Reviewer #1 (Public review):

Processing in the primary visual cortex (V1) of mice is not only based on sensory inputs but also strongly modulated by locomotion. In this study, Meier et al. ask whether neurons that are modulated by locomotion form clusters in V1. Their work is based on previous studies from their lab establishing a modularity in the organization of primary visual cortex based on M2-muscarinic-acetylcholine-receptor-positive patches and interpatches (Ji et al. 2015, D'Souza et al. 2019). In these studies, they have highlighted the clustering of specific visual pathways and inhibition. In the current study, they extend this modularity to motor inputs, confirming a clustering of locomotion modulated neurons but also show that these clusters overlap with the M2-negative interpatches of layer 1. Finally, they establish a blueprint for visual processing streams in V1, segregating projections to and from lateral visual areas (LM, AL, and RL) from projections to and from the lateral areas, including the visual area PM, the retrosplenial cortex (RSP), and the secondary motor area (MOs).

Conceptually, this study provides an important finding in the organization of locomotion-related signaling in primary visual cortex, which clearly has substantial implications for sensory processing in visual cortex. While the anatomical data are solid, the link to physiology is incomplete. In conclusion, there are numerous issues that leave the main findings in some doubt, so the authors have some work to do before I find this story convincing.

Major issues:

(1) The major results in this study rely on proper quantification of neuronal responses during resting and running. Recently, it has been reported that hemodynamic occlusion can strongly influence measurements of fluorescent changes using two-photon imaging (Yogesh et al. 2025, doi.org/10.1101/2024.10.29.620650). Since it is unclear whether there is an inherent bias in vasculature and hemodynamic occlusion in M2 patches and interpatches, a quantification of the effect of hemodynamic occlusion would be necessary. This control would ideally be done using mice with GFP expression to test if there is still a clustering of locomotion-modulated neurons that overlaps with M2-negative interpatches. Alternatively, the authors should at the very least quantify the vascularization in M2 patches and interpatches.

(2) To assess the effects, the authors use a correlation analysis for many of their findings (e.g., Figures 2b,c, 4j,k, ...). This, however, is inappropriate to assess the significance of the results. I suggest redoing all statistics with hierarchical bootstrap sampling (Saravanan et al. 2020, PMID: 33644783) or similar.

(3) The authors use two different measures to assess whether and to what extent a neuron is locomotion sensitive, the LMI and "locomotion-responsive". While the LMI is defined based on recording in the light and dark (Figure 2), the "locomotion-responsiveness" is defined only in the dark (Figure 3a,c,d). The link between the two measures should be clarified.

a) Additionally, Figure 2b shows higher average LMI for interpatches, but the locomotion-responsive fraction is similar in interpatches and patches (relative number of pairs in Figure 3c and Figure 3d). How do the authors explain this discrepancy?

b) How is the LMI calculated - based on the average or the maximum response over stimuli? One particular stimulus? If the LMI is defined for each stimulus separately, what is plotted in Figure 2b?

(4) In the last panels of Figures 4-7, the authors analyze the alignment of cell bodies with the M2 patches. While in superficial layers it might be straightforward to align the cell body locations with the M2 patches and interpatches in layer 1, this alignment does not appear to be trivial for deeper layers. The authors should provide additional material to convince the reader of the proper alignment.

(5) Related to point 4 above - Given the importance of a proper alignment of M2 patches with the in vivo imaging, the in vivo - ex vivo alignment should be more convincing than Figure 1 C-E. Measuring M2 patches in vivo (as the authors have tried to do) would have provided more solid evidence. Have the authors tried to remove the dura for their in vivo imaging to increase signal-to-noise? In any case, more examples of proper alignment are necessary.

(6) The authors state that locomotion selectively affects M2-/M2- pairs based on Figure 3c. However, to make this claim, there should be a significant difference between the correlation of stimulus-driven noise of M2-/M2- locomotion-responsive pairs and M2-/M2- locomotion-unresponsive pairs, AND no significant difference in the same analysis for M2+/M2+ pairs (i.e., testing the differences between the bars in Figure 3c and Figure 3d).

Reviewer #1 (Public review):

Summary:

In this study, the authors investigate mechanisms of acquired resistance (AR) to KRAS-G12C inhibitors (sotorasib) in NSCLC, proposing that resistance arises from signaling rewiring rather than additional mutations.

Strengths:

Using a panel of AR models-including cell lines, PDXs, CDXs, and PDXOs-they report activation of KRAS and PI3K/AKT/mTOR pathways, with elevated PI3K levels. Pharmacologic inhibition or CRISPR-Cas9 knockout of PI3K partially restores sotorasib sensitivity, and p-4EBP1 upregulation is implicated as an additional contributor, with dual mTORC1/2 inhibition more effective than mTORC1 inhibition alone.

Weaknesses:

While the study addresses an important clinical question, it is limited by several weaknesses in experimental rigor, data interpretation, and presentation. The mechanistic findings are not entirely novel, since the role of PI3K-AKT-mTOR signaling in therapeutic resistance is already well-established in the literature. Several key conclusions are not entirely supported by the data. Furthermore, while the authors use CRISPR-Cas9 to knock out PI3K and 4E-BP1 in H23-AR and H358-AR cells to restore sotorasib sensitivity, they do not perform reconstitution experiments to confirm that re-expressing PI3K or 4E-BP1 reverses the sensitization. This prevents full characterization of PI3K and p-4EBP1 upregulation as contributors to resistance.

Comments on revised version:

The authors have addressed some but not all of my concerns and suggestions. The authors do acknowledge some of the limitations. It would be useful to include a limitations paragraph in the Discussion.

Reviewer #1 (Public review):

Summary:

This carefully executed study uncovers the functional relevance of curl signals that impinge on the retina every time an observer's gaze direction and movement direction are not aligned.

Strengths:

This finding is important, highlighting the functional role of an abundant incidental signal (curl in retinal motion) that has thus far believed to be a nuisance that needs to be filtered out of the retinal motion stream.

