reactions to hyperosmotic shocks does not agree with previous literature (reference 22). Therefore defining which organism you are looking at is important. Hence the statement " Because the timescale of the osmoresponse process, which is around hours (Figure 3B), is much longer than the timescale of the supergrowth phase, which is about 20 minutes, the turgor pressure at the growth rate peak can be well approximated by its immediate value after the shock." from line 447 does not seem to make sense. The authors need to address this.

Reviewer #2 (Public review):

Summary:

This manuscript investigates how olfactory representations are transformed along the cortico-hippocampal pathway in mice during a non-associative learning paradigm involving novel and familiar odors. By recording single-unit activity in several key brain regions (AON, aPCx, LEC, CA1, and SUB), the authors aim to elucidate how stimulus identity and experience are encoded and how these representations change across the pathway.

The study addresses an important question in sensory neuroscience regarding the interplay between sensory processing and signaling novelty/familiarity. It provides insights into how the brain processes and retains sensory experiences, suggesting that the earlier stations in the olfactory pathway, the AON aPCx, play a central role in detecting novelty and encoding odor, while areas deeper into the pathway (LEC, CA1 & Sub) are more sparse and encodes odor identity but not novelty/familiarity. However, there are several concerns related to methodology, data interpretation, and the strength of the conclusions drawn.

Strengths:

The authors combine the use of modern tools to obtain high-density recordings from large populations of neurons at different stages of the olfactory system (although mostly one region at a time) with elegant data analyses to study an important and interesting question.

Weaknesses:

(1) The first and biggest problem I have with this paper is that it is very confusing, and the results seem to be all over the place. In some parts, it seems like the AON and aPCx are more sensitive to novelty; in others, it seems the other way around. I find their metrics confusing and unconvincing. For example, the example cells in Figure 1C show an AON neuron with a very low spontaneous firing rate and a CA1 with a much higher firing rate, but the opposite is true in Figure 2A. So, what are we to make of Figure 2C that shows the difference in firing rates between novel vs. familiar odors measured as a difference in spikes/sec. This seems nearly meaningless. The authors could have used a difference in Z-scored responses to normalize different baseline activity levels. (This is just one example of a problem with the methodology.)

(2) There are a lot of high-level data analyses (e.g., decoding, analyzing decoding errors, calculating mutual information, calculating distances in state space, etc.) but very little neural data (except for Figure 2C, and see my comment above about how this is flawed). So, if responses to novel vs. familiar odors are different in the AON and aPCx, how are they different? Why is decoding accuracy better for novel odors in CA1 but better for familiar odors in SUB (Figure 3A)? The authors identify a small subset of neurons that have unusually high weights in the SVM analyses that contribute to decoding novelty, but they don't tell us which neurons these are and how they are responding differently to novel vs. familiar odors.

(3) The authors call AON and aPCx "primary sensory cortices" and LEC, CA1, and Sub "multisensory areas". This is a straw man argument. For example, we now know that PCx encodes multimodal signals (Poo et al. 2021, Federman et al., 2024; Kehl et al., 2024), and LEC receives direct OB inputs, which has traditionally been the criterion for being considered a "primary olfactory cortical area". So, this terminology is outdated and wrong, and although it suits the authors' needs here in drawing distinctions, it is simplistic and not helpful moving forward.

(4) Why not simply report z-scored firing rates for all neurons as a function of trial number? (e.g., Jacobson & Friedrich, 2018). Figure 2C is not sufficient. For example, in the Discussion, they say, "novel stimuli caused larger increases in firing rates than familiar stimuli" (L. 270), but what does this mean? Odors typically increase the firing in some neurons and suppress firing in others. Where does the delta come from? Is this because novel odors more strongly activate neurons that increase their firing or because familiar odors more strongly suppress neurons?

(5) Lines 122-124 - If cells in AON and aPCx responded the same way to novel and familiar odors, then we would say that they only encode for odor and not at all for experience. So, I don't understand why the authors say these areas code for a "mixed representation of chemical identity and experience." "On the other hand," if LEC, CA1, and SUB are odor selective and only encode novel odors, then these areas, not AON and aPCx, are the jointly encoding chemical identity and experience. Also, I do not understand why, here, they say that AON and PCx respond to both while LEC, CA1, and SUB were selective for novel stimuli, but the authors then go on to argue that novelty is encoded in the AON and PCx, but not in the LEC, CA1, and SUB.

(6) Lines 132-140 - As presented in the text and the figure, this section is poorly written and confusing. Their use of the word "shuffled" is a major source of this confusion, because this typically is the control that produces outcomes at the chance level. More importantly, they did the wrong analysis here. The better and, I think, the only way to do this analysis correctly is to train on some of the odors and test on an untrained odor (i.e., what Bernardi et al., 2021 called "cross-condition generalization performance"; CCGP).

Reviewer #2 (Public review):

Summary:

The submitted manuscript aims to characterize the role of mast cells in TB granuloma. The manuscript reports heterogeneity in mast cell populations present within the granulomas of tuberculosis patients. With the help of previously published scRNAseq data, the authors identify transcriptional signatures associated with distinct subpopulations.

Strengths:

(1) The authors have carried out a sufficient literature review to establish the background and significance of their study.

(2) The manuscript utilizes a mast cell-deficient mouse model, which demonstrates improved lung pathology during Mtb infection, suggesting mast cells as a potential novel target for developing host-directed therapies (HDT) against tuberculosis.

Weaknesses:

(1) The manuscript requires significant improvement, particularly in the clarity of the experimental design, as well as in the interpretation and discussion of the results. Enhanced focus on these areas will provide better coherence and understanding for the readers.

(2) Throughout the manuscript, the authors have mislabelled the legends for WT B6 mice and mast cell-deficient mice. As a result, the discussion and claims made in relation to the data do not align with the corresponding graphs (Figure 1B, 3, 4, and S2). This discrepancy undermines the accuracy of the conclusions drawn from the results.

(3) The results discussed in the paper do not add a significant novel aspect to the field of tuberculosis, as the majority of the results discussed in Figure 1-2 are already known and are a re-validation of previous literature.

(4) The claims made in the manuscript are only partially supported by the presented data. Additional extensive experiments are necessary to strengthen the findings and enhance the overall scientific contribution of the work.

Reviewer #2 (Public review):

Background and Summary: 

This study addresses the intriguing question of whether and how tumours can develop in the freshwater polyp hydra and how they influence the fitness of the animals. Hydra is notable for its significant morphogenetic plasticity and nearly unlimited capacity for regeneration. While its growth through asexual reproduction (budding) and the associated processes of pattern formation have been extensively studied at the cellular level, the occurrence of tumours was only recently described in two strains of Hydra oligactis (Domazet-Lošo et al, 2014). Here, tumour-like tissue bulges formed within the ectodermal epithelial layer and contained increased numbers of interstitial cell-like cells which exhibited female germline markers, but none specific for somatic derivatives of interstitial stem cells (e.g., nematocytes, neurons or glandular cells). It seems likely that the cellular basis of these malformations is a misregulation of oogenesis. In wild-type polyps, interstitial-cell-related germline precursors give rise to oocytes and nurse cells, which are subsequently phagocytosed by the growing egg cell. By comparison, in the mutant strains, this uptake is disturbed, but the homeostasis between germline cells and epithelial cells must remain functional enabling further growth pattern formation in hydra. Determining whether this differentiation arrest constitutes a neoplasm also remains a challenge. 

Clonal lines of both strains have been maintained in the laboratory for years and have also been used by Boutry and colleagues. They published two further papers on the ecological and evolutionary aspects of hydra tumour formation (Boutry et al 2022, 2023), which is also the focus of this manuscript. In their paper, the authors demonstrate an increase in the number of tentacles when "tumour tissue" was transplanted to intact gastric tissue of wildtype and mutant strains. While the impact on tentacle formation is relatively modest, small, it indicates a potential influence on the cross-talk between epithelial and interstitial cells in growth control (proportion regulation). The presented data are of interest, although the underlying molecular processes remain to be demonstrated. The authors offer a different interpretation. They conclude that this growth pattern (increased number of tentacles) is correlated with "reducing the burden on the host by (over-) compensating for the reproductive costs of tumours" and claim that "transmissible tumours in hydra have evolved strategies to manipulate the phenotype of their host". 

Strength <br /> The question of whether and how tumours can develop in simple systems, here the freshwater polyp hydra, is of general interest. The authors describe transplantation experiments by using mutant strains that indicate an influence of tumour-like malformation on pattern formation. The experiments also suggest an interaction between epithelial cells and germline cells during oogenesis, interfering with the homeostatic growth control between the cell lineages. 