The study's evidence is compelling: a combination of psychophysical experiments and critical manipulations, control theory and neural modeling, which together make an internally consistent and biologically plausible case for the role of curl signals in estimating heading direction.

This study uncovers the functional relevance of curl signals that occur on the retina when an observer is moving, and gaze is not straight ahead. The experimental and modeling results clearly go beyond previous studies and significantly advance our understanding of vision-based navigation.

Another clear strength is that the study uses tightly controlled experimental manipulation to provide strong test cases for the hypothesis that curl is used for visual navigation. These conditions are important to constrain the proposed model (and future models) of heading control.

The modeling is very clearly described, and the modeling and analysis code is published and freely available. The authors go beyond a back-of-the-envelope control model and show how it might be implemented at the neural-circuit level. The model is biologically plausible.

Weaknesses:

The discussion would benefit from an extension of the implications of the study and predictions of their model.

Reviewer #1 (Public review):

Summary:

The study is technically extensive and employs a wide range of experimental approaches, including in vivo analyses, cell-based assays, and transcriptomic data integration. The authors provide a detailed characterization of inflammatory and stress-related pathways activated following IMQ exposure in mouse skin. These datasets may be informative for researchers specifically interested in IMQ-induced dermatitis or in stress responses triggered by chemical skin irritants.

Strengths:

The study is technically extensive and employs a wide range of experimental approaches, including in vivo analyses, cell-based assays, and transcriptomic data integration. The authors provide a detailed characterization of inflammatory and stress-related pathways activated following IMQ exposure in mouse skin. These datasets may be informative for researchers specifically interested in IMQ-induced dermatitis or in stress responses triggered by chemical skin irritants.

Weaknesses:

A major limitation of the manuscript is its exclusive reliance on the IMQ model, which does not adequately represent the immunological drivers, cellular interactions, or therapeutic responsiveness of human psoriasis, despite the manuscript's framing. IMQ-induced inflammation is dominated by innate immune activation and mouse-specific pathways, whereas human psoriasis is driven primarily by IL-23/IL-17-mediated interactions between keratinocytes and Th17/Tc17 cells. As a result, conclusions drawn entirely from IMQ-based experiments have limited relevance to human disease biology.

Consistent with this issue, the manuscript places strong emphasis on pathways such as TLR signaling, inflammasome activation, and IL-1-associated responses, none of which are established as central drivers of plaque psoriasis in patients. Therapeutic strategies targeting these pathways have failed to achieve clinical efficacy comparable to IL-23 or IL-17 blockade, yet this translational gap is not adequately addressed.

The in vitro keratinocyte experiments further limit interpretability. Stimulation of keratinocytes with IMQ is not an accepted model of psoriasis-relevant keratinocyte activation, and the study does not demonstrate induction of well-established psoriasis signature gene programs. Without this validation, it is difficult to assess the relevance of the observed cellular stress responses to human disease.

The RNA-sequencing analyses raise additional concerns regarding rationale and interpretation. The basis for selecting specific mouse and human datasets is unclear, including the use of unpublished or non-psoriasis inflammatory datasets. Key methodological details related to data processing, normalization, cross-species comparison, and statistical analysis are insufficiently described. In addition, the limited number of differentially expressed genes identified does not align with the extensive psoriasis transcriptomic literature, raising concerns about analytical rigor.

Finally, the manuscript emphasizes a small number of genes described as "psoriasis-associated" while failing to demonstrate regulation of widely accepted psoriasis signature genes known to correlate with disease activity and therapeutic response in patients.

Reviewer #1 (Public review):

Porte et al. investigate how observers form confidence judgments about the presence vs absence of near-threshold audiovisual stimuli. In two psychophysical detection experiments, human participants judged whether a stimulus (visual, auditory, or audiovisual) was present or absent, reported amodal confidence, and then gave modality-specific detection and confidence ratings using a bidimensional scale. The authors report that audiovisual (AV) stimuli are detected more accurately than unimodal stimuli, but that multisensory stimulation does not improve metacognitive efficiency. Participants are more confident in absence than in presence judgments. They extend a previously proposed model to an audiovisual setting, assuming evidence is available only for presence and that absence is inferred via counterfactual detectability. Detection is modeled with a disjunctive integration rule across modalities, while confidence is explained by a combination of conjunctive (for presence) and disjunctive/negation-of-disjunction (for absence) rules.

There are several points I wish to have clarified, outlined below:

(1) Framing of bimodal vs unimodal detection

On p.3, the introduction states that "Adults typically show higher detection rates and faster reaction times for bimodal than for unimodal stimuli." This is broadly consistent with the literature, but as written, it obscures the fact that these effects depend critically on experimenter-defined stimulus strengths. It is trivial to construct cases where a strong unimodal stimulus is more detectable than a bimodal stimulus made of two very weak unimodal stimuli. If "bimodal" is understood as the co-presentation of two unimodal components matched in detectability, then Bayes-rule-based arguments indeed predict better detection for the bimodal case; how much better is theoretically interesting, but not quantified in this paper. There is an entire literature on the combination of two unimodal stimuli, which is not touched on. For a pertinent reference, see Ernst & Banks 2002. I recommend clarifying that the statement assumes comparable unimodal intensities.

(2) Relationship to signal detection theory and counterfactual perceptibility

In the introduction, the authors write, "If sensory evidence is only available for presence," motivating counterfactual perceptibility as a necessary ingredient to infer absence. However, standard signal detection theory (SDT) already provides a widely accepted framework in which a continuous internal response is present on both signal and noise (absent) trials, with absence corresponding to the noise distribution and decisions implemented by a criterion.

Thus, there is no logical need to invoke counterfactual perceptibility simply to define absence; rather, the Mazor-style framework adds an explicit belief model about detectability and an optimal stopping policy. It would strengthen the paper to more clearly state how the proposed model goes beyond SDT conceptually, acknowledge that SDT can account for presence/absence decisions without counterfactuals, and position the counterfactual account as a hypothesis about how observers actually compute absence/confidence, not as a necessity. One of the central claims of the paper is that detection in the case of absence requires counterfactual reasoning. The authors should demonstrate whether or not an SDT-based generative model can describe these amodal and uni- and bi-modal stimulus decisions. In such an SDT model, an SDT-based generative model in which the noise distribution is shared across conditions, and unimodal vs bimodal differences are captured by changes in the mean or variance of the signal+noise distribution.