Weaknesses <br /> Although it is stimulating to consider a fresh perspective from other disciplines (here, ecological and evolutionary aspects), it appears that this interpretation of the data (reducing the burden on the host by (over-) compensating for the reproductive costs of tumours) is somewhat beyond what can be reasonably inferred from the evidence presented. It is essential, particularly in the context of evolutionary biology, to conduct further analysis of the underlying cell biology of these intriguing mutant hydra strains. Such cellular analysis is a relatively straightforward approach that could provide a mechanistic understanding of the phenomenon described by the authors.

Reviewer #2 (Public review):

Summary:

Saijilafu et al. demonstrate that MLCK/MLCP proteins promote axonal regeneration in both the central nervous system (CNS) and peripheral nervous system (PNS) using primary cultures of adult DRG neurons, hippocampal and cortical neurons, as well as in vivo experiments involving sciatic nerve injury, spinal cord injury, and optic nerve crush. The authors show that axon regrowth is possible across different contexts through genetic and pharmacological manipulation of these proteins. Additionally, they propose that MLCK/MLCP may regulate F-actin reorganization in the growth cone, which is significant as it suggests a novel strategy for promoting axonal regeneration.

Strengths:

This manuscript presents a wide range of experimental models to address its hypothesis and biological question. Notably, the use of multiple in vivo models significantly enhances the overall validity of the study.

Weaknesses:

-The authors previously published that blocking myosin II activity stimulates axonal growth and that MLCK activates myosin II. The present work shows that inhibiting MLCK blocks axonal regeneration while blocking MLCP (the protein that dephosphorylates myosin II) produces the opposite effect. Although this contradiction is discussed, no new evidence has been added to the manuscript to clarify this mechanism or address the remaining questions. Critical unresolved questions include: what happens to myosin II expression when both MLCK and MLCP are inhibited? If MLCK/MLCP are acting through an independent mechanism, what would that mechanism be?<br /> -In the discussion, the authors mention the existence of two myosin II isoforms with opposing effects on axonal growth. Still, there is no evidence in the manuscript to support this point.<br /> -It is also unclear how MLCK/MLCP acts on the actin cytoskeleton. The authors suggest that proteins such as ADF/cofilin, Arp 2/3, Eps8, Profilin, Myosin II, and Myosin V could regulate changes in F-actin dynamics. However, this study provides no experimental evidence to determine which proteins may be involved in the mechanism.

Reviewer #2 (Public review):

Summary:

This study examines how local DNA features around the amino acid permease gene GAP1 influence adaptation to glutamine limited conditions through changes in GAP1 Copy Number Variation (CNV). The study is well motivated by the observation of numerous CNVs documented in many organisms, but difficulty in distinguishing the mechanisms by which they are formed, and whether or how local genomic elements influence their formation. The main finding is convincing and is that a nearby Autonomous Replicating Sequence (ARS) influences the formation of GAP1 CNVs and this is consistent with a predominate mechanism of Origin Dependent Inverted Repeat Amplification (ODIRA). These results along with finding and characterizing other mechanisms of GAP1 CNV formation will be of general interest to those studying CNVs in natural systems, experimental evolution and in tumor evolution. While the results are limited to a single CNV of interest (GAP1), the carefully controlled experimental design and quantification of CNV formation will provide a useful guide to studying other CNVs and CNVs in other organisms.

Strengths:

The study was designed to examine the effects of two flanking genomic features next to GAP1 on CNV formation and adaptation during experimental evolution. This was accomplished by removing two Long Terminal Repeats (LTRs), removing a downstream ARS, and removing both LTRs and the ARS. Although there was some heterogeneity among replicates, later shown to include the size and breakpoints of the CNV and the presence of an unmarked CNV, both marker assisted tracking of CNV formation and modeling of CNV rate and fitness effects showed that deletion of the ARS caused a clear difference compared to the control and the LTR deletion.

The consequence of deletion of local features (LTR and ARS) was quantified by genome sequencing of adaptive clones to identify the CNV size, copy number and infer the mechanism of CNV formation. This greatly added value to the study as it showed that i) ODIRA was the most common mechanism but ODIRA is enhanced by a local ARS, ii) non-allelic homologous recombination (NAHR) is also used but depends on LTRs, and iii) de novo insertion of transposable elements mediate NAHR in strains with both ARS and LTR deletions. Together, these results show how local features influence the mechanism of CNV formation, but also how alternative mechanism can substitute when primary ones are unavailable.

Weaknesses:

The CNV mutation rate and effect on fitness are hard to disentangle. The frequency of the amplified GFP provides information about mutation rate differences as well as fitness differences. The data and analysis show that each evolved population has multiple GAP1 CNV lineages within it, with some being unmarked by GFP. Thus, estimates of CNV fitness are more of a composite view of all CNV amplifications increasing in frequency during adaptation. Another unknown but potential complication is whether the local (ARS, LTR) deletions influence GAP1 expression and thus the fitness gain of GAP1 CNVs. The neural network simulation based inference does a good job at estimating both mutation rates and fitness effects, while also accounting for unmarked CNVs. However, the model does not account for population heterogeneity of CNVs and their fitness effects. Despite these limitations of distinguishing mutation rate and fitness differences, the authors' conclusions are well supported in that the LTR and ARS deletions have a clear impact on the CNV mediated evolutionary outcome and the mechanism of CNV formation.

Reviewer #2 (Public review):

Summary:

This is an interesting and well-performed study that develops a new modeling approach (MoA-HMM) to simultaneously characterize reinforcement learning parameters of different RL agents, as well as latent behavioral states that differ in the relative contributions of those agents to the animal's choices. They performed this study in rats trained to perform the two-step task. While the major advance of the paper is developing and rigorously validating this novel technical approach, there are also a number of interesting conceptual advances. For instance, humans performing the two-step task are thought to exhibit a trade-off between model-free and model-based strategies. However, the MoA-HMM did not reveal such a trade-off in the rats, but instead suggested a trade-off between model-based exploratory vs. exploitative strategies. Additionally, the firing rates of neurons in the orbitofrontal cortex (OFC) reflected latent behavioral states estimated from the HMM, suggesting that (1) characterizing dynamic behavioral strategies might help elucidate neural dynamics supporting behavior, and (2) OFC might reflect the contributions of one or a subset of RL agents that are preferentially active or engaged in particular states identified by the HMM.

Strengths:

The claims were generally well-supported by the data. The model was validated rigorously, and was used to generate and test novel predictions about behavior and neural activity in OFC. The approach is likely to be generally useful for characterizing dynamic behavioral strategies.

Reviewer #2 (Public review):

Strengths:

Wang and colleagues successfully uncovered an important function of the Drosophila PRDM16/PRDM3 homolog Hamlet (Ham) - a PR domain-containing transcription factor with known roles in the nervous system in Drosophila. To do so, they generated and analyzed new mutants lacking the PR domain, and also employed diverse preexisting tools. In doing so, they made a fascinating discovery: They found that PR-domain containing isoforms of ham are crucial in the intriguing development of the fly genital tract. Wang and colleagues found three distinct roles of Ham: (1) specifying the position of the testis terminal epithelium within the testis, (2) allowing normal shaping and growth of the anlagen of the seminal vesicles and paragonia and (3) enabling the crucial epithelial fusion between the seminal vesicle and the testis terminal epithelium. The mutant blocks fusion even if the parts are positioned correctly. The last finding is especially important, as there are few models allowing one to dissect the molecular underpinnings of heterotypic epithelial fusion in development. Their data suggest that they found a master regulator of this collective cell behavior. Further, they identified some of the cell biological players downstream of Ham, like for example E-Cadherin and Crumbs. In a holistic approach, they performed RNAseq and intersected them with the CUT&TAG-method, to find a comprehensive list of downstream factors directly regulated by Ham. Their function in the fusion process was validated by a tissue-specific RNAi screen. Meticulously, Wang and colleagues performed multiplexed in situ hybridization and analyzed different mutants, to gain a first understanding of the most important downstream pathways they characterized, which are Wnt2 and Toll.

This study pioneers a completely new system. It is a model for exploring a process crucial in morphogenesis across animal species, yet not well understood. Wang and colleagues not only identified a crucial regulator of heterotypic epithelial fusion but took on the considerable effort of meticulously pinning down functionally important downstream effectors by using many state-of-the-art methods. This is especially impressive, as the dissection of pupal genital discs before epithelial fusion is a time-consuming and difficult task. This promising work will be the foundation future studies build on, to further elucidate how this epithelial fusion works, for example on a cell biological and biomechanical level.

Weaknesses:

The developing testis-genital disc system has many moving parts. Myotube migration was previously shown to be crucial for testis shape. This means, that there is the potential of non-tissue autonomous defects upon knockdown of genes in the genital disc or the terminal epithelium, affecting myotube behavior which in turn affects fusion, as myotubes might create the first "bridge" bringing the epithelia together. The authors clearly showed that their driver tools do not cause expression in myoblasts/myotubes, but this does not exclude non-tissue autonomous defects in their RNAi screen. Nevertheless, this is outside the scope of this work.