(3) Confidence vs performance: is AV confidence special?

The paper's central claims about multisensory confidence and metacognition would be stronger if the authors showed that AV confidence deviates from what is expected given performance alone. From the reported results, AV accuracy is around 80%, with visual and auditory at about 60% and 40%, respectively. Given that confidence typically monotonically scales with accuracy, the first question is whether AV confidence is entirely explained by improved performance, or whether there is an additional multisensory contribution. A simple, informative analysis would be for each subject, plot mean confidence vs per cent correct for AV, V, A, and absent conditions, and to test whether AV confidence lies above the trend predicted by accuracy alone.

(4) Metacognitive measures: logistic regression slopes vs meta-d′/d′

In the "Multisensory effects on metacognitive performance" section, the authors define "metacognitive sensitivity" as the slope of a Bayesian logistic regression predicting accuracy from confidence. There is substantial literature showing that logistic-slope measures of metacognitive sensitivity are criterion-dependent and can be affected by both task and confidence criteria (for one example, see Rausch & Zehetleitner, 2017). In contrast, meta-d′/d′ was specifically developed to provide a bias-invariant measure of metacognitive efficiency. Though this, too, is dated (see Boundy-Singer et al., 2023). Given that the authors already estimate HMeta-d-based M-ratios, it is unclear why they rely on logistic regression slopes as their primary "metacognitive sensitivity" metric in Figure 4A. I suggest either replacing the logistic-slope metric with SDT-based measures (meta-d′, meta-d′/d′) or providing a clear justification for using logistic slopes, along with a discussion of their known limitations.

Additionally, Figure 3 reports M-ratios without showing the corresponding d′ or meta-d′ for judge-present vs judge-absent conditions. Presenting these would help contextualize the metacognitive efficiency results and clarify whether differences are driven mainly by changes in metacognitive sensitivity, changes in task performance, or both. The d' values per condition could be added to Figure 2A.

(5) Interpretation of confidence in absence vs presence

The authors emphasise that it is surprising subjects are more confident in absence than in presence judgments, both at amodal and modality-specific levels. However, Figure 2B suggests that absent responses are very accurate: absent is reported as present only in about 10% of absent trials, implying a high correct rejection rate. If confidence tracks outcome probability, higher confidence for absence may be at least partly expected. Before attributing this asymmetry primarily to counterfactual reasoning, it would be important to explicitly relate confidence to accuracy for hits, misses, false alarms, and correct rejections and show whether absence confidence remains elevated relative to presence after controlling for accuracy differences across judgment types and conditions. Without this, the interpretation that higher absence confidence is inherently "unexpected" seems overstated.

(6) Model: integration rules, confidence, and evidence strength

The modeling section extends the Mazor et al. ideal observer to two modality-specific sensors, with disjunctive integration for detection and then disjunctive vs conjunctive integration rules for confidence. I have a few comments.

First, the detection rule is disjunctive and is reported as a finding. However, the conclusion that detection relies on a disjunctive rule ("present if A or V") closely mirrors the task instructions-participants are explicitly told to respond "present" if they detect the stimulus in any modality. As such, this seems more like a sanity check than a novel empirical finding.

Relatedly, the conjunctive detection is a weak null. The conjunctive rule ("present only if both A and V") is behaviorally implausible given the task instructions. A more informative baseline would be an SDT-style scalar-evidence model (see comment 2), rather than a conjunctive rule that participants would have to actively violate the instructions to follow.

Second, confidence in the model is defined as the probability of being correct at the time of the detection decision. However, this implies a fixed amount of evidence at decision time unless additional mechanisms are invoked. This issue is well known in diffusion modeling (see Kiani et al. 2014) and deserves explicit discussion; otherwise, it is unclear how the model produces graded confidence from a bound-crossing rule alone.

Third, the authors do not consider a straightforward evidence-strength account of confidence. When both modalities indicate presence, there is, on average, more total sensory evidence than in unimodal trials, making correct decisions more likely and, under most frameworks, confidence higher. Likewise, weak evidence in both modalities can be stronger evidence for absence than moderate in one and weak in the other. Many of the patterns that motivate the presence-conjunctive/absence-disjunctive mix could arise from a model where confidence simply reflects the amount of evidence for the chosen option, without positing distinct logical integration rules for presence vs absence. As the authors note, purely disjunctive or purely conjunctive confidence rules fail to capture the trends in confidence reports in Figure 7, leading them to adopt a combined presence-conjunctive / absence-disjunctive rule. A more parsimonious alternative-that confidence scales with evidence magnitude and cross-modal agreement-should be explicitly considered and, ideally, implemented as a competing model.


Finally, if the model is intended as a good account of the data, it would be useful to report whether it also reproduces the metacognitive efficiency patterns (M-ratios) beyond the mean confidence patterns shown in Figures 7-8. At present, the model appears systematically over-confident, which should be acknowledged and quantified.

(7) Confidence asymmetry index (CAI) and modality weighting

The confidence asymmetry index (CAI) is defined as the difference between auditory and visual confidence on AV vs absent trials, and the authors report strong correlations between observed and simulated CAI across participants. They interpret this as evidence that subjects place different weights on auditory vs visual signals. Several questions arise. First, does CAI capture asymmetries beyond what is expected from accuracy differences between modalities and conditions? Second, because the simulated data are generated from model fits to the observed data, a correlation between observed and simulated CAI is expected: the model is built to reproduce the individual patterns it is then compared to. A stronger test would compare CAI from data simulated with modality-specific belief parameters, versus CAI from data simulated with constrained equal belief parameters (same θs). Relatedly, the paper would benefit from a plot showing the distribution of θs for A and V- present stimuli across subjects. These values could also be related to unimodal sensitivity measured in the calibration/training phases. A natural prediction is that higher unimodal sensitivity should correspond to higher belief parameters for presence.

Reviewer #1 (Public review):

Summary:

Bot et al. introduce GeneSLand, a computational framework to quantify and visualize gene expression specificity across diverse transcriptomic datasets. The method leverages expression level-breadth (L-B) relationships to construct multi-level specificity landscapes and derives metrics such as lbSpec and dRate to characterize gene specificity in a threshold-independent manner. The authors showed the applicability of the approach across bulk RNA-seq, single-cell datasets, and cross-species primate brain data, showing that specificity patterns captured by this approach reflect both tissue-specific expression and evolutionary distances. Overall, the framework represents an interesting and potentially useful contribution to the analysis of gene expression specificity.

Strengths:

(1) Introduces an original conceptual framework based on expression level-breadth relationships to characterize gene specificity.

(2) Provides a threshold-independent approach that could overcome some limitations of classical specificity metrics.

(3) Demonstrates the applicability of the framework across different biological datasets.

Weaknesses:

(1) The method relies on predefined binning thresholds for expression levels, and the sensitivity of the derived metrics to this parameter is not fully explored.

(2) The advantages of lbSpec relative to established metrics could be more clearly shown with some biological examples.

(3) The robustness of the framework with noisy datasets, small sample sizes, or lower sequencing depth is not well evaluated.

Reviewer #1 (Public review):

Summary:

This manuscript investigates the degradation dynamics of extracellular DNA in soils and its impact on estimates of microbial abundance and diversity. By combining a broad geographic sampling design with a primer-labeling strategy, qPCR quantification, amplicon sequencing, and PMA treatment, the authors aim to disentangle total versus intracellular DNA signals and explore sequence-specific degradation patterns. The topic is relevant, particularly given the increasing awareness of relic DNA as a confounding factor in microbial ecology. The experimental design is ambitious and potentially impactful. However, several conceptual inconsistencies, methodological ambiguities, and statistical limitations currently weaken the robustness of the conclusions. These issues need to be addressed.

Strengths:

The manuscript addresses a timely and important question in microbial ecology, particularly given the growing recognition that relic DNA can bias interpretations of community composition derived from amplicon sequencing. The study is ambitious in scope, incorporating a broad geographic sampling design across multiple soil types, which enhances the generalizability of the findings. The use of a controlled microcosm experiment combined with a primer-labeling strategy to track extracellular DNA dynamics is conceptually innovative and provides a structured framework to investigate degradation processes.

In addition, the integration of multiple approaches, including qPCR for absolute quantification, high-throughput sequencing for community profiling, and PMA treatment to differentiate extracellular from intracellular DNA, represents a comprehensive attempt to disentangle complex sources of bias in soil microbiome analyses. The effort to link degradation dynamics with environmental variables and to explore sequence-level patterns further demonstrates the authors' intent to move beyond descriptive analyses toward a mechanistic understanding.

Weaknesses:

Several conceptual and methodological issues currently limit confidence in the study's conclusions. Key terms such as "sequence-specific degradation" are not clearly defined or supported by a mechanistic or structural hypothesis, making it difficult to interpret the biological meaning of the results. In addition, the bioinformatic workflow presents inconsistencies, particularly the use of ASVs followed by clustering at 97% similarity, which undermines the resolution required to support sequence-level inferences. Statistical analyses are also insufficiently described, including unclear definitions of "T values," a lack of detail on pairing structure, and no indication of multiple testing correction.

Furthermore, important methodological details are missing or unclear, including primer design (e.g., GAPDH tag vs ACTF), Illumina library preparation (e.g., adapter and indexing strategy), and validation of PMA treatment efficiency. The interpretation of PMA-treated samples as representing "living communities" is likely overstated, given the known limitations of the method in soil systems. Finally, typographical errors, inconsistent terminology, and unclear phrasing throughout the manuscript reduce readability and further complicate interpretation.

Reviewer #1 (Public review):

Summary:

Sugarman, Vanselow et al. adapted a microCT instrument to permit imaging of an entire organism, a hatchling octopus. In the resulting 3D dataset, they segmented the major organ systems, including the vascular, respiratory, digestive, and nervous systems. The authors released the dataset through a public web interface, and present some observations about body-wide neuroanatomy.

Strengths:

- The dataset is of good quality and access to a whole-cephalopod anatomical resource will be useful for the scientific community.

- The interactive web interface facilitates exploration of the dataset.

Weaknesses:

- The authors identify a series of bundles of nerve fibers between the suckers and the central brain and propose that these structures together constitute the chemotactile pathway, linking sensation to learning and memory. This is an over-interpretation of the available evidence. The data is not presented in a way that allows the reader to independently assess the proposed anatomical relationships: many images include near-opaque colored overlays on the fibers of interest, making it difficult to determine whether these bundles truly merge or interface. Additionally, the mesoscale resolution achieved here reveals the presence of large nerve bundles but cannot resolve the origin or synaptic relationships of the neurons in the bundles - including those from the chemotactile receptors of the suckers. There are likely multiple synapses between the periphery and the central brain, and the location and connectivity of individual neurons are not visible at this resolution. Consequently, this dataset does not demonstrate structural connectivity. Elucidating a neural circuit would require complementary approaches such as neuronal tracing or electron microscopy connectomics.

- The language used in the manuscript is often overly complex and convoluted, making it difficult to follow the main arguments and to assess the strength of the claims. In addition, some vocabulary in the main text is overly technical (e.g. related to microCT or anatomy), making it difficult for a general biology or cephalopod audience to understand, while some neuroscience vocabulary is used imprecisely or in ways that overstate what can be concluded from anatomical data. A substantial rewrite using clearer, more cautious language is recommended. Additionally, a deeper discussion of the observed octopus arm anatomy, and how this may relate to its semi-autonomous function would make this article of greater interest to a broader audience.