However, one point that could be addressed in this study: the RNAseq and CUT&TAG experiments would profit from adding principal component analyses, elucidating similarities and differences of the diverse biological and technical replicates.

Reviewer #2 (Public review):

Summary:

The study is an innovative and fundamental study that clarified important aspects of brain processes for integration of information from speech and iconic gesture (i.e., gesture that depicts action, movement, and shape), based on tDCS, TMS, and EEG experiments. They evaluated their speech and gesture stimuli in information-theoretic ways and calculated how informative speech is (i.e., entropy), how informative gesture is, and how much shared information speech and gesture encode. The tDCS and TMS studies found that the left IFG and pMTG, the two areas that were activated in fMRI studies on speech-gesture integration in the previous literature, are causally implicated in speech-gesture integration. The size of tDC and TMS effects are correlated with the entropy of the stimuli or mutual information, which indicates that the effects stem from the modulation of information decoding/integration processes. The EEG study showed that various ERP (event-related potential, e.g., N1-P2, N400, LPC) effects that have been observed in speech-gesture integration experiments in the previous literature, are modulated by the entropy of speech/gesture and mutual information. This makes it clear that these effects are related to information decoding processes. The authors propose a model of how the speech-gesture integration process unfolds in time, and how IFG and pMTG interact with each other in that process.

Strengths:

The key strength of this study is that the authors used information theoretic measures of their stimuli (i.e., entropy and mutual information between speech and gesture) in all of their analyses. This made it clear that the neuro-modulation (tDCS, TMS) affected information decoding/integration and ERP effects reflect information decoding/integration. This study used tDCS and TMS methods to demonstrate that left IFG and pMTG are causally involved in speech-gesture integration. The size of tDCS and TMS effects are correlated with information-theoretic measures of the stimuli, which indicate that the effects indeed stem from disruption/facilitation of the information decoding/integration process (rather than generic excitation/inhibition). The authors' results also showed a correlation between information-theoretic measures of stimuli with various ERP effects. This indicates that these ERP effects reflect the information decoding/integration process.

Weaknesses:

The "mutual information" cannot fully capture the interplay of the meaning of speech and gesture. The mutual information is calculated based on what information can be decoded from speech alone and what information can be decoded from gesture alone. However, when speech and gesture are combined, a novel meaning can emerge, which cannot be decoded from a single modality alone. When example, a person produces a gesture of writing something with a pen, while saying "He paid". The speech-gesture combination can be interpreted as "paying by signing a cheque". It is highly unlikely that this meaning is decoded when people hear speech only or see gestures only. The current study cannot address how such speech-gesture integration occurs in the brain, and what ERP effects may reflect such a process. Future studies can classify different types of speech-gesture integration and investigate neural processes that underlie each type. Another important topic for future studies is to investigate how the neural processes of speech-gesture integration change when the relative timing between the speech stimulus and the gesture stimulus changes.

Reviewer #2 (Public review):

Summary:

The authors provide a very thorough investigation of the role of UBR-1 in anthelmintic resistance using the non-parasitic nematode, C. elegans. Anthelmintic resistance to macrocyclic lactones is a major problem in veterinary medicine and likely just a matter of time until resistance emerges in human parasites too. Therefore, this study providing novel insight into the mechanisms of ivermectin resistance is particularly important and significant.

Strengths:

The authors use very diverse technologies (behavior, genetics, pharmacology, genetically encoded reporters) to dissect the role of UBR-1 in ivermectin resistance. Deploying such a comprehensive suite of tools and approaches provides exceptional insight into the mechanism of how UBR-1 functions in terms of ivermectin resistance.

Weaknesses:

I do not see any major weaknesses in this study. My only concern is whether the observations made by the authors would translate to any of the important parasitic helminths in which resistance has naturally emerged in the field. This is always a concern when leveraging a non-parasitic nematode to shed light on a potential mechanism of resistance of parasitic nematodes, and I understand that it is likely beyond the scope of this paper to test some of their results in parasitic nematodes.

Reviewer #2 (Public review):

Summary:

This manuscript describes a first-in-human clinical trial of autologous stem cells to address IPF. The significance of this study is underscored by the limited efficacy of standard-of-care anti-fibrotic therapies and increasing knowledge of the role p63+ stem cells in lung regeneration in ARDS. While models of acute lung injury and p63+ stem cells have benefited from widespread and dynamic DAD and immune cell remodeling of damaged tissue, a key question in chronic lung disease is whether such cells could contribute to the remodeling of lung tissue that may be devoid of acute and dynamic injury. A second question is whether normal regions of the lung in an otherwise diseased organ can be identified as a source of "normal" p63+ stem cells, and how to assess these stem cells given recently identified p63+ stem cell variants emerging in chronic lung diseases including IPF. Lastly, questions of feasibility, safety, and efficacy need to be explored to set the foundation for autologous transplants to meet the huge need in chronic lung disease. The authors have addressed each of these questions to different extents in this initial study, which has yielded important if incomplete information for many of them.

Strengths:

As with a previous study from this group regarding autologous stem cell transplants for COPD (Ref. 24), they have shown that the stem cells they propagate do not form colonies in soft agar or cancers in these patients. While a full assessment of adverse events was confounded by a wave of Covid19 infections in the study participants, aside from brief fevers it appears these transplants are tolerated by these patients.

Weaknesses:

The source of stem cells for these autologous transplants is generally bronchoscopic biopsies/brushings from 5th-generation bronchi. Although stem cells have been cloned and characterized from nasal, tracheal, and distal airway biopsies, the systematic cloning and analysis of p63+ stem cells across the bronchial generations is less clear. For instance, p63+ stem cells from the nasal and tracheal mucosa appear committed to upper airway epithelia marked by 90% ciliated cells and 10% goblet cells (Kumar et al., 2011. Ref. 14). In contrast, p63+ stem cells from distal lung differentiate to epithelia replete with Club, AT2, and AT1 markers. The spectrum of p63+ stem cells in the normal bronchi of any generation is less studied. In the present study, cells are obtained by bronchoscopy from 3-5 generation bronchi and expanded by in vitro propagation. Single-cell RNAseq identifies three clusters they refer to as C1, C2, and C3, with the major C1 cluster said to have characteristics of airway basal cells and C2 possibly the same cells in states of proliferation. Perhaps the most immediate question raised by these data is the nature of the C1/C2 cells. Whereas they are clearly p63/Krt5+ cells as are other stem cells of the airways, do they display differentiation character of "upper airway" marked by ciliated/goblet cell differentiation or those of the lung marked by AT2 and AT1 fates? This could be readily determined by 3-D differentiation in so-called air-liquid interface cultures pioneered by cystic fibrosis investigators and should be done as it would directly address the validity of the sourcing protocol for autologous cells for these transplants. This would more clearly link the present study with a previous study from the same investigators (Shi et al., 2019, Ref. 9) whereby distal airway stem cells mitigated fibrosis in the murine bleomycin model. The authors should also provide methods by which the autologous cells are propagated in vitro as these could impact the quality and fate of the progenitor cells prior to transplantation.

The authors should also make a more concerted effort to compare Clusters 1, 2, and 3 with the variant stem cell identified in IPF (Wang et al., 2023, Ref. 27). While some of the markers are consistent with this variant stem cell population, others are not. A more detailed informatics analysis of normal stem cells of the airways and any variants reported could clarify whether the bronchial source of autologous stem cells is the best route to these transplants.

Other than these issues the authors should be commended for these first-in-human trials for this important condition.

Reviewer #2 (Public review):

This manuscript investigates the genetic basis of otitis media with effusion (OME) in children with Down syndrome (DS). Utilizing an impressive number of mouse models, the study identifies a significant locus on mouse chromosome 16 that contributes to the development of OME. Notably, the gene Dyrk1a is identified as a critical factor for OME in DS; Normalizing Dyrk1a dosage in Dp3Tyb mice restores the wild-type phenotype, highlighting its major contribution to OME in DS. The research also explores the downstream pathways affected by DYRK1A, revealing interactions with TGFβ signaling and the modulation of pro-inflammatory cytokines like IL-6 and IL-17, as well as increased VEGF levels linked to middle ear inflammation.

This work is novel in its comprehensive approach to linking specific genetic loci and genes to the development of OME in DS, and offers a refined genetic analysis, pinpointing Dyrk1a as a key gene. Additionally, the identification of some of the signaling pathways involved provides new insights into the pathophysiology of OME in DS. The findings have significant clinical implications, as they suggest that targeting Dyrk1a could be a potential therapeutic strategy for managing OME in children with DS. This could lead to improved treatment options that go beyond current surgical interventions, reducing the need for repeated tympanostomy tube placements and potentially mitigating the associated risks. Overall, this research enhances our understanding of the genetic factors underlying OME in DS, motivates future studies on the newly identified genetic loci, and opens avenues for future therapeutic developments.