Reviewer #1 (Public review):

Mutations in CDHR1, the human gene encoding an atypical cadherin-related protein expressed in photoreceptors, are thought to cause cone-rod dystrophy (CRD). However, the pathogenesis leading do this disease is unknown. Previous work has led to the hypothesis that CDHR1 is part of a cadherin-based junction that facilitates the development of new membranous discs at the base of the photoreceptor outer segments, without which photoreceptors malfunction and ultimately degenerate. CDHR1 is hypothesized to bind to a transmembrane partner to accomplish this function, but the putative partner protein has yet to be identified.

The manuscript by Patel et al. makes an important contribution toward improving our understanding of the cellular and molecular basis of CDHR1 associated CRD. Using gene editing, they generate a loss of function mutation in the zebrafish cdhr1a gene, an ortholog of human CDHR1, and show that this novel mutant model has a retinal dystrophy phenotype, specifically related to defective growth and organization of photoreceptor outer segments (OS) and calyceal processes (CP). This phenotype seems to be progressive with age. Importantly, Patel et al, present intriguing evidence that pcdh15b, also known for causing retinal dystrophy in previous Xenopus and zebrafish loss of function studies, is the putative cdhr1a partner protein mediating the function of the junctional complex that regulates photoreceptor OS growth and stability.

This research is significant in that it:

(1) provides evidence for a progressive, dystrophic photoreceptor phenotype in the cdhr1a mutant and, therefore, effectively models human CRD; and

(2) identifies pcdh15b as the putative, and long sought after, binding partner for cdhr1a, further supporting the theory of a cadherin-based junction complex that facilitates OS disc biogenesis.

Comments on the revised version of the manuscript:

The authors adequately addressed previous comments related to lack of details on quantitative and statistical analyses and methods. In this regard, I believe the revised manuscript presents a stronger analysis of the data. I also appreciated the revised discussion section, which better contextualizes their new data with previous observations in different animal models.

The authors provided additional evidence in Fig 1C-H for the co-localization of pcdh15b and actin within CPs using immunolabeling with super resolution imaging. This data firmly supports their other observations. A similar approach tends to also show co-localization of actin and cdhr1a, although the authors suggest that the pattern of expression is less overlapping, which would be expected if cdhr1a is predominately expressed in the OS membranes whereas pcdh15b is predominantly expressed in the CP membranes. In my opinion the data presented to support this separation is still not that convincing. Moreover, the authors show that both cdhr1a and pcdh15b are expressed in CPs using immuno-TEM (Fig 1I). This is a difficult question to address experimentally, and it is, of course, still plausible that pcdh15b within the CP membrane and cdhr1a within the OS membrane are interacting in trans. However, I just don't think that the data unequivocally support mutually exclusive localization of these proteins as suggested by the authors and depicted in the model in Fig 1J.

Reviewer #1 (Public review):

Summary:

The manuscript by Tsukamoto et al. describes a compelling approach to understanding whether inter-species differences in social behavior might emerge from differential expression patterns of the oxytocin receptor (Oxtr) in the brain. To this end, they genetically engineer BAC transgenic mouse lines with insertions of a large construct incorporating prairie vole Oxtr gene and surrounding regulatory elements. They name these lines Koi lines. They first evaluate if prairie vole-like Oxtr expression is reproduced in the Koi mouse lines, and they find heterogenous patterns across different lines that do not depend on the number of insertions. While they found that Koi mice can reproduce vole-like expression in PFC, NAc, and BLA, the reproduction was never complete: one Koi line had NAc and mPFC expression, another had BLA expression, etc. They confirmed major expression patterns across 3 methods: crossing with LacZ reporter line, in situ hybridization, and ligand binding (autoradiography). To determine the expression pattern of the BAC insert but not endogenous Oxtr, the authors generated new mouse lines by crossing Koi lines with Oxtr -/- line. Importantly, they found that Oxtr expression pattern in the mammary gland was similar across all lines, and wild-type mice.

The authors used Koi:Oxtr-/- lines to test social behavior, specifically partner preference ( a behavior specific to prairie voles) and maternal behavior. They find that different Koi lines showed different changes in these behaviors compared to wild-type mice. Moreover, while some lines showed changes in partner preference, others seemed to show changes in maternal behavior. For one of the lines (Koi4), the partner preference and the maternal behavior were incongruent.

The manuscript then hypothesizes that the Oxtr gene is positioned in different 3D chromatin structures across species and across tissues, leading to more rigid expression in the mammary glands, but more flexible expression patterns in the brain.

Strengths:

This study has major implications in the field of oxytocin research, and more broadly in the field of neuromodulation. It is novel, bold, and rigorous.

Weaknesses:

(1) The expression in the brain and mammary gland (Figure 2) was not quantified, preventing a more objective conclusion that the brain has flexible expression and mammary gland expression is rigid.

(2) In Figure 7, a similar heatmap for the mammary gland is missing.

(3) Partner preference in males was not tested.

(4) It is unclear if in the behavioral testing the stimulus animals were the same genotype as the focal female or were wild-types. This could have an impact on the behavioral outcome.

Reviewer #1 (Public review):

Summary:

The authors describe co-regulated gene modules underlying stage differentiation in Leishmania donovani through a system-level analysis of multiple molecular layers. Using amastigotes isolated from infected hamster spleens and corresponding culture-derived promastigotes, they analyzed genomic variation, transcript abundance, protein levels, phosphorylation states, and metabolite profiles. By combining these, the study identified potential regulatory mechanisms associated with parasite differentiation and generated hypotheses regarding how gene expression is coordinated across different levels.

Strengths:

A major strength of the study is the breadth of the dataset generated. The integration provides an unusually comprehensive view of molecular changes associated with Leishmania differentiation in vitro. Such multi-layer datasets involving bona fide vertebrate host stages remain relatively rare in parasitology and will likely become a valuable resource for the molecular parasitology community. In addition, the use of amastigotes isolated from infected hamsters rather than relying on axenic models provided a biologically relevant framework for the analyses.