Strengths:

(1) Robust methodology: The use of a comprehensive set of mouse models allows for precise localization of genetic loci associated with OME, an advancement over previous studies.

(2) Identification of Key Genes: The clear demonstration of Dyrk1a's role in OME provides a strong basis for further exploration of targeted therapies.

(3) Pathway Insights: The exploration of signaling pathways, including TGFβ and IL-6 interactions, enriches the discussion around the inflammatory mechanisms that contribute to OME in DS.

Weaknesses:

(1) Limited Human Data: While the mouse models are robust, the translation of findings to human populations could be further strengthened with comparative studies.

(2) Pathway Complexity: The study primarily focuses on Dyrk1a and its immediate inflammatory pathways, which may oversimplify the multifactorial nature of OME in DS; exploring additional genetic interactions, and further exploring the implications of the potential ciliogenesis role of DYRK1A in OME could provide a more complete view.

This study is a valuable contribution to the field of genetic research in Down syndrome, providing critical insights that could inform future therapeutic strategies for managing OME. The implications for treatment and understanding of DS phenotypes in mouse models are particularly noteworthy. The findings are well-supported and present clear avenues for further research.

Reviewer #2 (Public review):

Summary:

Mehta et al., in constructing E. coli strains unable to synthesize polyamines, noted that strains deficient in putrescine synthesis showed decreased movement on semisolid agar. They show that strains incapable of synthesizing putrescine have decreased expression of Type I pilin and, hence, decreased ability to perform pilin-dependent surface motility.

Strengths:

The authors characterize the specific polyamine pathways that are important for this phenomenon. RNAseq provides a detailed overview of gene expression in the strain lacking putrescine. The data suggest homeostatic control of polyamine synthesis and metabolic changes in response to putrescine.

Weaknesses:

In this version, the authors ignore phase variation of the pil operon promoter, which can be monitored via PCR. The gene expression data suggest that shifting to the pilin "off" state could help explain the phenotype.

Reviewer #2 (Public review):

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

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

The model and its successive implantation steps are well presented along a clear thread. However, the manuscript would benefit from clarifications at several key points (Hebbian vs homeostatic timeline).

First of all, it would have benefited from having an actual timeline of structural changes throughout the three days of AMPAR inhibition, especially as their experimental model allows it. This would have provided much-needed and otherwise entirely lacking information on spine dynamics (especially on transient spines) and on the respective timescale of the structural and functional changes, instead of modelling an entire timeline based solely on an experimental endpoint.

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

Finally, the difference between weak and complete inhibition could have been more extensively characterized. The authors focus indeed on the effects of either condition on spine number, but only integrate synaptic weights following complete inhibition. This is a pity, as they show some intriguing data suggesting a differential effect on spine size by partial or complete AMPAR inhibition (although further work is required to support some of their interpretations). Since the model aims at correlating structural and functional homeostatic plasticity, the fact that it is only demonstrated for one of the two conditions tested severely undermines the claims of the authors in the discussion that the model tackles that question.

Reviewer #2 (Public review):

Reeves et al explore a model of bone healing in the context of aging. They show that intermittent fasting can improve bone healing, even in aged animals. Their study combines a 'bone bandage' which delivers a canonical Wnt signal with intermittent fasting and shows impacts on the CD90 progenitor cell population and the healing of a critical-sized defect in the calvarium. They also explore potential regulators of this process and identify mitochondrial dysfunction in the age-related decline of stem cells. In this context, by modulating NAD+ pathways or the gut microbiota, they can also enhance healing, hinting at an effect mediated by complex impacts on multiple pathways associated with cellular metabolism.

The study shows a remarkable finding: that age-related decreases in bone healing can be restored by intermittent fasting. There is ample evidence that intermittent fasting can delay aging, but here the authors provide evidence that in an already-aged animal, intermittent fasting can restore healing to levels seen in younger animals. This is an important finding as it may hint at the potential benefits of intermittent fasting in tissue repair.

Reviewer #2 (Public review):

Neuromodulators are important for circuit function, but their roles in the retinal circuitry are poorly understood. This study by Gonschorek and colleagues aims to determine the modulatory effect of nitric oxide on the response properties of retinal ganglion cells. The authors used two photon calcium imaging and multi-electrode arrays to classify and compare cell responses before and after applying a NO donor DETA-NO. The authors found that DETA-NO selectively increases activity in a subset of contrast-suppressed RGC types. In addition, the authors found cell-type specific changes in light response in the absence of pharmacological manipulation in their calcium imaging paradigm. This study focuses on an important question and the results are interesting. The limitations of the method and data interpretation are adequately discussed in the revised manuscript.

The authors have addressed my previous comments, included additional discussions on the limitations of the method, and provided a more careful interpretation of their data.

Reviewer #2 (Public review):

In this work, Chang-Gonzalez and coworkers follow up on an earlier study on the force-dependence of peptide recognition by a T-cell receptor using all-atom molecular dynamics simulations. In this study, they compare the results of pulling on a TCR-pMHC complex between two different TCRs with the same peptide. A goal of the paper is to determine whether the newly studied B7 TCR has the same load-dependent behavior mechanism shown in the earlier study for A6 TCR. The primary result is that while the unloaded interaction strength is similar, A6 exhibits more force stabilization.

This is a detailed study, and establishing the difference between these two systems with and without applied force may establish them as a good reference setup for others who want to study mechanobiological processes if the data were made available, and could give additional molecular details for T-Cell-specialists. As written, the paper contains an overwhelming amount of details and it is difficult (for me) to ascertain which parts to focus on and which results point to the overall take-away messages they wish to convey.

Detailed comments:

(1) In Table 1 - are the values of the extension column the deviation from the average length at zero force (that is what I would term extension) or is it the distance between anchor points (which is what I would assume based on the large values. If the latter, I suggest changing the heading, and then also reporting the average extension with an asterisk indicating no extensional restraints were applied for B7-0, or just listing 0 load in the load column. Standard deviation in this value can also be reported. If it is an extension as I would define it, then I think B7-0 should indicate extension = 0+/- something. The distance between anchor points could also be labeled in Figure 1A.

(2) As in the previous paper, the authors apply "constant force" by scanning to find a particular bond distance at which a desired force is selected, rather than simply applying a constant force. I find this approach less desirable unless there is experimental evidence suggesting the pMHC and TCR were forced to be a particular distance apart when forces are applied. It is relatively trivial to apply constant forces, so in general, I would suggest this would have been a reasonable comparison. Line 243-245 speculates that there is a difference in catch bonding behavior that could be inferred because lower force occurs at larger extensions, but I do not believe this hypothesis can be fully justified and could be due to other differences in the complex.

(3) On a related note, the authors do not refer to or consider other works using MD to study force-stabilized interactions (e.g. for catch bonding systems), e.g. these cases where constant force is applied and enhanced sampling techniques are used to assess the impact of that applied force: https://www.cell.com/biophysj/fulltext/S0006-3495(23)00341-7, https://www.biorxiv.org/content/10.1101/2024.10.10.617580v1. I was also surprised not to see this paper on catch bonding in pMHC-TCR referred to, which also includes some MD simulations: https://www.nature.com/articles/s41467-023-38267-1

(4) The authors should make at least the input files for their system available in a public place (github, zenodo) so that the systems are a more useful reference system as mentioned above. The authors do not have a data availability statement, which I believe is required.

Reviewer #2 (Public review):

Summary:

The mechanism(s) by which the therapeutic drug metformin lowers blood glucose in type 2 diabetes and inhibits cell proliferation at higher concentrations remain contentious. Inhibition of complex 1 of the mitochondrial respiratory chain with consequent changes in cellular metabolites which favour allosteric activation of phosphofructokinase-1, allosteric inhibition of fructose bisphosphatase-1 and cAMP signalling and activation of AMPK which phosphorylates transcription factors are candidate mechanisms. The current manuscript proposes the e-subunit of ATP-synthase as a putative binding protein of biguanides and demonstrates that it regulates the expressivity of the Complex 1 protein NDUFB8.

Strengths:

(1) The metformin conjugate and metformin show comparable efficacy on inhibition of cell proliferation in the millimolar range.

(2) Demonstration of compromised expression of the Complex I protein NDUFB8 by the ATP5I knockout and its reversal by ATP5I expression is an important strength of the study. This shows that the decreased "sensitivity" to metformin in the ATP5I knock-out cells could be due to various proteins.

(3) Demonstration of converse effects of ATP5I KO and re-expression ATP5I on the NAD/NADH ratio.

Weaknesses:

(1) The interpretation of the cellular co-localization of the biotin-biguanide conjugate with TOMM20 (Figure 1-D) as mitochondrial "accumulation" of the conjugate is overstated because it cannot exclude binding of the conjugate to the mitochondrial membrane. It would have been more convincing if additional incubations with the biotin-biguanide conjugate in combination with metformin had shown that metformin is competitive with the biotin-conjugate.

(2) The manuscript reports the identification of 69 proteins by mass spectrometry of the pull-down assay of which 31 proteins were eluted by metformin. However, no Mass Spectrometry data is presented of the peptides identified. The methodology does not state the minimum number of peptides (1, 2?) that were used for the identification of the 31/69 proteins.

(3) The validation of ATP5I was based on the use of recombinant protein (which was 90% pure) for the SPR and the use of a single antibody to ATP5I. The validity of the immunoblotting rests on the assumption that there is no "non-specific" immunoactivity in the relevant mol wt range. Information on the validation of the antibody would be helpful.

(4) Knock-out of ATP5I markedly compromised the NAD/NADH ratio (Fig.3A) and cell proliferation (Figure 3D). These effects may be associated with decreased mitochondrial membrane potential which could explain the low efficacy of metformin (and most of the data in Figures 3-5). This possibility should be discussed. Effects of [metformin] on the NAD/NADH ratio in control cells and ATP5I-KO would have been helpful because the metformin data on cell growth is normalized as fold change relative to control, whereas the NAD/NADH ratio would represent a direct absolute measurement enabling comparison of the absolute effect in control cells with ATP5I KO.

(5) Figure-6 CRISPR/Cas9 KO at 16mM metformin in comparison with 70nM rotenone and 2 micromolar oligomycin (in serum-containing medium). The rationale for the use of such a high concentration of metformin has not been explained. In liver cells metformin concentrations above 1mM cause severe ATP depletion, whereas therapeutic (micromolar) concentrations have minimal effects on cellular ATP status. The 16mM concentration is ~2 orders of magnitude higher than therapeutic concentrations and likely linked to compromised energy status. The stronger inhibition of cell proliferation by 16mM metformin compared with rotenone or oligomycin raises the issue of whether the changes in gene expression may be linked to the greater inhibition of mitochondrial metabolism. Validation of the cellular ATP status and NAD/NADH with metformin as compared with the two inhibitors could help the interpretation of this data.

Reviewer #2 (Public review):

Summary:

A particular challenge in treating infections caused by the parasite Toxoplasma gondii is to target (and ultimately clear) the tissue cysts that persist for the lifetime of an infected individual. The study by Maus and colleagues leverages the development of a powerful in vitro culture system for the cyst-forming bradyzoite stage of Toxoplasma parasites to screen a compound library for candidate inhibitors of parasite proliferation and survival. They identify numerous inhibitors capable of inhibiting both the disease-causing tachyzoite and the cyst-forming bradyzoite stages of the parasite. To characterize the potential targets of some of these inhibitors, they undertake metabolomic analyses. The metabolic signatures from these analyses lead them to identify one compound (MMV1028806) that interferes with aspects of parasite mitochondrial metabolism. The authors claim that MV1028806 targets the bc1 complex of the mitochondrial electron transport chain of the parasite, although the evidence for this is indirect and speculative. Nevertheless, the study presents an exciting approach for identifying and characterizing much-needed inhibitors for targeting tissue cysts in these parasites.

Strengths:

The study presents convincing proof-of-principle evidence that the myotube-based in vitro culture system for T. gondii bradyzoites can be used to screen compound libraries, enabling the identification of compounds that target the proliferation and/or survival of this stage of the parasite. The study also utilizes metabolomic approaches to characterize metabolic 'signatures' that provide clues to the potential targets of candidate inhibitors, although falls short of identifying the actual targets.

Weaknesses:

(1) The authors claim to have identified a compound in their screen (MMV1028806) that targets the bc1 complex of the mitochondrial electron transport chain (ETC). The evidence they present for this claim is indirect (metabolomic signatures and changes in mitochondrial membrane potential) and could be explained by the compound targeting other components of the ETC or affecting mitochondrial biology or metabolism in other ways. In order to make the conclusion that MMV1028806 targets the bc1 complex, the authors should test specifically whether MMV1028806 inhibits bc1-complex activity (i.e. in a direct enzymatic assay for bc1 complex activity). Testing the activity of MMV1028806 against other mitochondrial dehydrogenases (e.g. dihydroorotate dehydrogenase) that feed electrons into the ETC might also provide valuable insights. The experiments the authors perform also do not directly measure whether MMV1028806 impairs ETC activity, and the authors could also test whether this compound inhibits mitochondrial O2 consumption (as would be expected for a bc1 inhibitor).

(2) The authors claim that compounds targeting bradyzoites have greater lipophilicity than other compounds in the library (and imply that these compounds also have greater gastrointestinal absorbability and permeability across the blood-brain barrier). While it is an attractive idea that lipophilicity influences drug targeting against bradyzoites, the effect seems pretty small and is complicated by the fact that the comparison is being made to compounds that are not active against parasites. If the authors are correct in their assertion that lipophilicity is a major determinant of bradyzoicidal compounds compared to compounds that target tachyzoites alone, you would expect that compounds that target tachyzoites alone would have lower lipophilicity than those that target bradyzoites. It would therefore make more sense to (statistically) compare the bradyzoicidal and dual-acting compounds to those that are only active in tachyzoites (visually the differences seem small in Figure S2B). This hypothesis would be better tested through a structure-activity relationship study of select compounds (which is beyond the scope of the study). Overall, the evidence the authors present that high lipophilicity is a determinant of bradyzoite targeting is not very convincing, and the authors should present their conclusions in a more cautious manner.

(3) Page 11 and Figure 7. The authors claim that their data indicate that ATP is produced by the mitochondria of bradyzoites "independently of exogenous glucose and HDQ-target enzymes." The authors cite their previous study (Christiansen et al, 2022) as evidence that HDQ can enter bradyzoites, since HDQ causes a decrease in mitochondrial membrane potential. Membrane potential is linked to the synthesis of ATP via oxidative phosphorylation. If HDQ is really causing a depletion of membrane potential, is it surprising that the authors observe no decrease in ATP levels in these parasites? Testing the importance of HDQ-target enzymes using genetic approaches (e.g. gene knockout approaches) would provide better insights than the ATP measurements presented in the manuscript, although would require considerable extra work that may be beyond the scope of the study. Given that the authors' assay can't distinguish between ATP synthesized in the mitochondrion vs glycolysis, they may wish to interpret their data with greater caution.

Reviewer #2 (Public review):

The present study by Le Gac et al. investigates the vasoconstriction of cerebral arteries during neurovascular coupling. It proposes that pyramidal neurons firing at high frequency lead to prostaglandin E2 (PGE2) release and activation of arteriolar EP1 and EP3 receptors, causing smooth muscle cell contraction. The authors further claim that interneurons and astrocytes also contribute to vasoconstriction via neuropeptide Y (NPY) and 20-hydroxyeicosatetraenoic acid (20-HETE) release, respectively. The study mainly uses brain slices and pharmacological tools in combination with Emx1-Cre; Ai32 transgenic mice expressing the H134R variant of channelrhodopsin-2 (ChR2) in the cortical glutamatergic neurons for precise photoactivation. Stimulation with 470 nm light using 10-second trains of 5-ms pulses at frequencies from 1-20 Hz revealed small constrictions at 10 Hz and robust constrictions at 20 Hz, which were abolished by TTX and partially inhibited by a cocktail of glutamate receptor antagonists. Inhibition of cyclooxygenase-1 (COX-1) or -2 (COX-2) by indomethacin blocked the constriction both ex vivo (slices) and in vivo (pial artery), and inhibition of EP1 and EP3 showed the same effect ex vivo. Single-cell RT-PCR from patched neurons confirmed the presence of the PGE2 synthesis pathway.

While the data are convincing, the overall experimental setting presents some limitations. How is the activation protocol comparable to physiological firing frequency? The delay (minutes) between the stimulation and the constriction appears contradictory to the proposed pathway, which would be expected to occur rapidly. The experiments are conducted in the absence of vascular "tone," which further questions the significance of the findings. Some of the targets investigated are expressed by multiple cell types, which makes the interpretation difficult; for example, cyclooxygenases are also expressed by endothelial cells. Finally, how is the complete inhibition of the constriction by the NPY Y1 receptor antagonist BIBP3226 consistent with a direct effect of PGE2 and 20-HETE in arterioles? Overall, the manuscript is well-written with clear data, but the interpretation and physiological relevance have some limitations. However, vasoconstriction is a rather understudied phenomenon in neurovascular coupling, and the present findings may be of significance in the context of pathological brain hypoperfusion.