The revised manuscript improved several aspects of the original. The RNA-seq analysis is described with a clearer pipeline, and several claims regarding causal regulatory feedback associations have been appropriately toned down. Among the observations reported, the association between parasite differentiation and proteasome-mediated protein degradation is particularly remarkable. The combination of quantitative proteomics with pharmacological inhibition of the proteasome with lactacystin provides support for a role for protein turnover in developmental transitions and paves the way for future mechanistic studies.

Weaknesses:

Most regulatory interpretations remain largely inferential or indirect. The integration identifies correlations between different levels, but direct functional validation is limited/absent. Many of the descriptions should not be interpreted as validated. As highlighted by the authors in this revised version, the mechanistic studies will be part of future work and are beyond the scope of the current work. Of note, the attempt to confirm lactacystin-induced inhibition of proteasomal activity via anti-polyUb immunoblotting did not demonstrate the expected outcome of increase in overall poly-ubiquitylation.

Comments on revised version:

The authors have appropriately addressed my comments and questions from the initial review process. My remaining concern relates to the lack of evidence to confirm proteasomal inhibition by lactacystin in both promastigotes and amastigotes. The immunoblotting experiment newly presented does not reveal a clear increase in the levels of poly-ubiquitylated proteins in treated parasites. In fact, poly-Ub levels were lower at both the 4h and 18h timepoints of treatment. If alternative antibodies or additional immunoblots are not available, the manuscript would benefit from an expanded discussion of this observation and potential explanations. In particular, the interpretation that lactacystin stabilizes ama- and pro-specific degradation would be greatly strengthened by such validation.

Reviewer #1 (Public review):

Summary:

The authors aim to study mutational paths connecting WW domains with different binding specificities. Their approach combines an unsupervised sequence generative model based on RBMs with a path-sampling algorithm. The key result is that most intermediate sequences along the designed transition paths retain measurable binding activity in wet-lab assays, whereas paths containing the same mutations introduced in a randomized order are largely non-functional. This difference is attributed to epistatic interactions captured by the RBM model.

Strengths:

Exploring mutational paths in high-dimensional protein sequence space is a challenging problem. The computational framework used here is state-of-the-art and is strengthened by systematic experimental characterization of binding activity. The study is comprehensive in scope, including multiple transition paths both within and across WW specificity classes, and the integration of modeling with high-throughput experimental validation is a clear strength.

Weaknesses:

A major concern is whether the stated goal of specificity switching is fully achieved. Along the sampled transition paths, most intermediate variants appear to retain specificity close to either the initial or the final class, rather than exhibiting gradually shifting specificity. For example, in Figure 4G (Class I to Class II/III), binding appears largely binary, with intermediates behaving similarly to one of the endpoints. A similar pattern is observed in Figure 3H for the Class I to Class IV transition, where binding responses are close to 0 or 1. In this sense, the specificity-switching objective is only partially realized by assigning two endpoints with different specificity. This raises a broader conceptual question: is it possible that different WW specificities evolved from a common ancestor without passing through intermediates that exhibit mixed or intermediate specificity? If so, then inferring specificity-switching pathways purely from extant natural sequences may be fundamentally challenging.

Reviewer #1 (Public review):

Summary:

In this paper, the authors investigate the effects of Miro1 on VSMC biology after injury. Using conditional knockout animals, they provide the important observation that Miro1 is required for neointima formation. They also confirm that Miro1 is expressed in human coronary arteries. Specifically, in conditions of coronary diseases, it is localized in both media and neointima and, in atherosclerotic plaque, Miro1 is expressed in proliferating cells.

However, the role of Miro1 in VSMC in CV diseases is poorly studied and the data available are limited; therefore, the authors decided to deepen this aspect. The evidence that Miro-/- VSMCs show impaired proliferation and an arrest in S phase is solid and further sustained by restoring Miro1 to control levels, normalizing proliferation. Miro1 also affects mitochondrial distribution, which is strikingly changed after Miro1 deletion. Both effects are associated with impaired energy metabolism due to the ability of Miro1 to participate in MICOS/MIB complex assembly, influencing mitochondrial cristae folding. Interestingly, the authors also show the interaction of Miro1 with NDUFA9, globally affecting super complex 2 assembly and complex I activity.<br /> Finally, these important findings also apply to human cells and can be partially replicated using a pharmacological approach, proposing Miro1 as a target for vasoproliferative diseases.

Comments on revisions:

The authors have adequately addressed all the concerns raised by the reviewers, and the manuscript has been substantially improved

Reviewer #1 (Public review):

Summary:

This article provides new insights into the organisational changes of the X4-tropic HIV-1 co-receptor CXCR4 upon binding of the viral receptor-binding protein X4-gp120, either in its soluble form or when displayed as Env on virus-like particles (VLPs). The study employs single-particle tracking total internal reflection fluorescence (SPT-TIRF) microscopy to quantify the dynamics and clustering of CXCR4 on CD4+ T cells. The data show that CXCR4 clusters in the presence of X4-gp120 and VLPs, a phenomenon that is also observed for the primary HIV-1 receptor CD4. The authors also show that a WHIM mutant of CXCR4 (CXCR4-R334X) that does not cluster in the presence of its natural ligand, CXCL12, clusters in the presence of X4-gp120 and VLPs.

Major strengths:

The data are well presented, discussed, and supported by solid evidence. Literature is cited appropriately.

Major weaknesses:

The authors have addressed my concerns in the revised manuscript.

Significance:

In summary, the work is presented in a clear fashion, and the main findings are properly highlighted. The paper will be of interest to the broader virology community as well as to researchers studying cell receptor clustering. The findings are not entirely surprising because it has been shown previously that the binding of Env to CD4 mediates CD4 clustering, which would also suggest clustering of the co-receptor. Nonetheless, the paper provides strong evidence that CXCR4 clusters and changes its dynamics in the presence of CD4 and X4-gp120. Moreover, the evidence that X4-gp120 clusters CXCR4-R334X is of high interest as it suggests a different binding mechanism for X4-gp120 from that of the natural ligand CXCL12, raising questions for further research.

Reviewer #1 (Public review):

Summary:

Yang et al. investigate the central pathways underlying nociceptive responses in Drosophila. The authors employ a behavioral platform they previously developed, which uses laser stimulation to deliver nociceptive stimuli while enabling automated tracking of fly behavior. By combining large-scale behavioral screening with circuit tracing approaches, the study identifies a set of dopaminergic neurons (DANs) and mushroom body output neurons (MBONs) that participate in the transmission of nociceptive signals. Nociceptive escape behavior has generally been regarded as largely reflexive. It is therefore intriguing that the mushroom body, a neural circuit classically associated with learning, is involved in this process. In particular, the recruitment of dopaminergic neurons typically linked to both appetitive and aversive valence is noteworthy and raises interesting questions about how nociceptive information is integrated within the circuits. Overall, the findings are conceptually interesting and may provide useful insights into dissecting the nociceptive escape behavior.

Strengths:

The behavioral assay used in this study is high-throughput and appears reproducible. The authors screened a large number of genetic lines, and the behavioral responses were carefully quantified. The trans-Tango tracing results are consistent with the behavioral screening results. And the observation that circuits typically associated with learned behaviors (mushroom body) contribute to a nociceptive escape response, generally considered a hard-wired reflex, is conceptually interesting.

Weaknesses:

The use of laser stimulation to induce nociceptive stimuli makes the paradigm difficult to combine with calcium imaging or optogenetic manipulations. As a result, the study lacks functional and temporally precise tests of the proposed circuit mechanisms.

Several aspects of the Methods section require additional detail:

(1) How was the behavioral potency level calculated? Since some of the split-GAL4 lines label multiple neurons, and the individual neurons may innervate multiple compartments. It is therefore unclear how a single "behavioral potency level" value was assigned to a compartment.

(2) Additional details are needed on how velocity was calculated, particularly the time window used for the analysis. In the Kir-silenced condition, the variation in velocity appears smaller than in the control group, which would benefit from clarification.

(3) Connectome analysis. More details are needed regarding how DAN-MBON connectivity was quantified in Figure 5. For example, were only DAN → MBON connections considered, or were bidirectional connections included?

Reviewer #1 (Public review):

Summary:

This paper presents a wireless device for closed-loop control of optogenetic stimulation based on behavioral triggers. The authors demonstrate the device through two behavioral experiments in mice, showcasing the device's capabilities and emphasizing open accessibility and using off-the-shelf components.

Strengths:

The paper presents a device that is open access and easily reproducible for wireless stimulation in a closed loop based on behavioral triggers. Other strengths of the device include the simultaneous use of multiple devices in parallel and the claimed ease of integration with existing frameworks. The paper shows to behavioral experiments on multiple mice along with some device validation results.

Weaknesses:

The main weakness of the presented device lies in the lack of flexibility in stimulation power. For a device that is intended for stimulation only, having to physically change a component on the board to adapt stimulation power is a major downside. Reprogrammable stimulation current is not complex to implement and should really have been included on this device. Another weakness lies in the limited battery life of the device. While using a battery-powered device decreases spatial constraints, allowing for the maze experiment presented in the paper, it also means the lifespan of the device is limited compared to an inductively powered device, limiting its ability for long-term experiments.

Reviewer #1 (Public review):

Summary:

Mancl et al. present an integrative structural and mechanistic analysis of the human insulin-degrading enzyme (IDE), combining cryo‑EM, time‑resolved cryo‑EM, SEC‑SAXS, enzymatic assays, all-atom molecular dynamics (MD) simulations, and coarse‑grained MD simulations. Their study delineates how IDE undergoes coordinated open-close transitions and interdomain rotations, how these motions relate to its unfoldase and protease activities, and how a single residue, R668, acts as a molecular latch governing these conformational changes. Through expanded structural datasets and computational analyses, the authors propose a mechanistic model for how IDE captures, unfolds, and degrades diverse amyloidogenic substrates such as insulin and Aβ.

Strengths:

A major strength of this study is its integration of structural, biophysical, biochemical, and computational approaches. The authors now provide six cryo‑EM structures, including a new time‑resolved O/O state captured 123 ms after substrate mixing, which clarifies the early structural response of IDE to insulin binding. The combination of multibody analysis, 3D variability analysis, all‑atom MD, and coarse‑grained Upside simulations yields a coherent picture in which rotational interdomain motions and charge‑swapping events at the IDE‑N/C interface underpin substrate unfolding and repositioning.

The identification of R668 as a central determinant of the open-close transition, supported by MD, HDX‑MS data from prior work, SEC‑SAXS, and functional assays on the R668A mutant, represents a significant mechanistic advance. The inclusion of Aβ degradation assays adds biological breadth and supports the conclusion that R668 modulates activity in a substrate‑dependent manner.

The authors have also substantially improved clarity by reorganizing figures, refining section headers, and adding introductory structural schematics. Taken together, the revised manuscript now provides a rigorous and accessible framework for understanding IDE dynamics and their relevance to amyloid peptide turnover.

Weaknesses:

At this stage, remaining limitations are modest and inherent to the system rather than the approach. While the study convincingly demonstrates substrate‑dependent modulation of IDE dynamics, it does not experimentally assess additional endogenous substrates (e.g., amylin, glucagon), which would be needed to fully generalize the role of R668 across the substrate spectrum of IDE. Furthermore, the timescale mismatch between MD simulations and catalytic turnover, which the authors clearly acknowledge, means that correlations between simulated motions and enzymatic kinetics remain inferential. Finally, some flexible cryo‑EM states (particularly O/pO) continue to exhibit moderate local resolution, which constrains atomic interpretation of highly dynamic regions, although this is addressed transparently.

Reviewer #2 (Public review):

Summary

This study addresses the hypothesis that the higher prevalence of autoimmune diseases in women could result from sex-dependent differences in thymic generation or selection of TCR repertoires. The biological question is important and the dataset is valuable. However, the study has major conceptual and analytical limitations.