Reviewer #2 (Public review):

The authors aim to investigate the role of spontaneous activity in shaping the development of multisensory integration in the brain, specifically focusing on the connections between primary visual and somatosensory sensory areas (V1 and S1) and a higher-order cortical area rostro-lateral to V1 (RL). They seek to understand how spontaneous activity guides the formation of aligned topographic maps and the emergence of bimodal neurons in RL.

First, the authors found that spontaneous activity in all three areas sparsifies over time, but S1 exhibits more mature patterns earlier than V1 and RL. They claimed that correlated activity among neighboring regions of these areas during development carries topographic information. These data were used to implement a computational model that employed Hebbian rules of synaptic plasticity. The model indicated that correlated spontaneous activity can generate topographic connectivity between S1/V1 and RL and bimodal neurons in RL. The model suggested that the more mature spontaneous activity in S1 can guide map alignment between V1 and RL. In addition, the model also suggested that a mixture of bimodal and unimodal neurons in RL is optimal for decoding information from V1 and S1.

While the data presented in the manuscript is promising and provides preliminary insights into the role of spontaneous activity in multisensory integration, it would be beneficial to strengthen the experimental foundation regarding the correlation between V1, S1, and RL. Incorporating more rigorous spatio-temporal analyses of spontaneous activity could enhance the robustness of these findings.

Here are some important concerns:

(1) The analysis of how spatial topography influences activity correlations in Figure 2 has several issues.<br /> 1a. While squares in V1 and S1 covered a small area of these sensory areas, the correlated territories in RL covered the entire area of RL. The topographic map in V1 continues caudally, so where is the rest of the map in RL? Something similar applies to the relationship between S1 and RL.<br /> 1b. It is essential to know how areas were drawn. High precision is required.<br /> 1c. It is not clear if correlated activity means different events in sync or large events that cover 2 or all 3 cortical areas of interest. The figure points to the second option, which contradicts the size of events at these stages, mainly in the oldest mice analyzed here.<br /> 1d. It is fundamental to know in detail and provide examples of how the detection of events was performed. For instance, could the dispersion of light from an event in V1 close to RL cause the detection of activity in RL?

(2) For the correlations among V1, S1, and RL, it is crucial to have a consistent method to delineate the borders of cortical areas. The authors mention in one sentence that areas were drawn according to a reference map. More details are needed to convince the reader that the borders are accurate, especially because their shape and position change with age.

(3) The results from the model seem to be based on the initial bias in connectivity between neighboring cells from the different areas. Then, it seems straightforward that implementing correlated activity with Hebbian and synaptic depression rules will force the strengthening of connections between spatially close cells. Despite this apparent predisposition of the model towards a defined outcome, the flaws in the experimental data used prevent a rigorous interpretation of the computational model.

(4) In the Introduction, the authors nicely and briefly explain the role of primary and higher-order sensory cortices in information processing. They also explain how spontaneous activity during development helps to build these circuits by refining connections or establishing hierarchies. They continue explaining the relevance of aligning different topographic maps to allow multisensory integration. Then they provide some examples of sites of multisensory integration. This provides a general context for the data presented in the Results section; however, and importantly, there is no specific introduction of why they are interested in RL and its interaction with V1 and S1. The authors should introduce the RL area and explain why it is an interesting site for multisensory processing.

(5) The results shown in Figure 1 corroborate published data from Golshani et al, Rochefort et al, Murakami et al. While the reproduction of data is more than welcome, the authors should specify which part of the data is completely new and acknowledge clearly the rest as corroboration of previous data. The sentence "As described in previous experiments ..." partially acknowledges this fact but is not clear enough. In addition, the transition between this part of the manuscript and the next data is not smooth. Data seems to be used to feed the model so perhaps the organization of the manuscript leaves room for improvement.

Reviewer #2 (Public review):

Summary

Briola and co-authors have performed a structural analysis of the human CTF18 clamp loader bound to PCNA. The authors purified the complexes and formed a complex in solution. They used cryo-EM to determine the structure to high resolution. The complex assumed an auto-inhibited conformation, where DNA binding is blocked, which is of regulatory importance and suggests that additional factors could be required to support PCNA loading on DNA. The authors carefully analysed the structure and compared it to RFC and related structures.

Strength & Weakness

Their overall analysis is of high quality, and they identified, among other things, a human-specific beta-hairpin in Ctf18 that flexibly tethers Ctf18 to Rfc2-5. Indeed, deletion of the beta-hairpin resulted in reduced complex stability and a reduction in a primer extension assay with Pol ε. This is potentially very interesting, although some more work is needed on the quantification. Moreover, the authors argue that the Ctf18 ATP-binding domain assumes a more flexible organisation, but their visual representation could be improved.

The data are discussed accurately and relevantly, which provides an important framework for rationalising the results.

All in all, this is a high-quality manuscript that identifies a key intermediate in CTF18-dependent clamp loading.

Reviewer #2 (Public review):

Summary:

This paper describes the molecular characterisation of a new isolate of the giant virus Jyvaskylavirus, a member of the Marseilleviridae family infecting Acanthamoeba castellanii. The isolate comes from a boreal environment in Finland, showcasing that giant viruses can thrive in this ecological niche. The authors came up with a non-trivial isolation procedure that can be applied to characterise other members of the family and will be beneficial for the virology field. The genome shows typical Marseilleviridae features and phylogenetically belongs to their clade B. The structural characterisation was performed on the level of isolated virion morphology by negative stain EM, virions associated with cells either during the attachment or release by helium microscopy, the visualisation of the virus assembly inside cells using stained thin sections, and lastly on the protein secondary structure level by reconstructing ~6 A icosahedral map of the massive virion using cryoEM. The cryoEM density combined with gene product structure prediction enabled the identification and functional assessment of various virion proteins.

Strengths:

The detailed description of the virus isolation protocol is the largest strength of the paper and this reviewer believes it can be modified for isolating various viruses infecting small eukaryotes. The cryoEM map allows us to understand how exceptionally large virions of these viruses are stabilised by minor capsid proteins and nicely demonstrates the integration of medium-resolution cryoEM with protein structure prediction in deciphering virion protein function. The visualisation of ongoing virus assembly inside virus factories brings interesting hypotheses about the process that; however, needs to be verified in the next studies.

Weaknesses:

The conclusions from helium microscopy images are overinterpreted, as the native membrane structure cannot be preserved in a fixed and dehydrated sample. In the image, there are many other parts of the curved membrane and a lot of virions, to me it seems the specific position of the highlighted virion could arise by a random chance. The claim that the cells were imaged in the near-original state by this method should be therefore omitted. Also, no mass spectrometry data are presented that would supplement and confirm the identity of virion proteins which predicted models were fitted into the cryoEM density. For a general virology reader outside of the giant virus field, the results presented in the current state might not have enough influence and the section should be rewritten to better showcase the novelty of findings.

Reviewer #2 (Public review):

Summary:

The authors recently uncovered a novel nested gene, Aff3ir, and this work sets out to study its function in endothelial cells further. Based on differences in expression correlating with areas of altered shear stress, they investigate a role for the isoform Aff3ir-ORF2 in endothelial activation and development of atherosclerosis downstream of disturbed shear stress. Using a knockout mouse model and in vivo overexpression experiments, they demonstrate a strong potential for Aff3ir-ORF2 to alleviate atherosclerosis. They find that Aff3ir-ORF2 interacts with the pro-inflammatory transcription factor IRF5 and retains it in the cytoplasm, hence preventing upregulation of inflammation-associated genes. The data expands our knowledge of IRF5 regulation which could be relevant to researchers studying various inflammatory diseases as well as adding to our understanding of atherosclerosis development.

Strengths:

The in vivo data is solid using immunofluorescence staining to assess AFF3ir-ORF2 expression, a knockout mouse model, overexpression and knockdown studies, and rescue experiments in combination with two atherosclerotic models to demonstrate that Aff3ir-ORF2 can lessen atherosclerotic plaque formation in ApoE-/- mice.

Weaknesses:

While the in vivo data is generally convincing, a few data panels have issues and will need addressing. Also, the knockout mouse model will need to be described, since the paper referred to in the manuscript does not actually report any knockout mouse model. Hence it is unclear how Aff3ir-ORF2 is targeted, but Figure S2B shows that targeting is partial, since about 30% expression remains at the RNA level in MEFs isolated from the knockout mice.

While the effect on atherosclerosis is clear, the conclusion that this is the result of reduced endothelial cell activation is not supported by the data. The mouse model is described as a global knockout and the shRNA knockdowns (Figure 5) and overexpression data in Figure 2 are not cell type-specific. Only the overexpression construct in Figure 6 uses an ICAM-2 promoter construct, which drives expression in endothelial cells, though leaky expression of this promoter has been reported in the literature. Therefore, other cell types such as smooth muscle cells or macrophages could be responsible for the effects observed.

The weakest part of the manuscript is the in vitro experiments. While they are solidly executed, all experiments are performed in MEFs, and results are interpreted as being equivalent to endothelial cell responses. There is also an RNA-seq experiment performed on MEFs from the Aff3ir-ORF2 knockout and control mice, but the data is not disclosed other than showing some non-identifiable expression differences. The data is used to hypothesise on a role for IRF5 in the effects observed with Aff3ir-ORF2 knockout.

Overall, the paper succeeds in demonstrating a link between Aff3ir-ORF2 and atherosclerosis, but the cell types involved and mechanisms remain unclear. The study also shows a functional interaction between Aff3ir-ORF2 and IRF5 in embryonic fibroblasts, but any relevance of this mechanism for atherosclerosis or any cell types involved in the development of this disease remains largely speculative.

Reviewer #2 (Public review):

Summary:

In their study 'AI-Based Discovery and CryoEM Structural Elucidation of a KATP Channel Pharmacochaperone', ElSheikh and colleagues undertake a computational screening approach to identify candidate drugs that may bind to an identified binding pocket in the SUR1 subunit of KATP channels. Other KATP channel inhibitors such as glibenclamide have been previously shown to bind in this pocket, and in addition to inhibition of KATP channel function, these inhibitors can very effectively rescue cell surface expression of trafficking deficient KATP mutations that cause excessive insulin secretion (Congenital Hyperinsulinism). However, a challenge for their utility for the treatment of hyperinsulinism has been that they are powerful inhibitors of the channels that are rescued to the channel surface. In contrast, successful therapeutic pharmacochaperones (eg. CFTR chaperones) permit the function of the channels rescued to the cell membrane. Thus, a key criterion for the authors' approach, in this case, was to identify relatively low-affinity compounds that target the glibenclamide binding site (and be washed off) - these could potentially rescue KATP surface expression but also permit KATP function.

Strengths:

The main findings of the manuscript include:

(1) Computational screening of a large virtual compound library, followed by functional screening of cell surface expression, which identified several potential candidate pharmacochaperones that target the glibenclamide binding site.

(2) Prioritization and functional characterization of Aekatperone as a low-affinity KATP inhibitor which can be readily 'washed off' in patch clamp and cell-based efflux assays. Thus the drug clearly rescues cell surface expression but can be manipulated experimentally to permit the function of rescued channels.

(3) Determination of the binding site and dynamics of this candidate drug by cryo-EM, and functional validation of several residues involved in drug sensitivity using mutagenesis and patch clamp.

The experiments are well-conceived and executed, and the study is clearly described. The results of the experiments are very straightforward and clearly support the conclusions drawn by the authors. I found the study to provide important new information about the KATP chaperone effects of certain drugs, with interesting considerations in terms of ion channel biology and human disease.

Weaknesses:

I don't have any major criticisms of the study as described, but I had some remaining questions that could be addressed in a revision.

(1) The chaperones can effectively rescue KATP trafficking mutants, but clearly not as strongly as the higher affinity inhibitor glibenclamide. Is this relationship between inhibitory potency, and efficacy of trafficking an intrinsic challenge of the approach? I suspect that it may be an intractable problem in the sense that the inhibitor-bound conformation that underlies the chaperone effect cannot be uncoupled from the inhibited gating state. But this might not be true (many partial agonist drugs with low efficacy can be strongly potent, for example). In this case, the approach is really to find a 'happy medium' of a drug that is a weak enough inhibitor to be washed away, but still strong enough to exert some satisfactory chaperone effect. Could some additional clarity be added in the discussion on whether the chaperone and gating effects can be 'uncoupled'?

(2) Based on the western blots in Figure 2B, the rescue of cell surface expression appears to require a higher concentration of AKP compared to the concentration-response of channel inhibition (~9 microM in Figure 3, perhaps even more potent in patch clamp in Figure 2C). Could the authors clarify/quantify the concentration response for trafficking rescue?

(3) A future challenge in the application of pharmacochaperones of this type in hyperinsulinism may be the manipulation of chaperone concentration in order to permit function. In experiments, it is straightforward to wash off the chaperone, but this would not be the case in an organism. I wondered if the authors had attempted to rescue channel function with diazoxide in the presence of AKP, rather than after washing off (ie. is AKP inhibition insurmountable, or can it be overcome by sufficient diazoxide).

(4) Do the authors have any information about the turnover time of KATP after the wash-off of the chaperone (how stable are the rescued channels at the cell surface)? This is a difficult question to probe when glibenclamide is used as a chaperone, but may be much simpler to address with a lower affinity chaperone like AKP.

Reviewer #2 (Public review):

Summary:

The regulation of kinesin is fundamental to cellular morphogenesis. Previously, it has been shown that OSM-3, a kinesin required for intraflagellar transport (IFT), is regulated by autoinhibition. However, it remains totally elusive how the autoinhibition of OSM-3 is released. In this study, the authors have shown that NEKL-3 phosphorylates OSM-3 and releases its autoinhibition.

The authors found NEKL-3 directly phosphorylates OSM-3 (although the method is not described clearly) (Figure 1). The phophorylated residue is the "elbow" of OSM-3. The authors introduced phospho-dead (PD) and phospho-mimic (PM) mutations by genome editing and found that the OSM-3(PD) protein does not form cilia, and instead, accumulates to the axonal tips. The phenotype is similar to another constitutive active mutant of OSM-3, OSM-3(G444A) (Imanishi et al., 2006; Xie et al., 2024). osm-3(PM) has shorter cilia, which resembles with loss of function mutants of osm-3 (Figure 3). The authors did structural prediction and showed that G444E and PD mutations change the conformation of OSM-3 protein (Figure 3). In the single-molecule assays G444E and PD mutations exhibited increased landing rate (Figure 4). By unbiased genetic screening, the authors identified a suppressor mutant of osm-3(PD), in which A489T occurs. The result confirms the importance of this residue. Based on these results, the authors suggest that NEKL-3 induces phosphorylation of the elbow domain and inactivates OSM-3 motor when the motor is synthesized in the cell body. This regulation is essential for proper cilia formation.

Strengths:

The finding is interesting and gives new insight into how the IFT motor is regulated.

Weaknesses:

The methods section has not presented sufficient information to reproduce this study.

Reviewer #2 (Public review):

Summary:

In this manuscript, Farber and colleagues have performed single-cell RNAseq analysis on bone marrow-derived stem cells from DO Mice. By performing network analysis, they look for driver genes that are associated with bone mineral density GWAS associations. They identify two genes as potential candidates to showcase the utility of this approach.

Strengths:

The study is very thorough and the approach is innovative and exciting. The manuscript contains some interesting data relating to how cell differentiation is occurring and the effects of genetics on this process. The section looking for genes with eQTLs that differ across the differentiation trajectory (Figure 4) was particularly exciting.

Weaknesses:

The manuscript is in parts hard to read due to the use of acronyms and there are some questions about data analysis that need to be addressed.

Reviewer #2 (Public review):

Summary:

The present study described GEARBOCS, an adeno-associated virus tool for in vivo gene editing in astrocytes. This tool is timely and important for glial biologists who often are troubled by efficient gene targeting in astrocytes. Overall the significance of the finding is valuable, and the strength of the evidence is solid. Presumably, there will be great potential associated with GEARBOCS applications in the future.

Strengths:

As efficient tools for targeting non-neuronal cells in the brains are rather limited for astrocytes and microglia, GEARBOCS adds to the small pool of currently available tools and will provide new options for glial biologists studying these tools. As the study revealed, GEARBOCS are capable of knockout and knockin manipulations for genes of interest, also ascribed with reporter tracking and gene-trap strategy. The promising multi-functional tool will advance our understanding of astrocytes and help to further elucidate the mechanism of neuron-glia interaction.

Weaknesses:

Even though the tool seems promising and powerful. the authors failed to provide more evidence on the robustness and specificity of GEARBOCS. Also, the advantages of GEARBOCS over some of the traditional methods were not clearly stated. Some of these concerns are described below.

Reviewer #2 (Public review):

Summary:

Wang et al. developed a set of optical sensors to monitor Rab protein activity. Their investigation into Rab activity in dendritic spines during structural long-term plasticity (sLTP) revealed sustained Rab10 inactivation (>30min) and transient Rab4 activation (~5 min). Through pharmacological and genetic manipulation to constitutively activate or inhibit Rab proteins, they found that Rab10 negatively regulates sLTP and AMPA receptor insertion, while Rab4 positively influences sLTP but only in the transient phase. The optical sensors provide new tools for studying Rab activity in cells and neurobiology. However, a full understanding of the timing of Rab activity will require a detailed characterization of sensor kinetics.

Strengths:

(1) Introduction of a series of novel sensors that can address numerous questions in Rab biology.

(2) Multiple methods to manipulate Rab proteins to reveal the roles of Rab10 and rab4 in LTP.

(3) Discovery of Rab4 activation and Rab10 inhibition with different kinetics during sLTP, correlating with their functional roles in the transient (Rab4) and both transient and sustained (Rab10) phases of sLTP.

Weaknesses:

(1) Lack of characterization of sensor kinetics, making it difficult to determine if the observed Rab kinetics during sLTP were due to sensor behavior or actual Rab activity.

(2) It is crucial to assess whether the overexpression of Rab proteins as reporters, affects Rab activity and cellular structure and physiology (e.g. spine number and size).

(3) The paper does not explain the apparently different results between NMDA receptor activation and glutamate uncaging. NMDA receptor activation increased Rab10 activity, while glutamate uncaging decreased it. NMDA receptor activation resulted in sustained Rab4 activation, whereas glutamate uncaging caused only brief activation of about 5 minutes. A potential explanation, ideally supported by data, is needed.

(4) There is a discrepancy between spine phenotype and sLTP potential with Rab10 perturbation. Rab10 perturbation affected spine density but not size, suggesting a role in spinogenesis rather than sLTP. However, glutamate uncaging affected sLTP, and spinogenesis was not examined. Explaining the discrepancy between spine size and sLTP potential is necessary. Exploring spinogenesis with glutamate uncaging would strengthen these results. Additionally, Figure 4j shows no change in synaptic transmission with Rab10 knockout, despite an increase in spine density. An explanation, ideally supported by data, is needed for the unchanged fEPSP slope despite an increase in spine density.

(5) Spine volume was imaged using acceptor fluorophores (mCherry, or mCherry/Venus) at 920nm, where the two-photon cross-section of mCherry is minimal. 920nm was also used to excite the donor fluorophore, hence the spine volume measurement based on total red channel fluorescence is the sum of minimal mCherry fluorescence from direct 920nm excitation, bleed-through from the green channel, and FRET. This confounded measurement requires correction and clarification.

Reviewer #2 (Public review):

This manuscript examines network mechanisms that allow networks of neurons to perform context-dependent decision-making.

In a recent study, Pagan and colleagues identified two distinct mechanisms by which recurrent neural networks can perform such computations. They termed these two mechanisms input-modulation and selection-vector modulation. Pagan and colleagues demonstrated that recurrent neural networks can be trained to implement combinations of these two mechanisms, and related this range of computational strategies with inter-individual variability in rats performing the same task. What type of structure in the recurrent connectivity favors one or the other mechanism however remained an open question.

The present manuscript addresses this specific question by using a class of mechanistically interpretable recurrent neural networks, low-rank RNNs.

The manuscript starts by demonstrating that unit-rank RNNs can only implement the input-modulation mechanism, but not the selection-vector modulation. The authors then build rank three networks that implement selection-vector modulation and show how the two mechanisms can be combined. Finally, they relate the amount of selection-vector modulation with the effective rank, ie the dimensionality of activity, of a trained full-rank RNN.

Strengths:

(1) The manuscript is written in a straightforward manner.<br /> (2) The analytic approach adopted in the manuscript is impressive.<br /> (3) Very clear identification of the mechanisms leading to the two types of context-dependent modulation.<br /> (4) Altogether this manuscript reports remarkable insights into a very timely question.

Weaknesses:

- The introduction could have been written in a more accessible manner for any non-expert readers.

Reviewer #2 (Public review):

Summary:

Scott and Frank propose a new method for controlling generalization and interference in neural networks that undergo continual learning. Their method called coordinated eligibility models (CEM), relies on the factorization of synaptic updates into input-driven and output-driving factors. They subsequently employ the fact that it is sufficient to orthogonalize any one of these two factors across different data points to nullify the interference during learning. They exemplify this on a number of toy tasks while comparing their result to vanilla gradient.

Strengths:

The specific mechanism proposed here is novel (while, as authors acknowledge, there is a large number of other mechanisms for the selective recruitment of synapses for the prevention of catastrophic forgetting). Furthermore, it is simple, elegant, and to a large extent biologically plausible, potentially pointing to specific and testable aspects of learning dynamics.

Weaknesses:

(1) Scope and toy nature of experiments: the model was only applied to very simple problems tailored specifically to demonstrate the strengths of the CEM method. Furthermore, single hyperparameter setting is presented for every scenario which leaves it questionable how general the numerical results are. The selection of input, output dimensionality and data set size also seems to be underexplored. Will a larger curriculum, smaller or larger dimension, compromise any of the CEM ingredients? Restriction to linear models seems arbitrary (it should be a no-time test to add non-linearity within a pytorch framework that authors used), and applicability for any non-synthetic problem is not obvious.

It is also unclear to what extent of domain knowledge is needed for surprise signals to be successfully generated. Can the authors make a stronger case about novel curriculum entries being easily recognizable by cosine distance, either in the brain or in machine learning? Can they alternatively demonstrate their method on a less toy benchmark (e.g. permuted MNIST from Kirkpatrick et al 2017 that they cite)?

Another limitation is that unlike smoother models of plasticity budgets (e.g. Kirkpatrick et al 17, Zenke et al 17), here eligibility seems to be lost forever, once surprise is applied. What happens to the model if more data from a previously visited task becomes available? Will the system be able to continue learning within the right context and how does CEM perform compared to other catastrophic-forgetting-prevention strategies?

(2) The clarity and organization must be improved. Specifically, the balance between verbal descriptions, equations, figures, and their captions needs to be improved. For example - two full-size equations are dedicated to the application of linear regression (around lines 183 and 236) while by far less obvious math such as settings for fig 7, including 'feature loadings', 'demands', etc., is presented in a hardly readable mixture figure and main text. Similarly, the surprise mechanism which is a key ingredient for the model is presented in a very non-straightforward fashion, scattered between the main text, figure, and methods. The figure legends are poorly informative in many cases as well (see minor comments for examples).

Reviewer #2 (Public review):

The author investigates the role of background noise on EEG-assessed speech tracking in a series of five experiments. In the first experiment, the influence of different degrees of background noise is investigated and enhanced speech tracking for minimal noise levels is found. The following four experiments explore different potential influences on this effect, such as attentional allocation, different noise types, and presentation mode.

The step-wise exploration of potential contributors to the effect of enhanced speech tracking for minimal background noise is compelling. The motivation and reasoning for the different studies are clear and logical and therefore easy to follow. The results are discussed in a concise and clear way. While I specifically like the conciseness, one inevitable consequence is that not all results are equally discussed in depth.

Based on the results of the five experiments, the author concludes that the enhancement of speech tracking for minimal background noise is likely due to stochastic resonance. Given broad conceptualizations of stochastic resonance as a noise benefit this is a reasonable conclusion.

This study will likely impact the field as it provides compelling support questioning the relationship between speech tracking and speech processing.

Reviewer #2 (Public review):

This paper examines how structural plasticity in neural circuits, particularly in dopaminergic systems, is regulated by Drosophila neurotrophin-2 (DNT-2) and its receptors, Toll-6 and Kek-6. The authors show that these molecules are critical for modulating circuit structure, dopaminergic neuron survival, synaptogenesis, and connectivity. They demonstrate that the loss of DNT-2 or Toll-6 function leads to the loss of dopaminergic neurons, reduced dendritic arborization, and synaptic impairment, whereas overexpression of DNT-2 increases dendritic complexity and synaptogenesis. Additionally, DNT-2 and Toll-6 influence dopamine-dependent behaviors, including locomotion and long-term memory, suggesting a link between DNT-2 signaling, structural plasticity, and behavior.

A major strength of this study is the impressive cellular resolution achieved. By focusing on specific dopaminergic neurons, such as the PAM and PPL1 clusters, and using a range of molecular markers, the authors were able to clearly visualize intricate details of synapse formation, dendritic complexity, and axonal targeting within defined circuits. Given the critical role of dopaminergic pathways in learning and memory, this approach provides a valuable foundation for exploring the role of DNT-2, Toll-6, and Kek-6 in experience-dependent structural plasticity. While the manuscript hints at a connection to experience-induced plasticity, the study does not establish a direct causal link between neurotrophin signaling and experience-driven changes. To support this idea, it would be necessary to observe experience-induced structural changes and demonstrate that downregulation of DNT-2 signaling prevents these changes. The closest attempt in this study was the artificial activation of DNT-2 neurons using TrpA1, which resulted in overgrowth of axonal arbors and an increase in synaptic sites in both DNT-2 and PAM neurons. However, whether the observed structural changes were dependent on DNT-2 signaling remains unclear.

In conclusion, this study demonstrates that DNT-2 and its receptors play a role in regulating the structure of dopaminergic circuits in the adult fly brain. Whether DNT-2 signaling contributes to experience-dependent structural plasticity within these circuits remains an exciting open question and warrants further investigation.

Comments on revisions:

I appreciate the authors' responses to my previous comments and have no further suggestions.