In particular:

- The conclusions cannot be generalized to autoimmune diseases as a whole, as only type 1 diabetes (T1D) and celiac disease (CeD) antigens were analyzed.<br /> - The central interpretation is not supported by the data, as the observed signal is strongly influenced by TCRs associated with T1D, which shows a male-biased incidence and therefore does not align with the female bias the study aims to explain.

Strengths

The key strength of this work is the newly generated dataset of TCR repertoires from sorted thymocyte subsets (DP and SP populations). This approach enables the authors to distinguish between biases in TCR generation (DP) and thymic selection (SP). Bulk TCR sequencing allows deeper repertoire coverage than single-cell approaches, which is valuable here. However, the absence of TRA-TRB pairing and HLA context limits the interpretability of antigen specificity analyses.

Weaknesses

The authors did not adequately address the central concerns raised in the previous review. As a result, the major issues remain unresolved.

(1) Generalization to autoimmune diseases is not justified.

The study aims to explain the higher prevalence of autoimmune diseases in females. The main conclusion is based on enrichment in females of TCRs annotated as autoimmune-associated using database matching.<br /> However, these matches correspond exclusively to TCRs specific for T1D and CeD. This already limits the conclusions to these two diseases and does not justify generalization to autoimmune diseases as a whole.

(2) Contradiction with epidemiology of T1D which is male-biased

T1D and CeD have opposite sex biases in European populations. While CeD is more frequent in females (~60%; doi:10.1016/j.cgh.2018.11.013), T1D is more frequent in males (male:female = 1.11 in France; doi:10.1111/dom.70124).<br /> Importantly, T1D constitutes a substantial fraction of the autoimmune-associated dataset (42 out of 48 epitopes; 83 out of 185 TRB sequences). Therefore, the observed signal is strongly influenced by a disease that does not follow the female bias the study aims to explain.

The authors argue that T1D sex bias varies globally, including female-biased incidence in East Asia and Africa. However, this argument does not resolve the issue, as the cohort analyzed in this study was derived from France, where T1D shows a male-biased incidence. Thus, the interpretation remains inconsistent with the population context of the dataset.

(3) Lack of disease-level and donor-level resolution

The authors combine T1D and CeD into a single "autoimmune" category and do not provide per-disease, per-donor or per-epitope distributions, despite explicit reviewer's requests.

This prevents evaluation of whether the observed signal is driven by:<br /> - a specific disease (T1D or CeD), or<br /> - a small number of donors

Without this analysis, the conclusions cannot be properly interpreted.

(4) Use of "polyspecificity" concept is not supported by experimental evidence

The authors extensively use the concept of "polyspecific TCRs," defined as single-chain CDR3 sequences annotated across databases as recognizing distinct and unrelated antigenic categories. This concept is not supported by experimental evidence (except for a single TCR in Quiniou et al., as acknowledged by the authors).

In the absence of robust validation, a more parsimonious explanation for such ambiguously annotated TCR chains is the presence of false-positive annotations in public databases (see, e.g., Ton Schumacher's preprint https://www.biorxiv.org/content/10.1101/2025.04.28.651095.abstract) or alternatively, distinct TRA pairing for identical TRB sequences resulting in different specificities.

The observation that these TCRs have high generation probability is expected, as TCRs found in independent studies are likely to have high generation probability. The interpretation of these sequences as biologically meaningful entities (e.g., a "first line of defense") is therefore speculative and not supported by the data.

The authors also refer to in silico-generated polyspecific TCRs (ref. to Nature Machine Intelligence). However, such sequences are generated ex vivo and do not undergo thymic selection. A TCR capable of recognizing multiple unrelated foreign antigens would likely also recognize self-antigens and be eliminated during negative selection. Therefore, this argument does not support the biological relevance and in vivo existence of the proposed polyspecific TCR class.

(5) Insufficient statistical analysis of diversity

The absence of statistically significant differences in repertoire diversity between sexes (Figure 3), despite an apparent visual trend, may reflect limited sample size and insufficient statistical power rather than a true absence of differences. A more appropriate statistical approach, such as mixed-effects modeling, was requested in the previous review but was not performed.

Reviewer #1 (Public review):

Summary:

Age-related synaptic dysfunction can have detrimental effects on cognitive and locomotor function. Additionally, aging makes the nervous system vulnerable to late-onset neurodegenerative diseases. This manuscript by Marques et al. seeks to profile the cell surface proteomes of glia to uncover signaling pathways that implicated in age-related neurodegeneration. They compared the glial cell-surface proteomes in the central brain of young (day 5) and old (day 50) flies and identified the most up- and down-regulated proteins during the aging process. 48 genes were selected for analysis in a lifespan screen, and interestingly, most sex-specific phenotypes. Among these, adult-specific pan-glial DIP-β overexpression (OE) significantly increased the lifespan of both males and females and improved their motor control ability. To investigate the effect of DIP-β in the aging brain, Marques et al. performed snRNA-seq on 50-day old Drosophila brains with or without DIP-β OE in glia. Cortex and ensheathing glia showed the most differentially expressed genes. Computational analysis revealed that glial DIP-β OE increased the cell-cell communication, particularly with neurons and fat cells.

Strengths:

(1) State-of-the-art methodology to reveal the cell surface proteomes of glia in young and old flies.

(2) Rigorous analyses to identify differentially expressed proteins. 3

(3) Examination of up- and down-regulated candidates and identification of glial-expressed mediators that impact fly lifespan.

(4) Intriguing sex-specific glial genes that regulate life span.

(5) Follow-up RNA-seq analysis to examine cellular transcriptomes upon overexpression of an identified candidate (DIP-β).

(6) A compelling dataset for the community that should generate extensive interest and spawn many project.

Weaknesses:

(1) DIP-β OE using flySAM:

a) These flies showed a larger increase in lifespan compared to using UAS-DIP-β (Figure 2 C,D). Do the authors think that flySAM is a more efficient way of OE than UAS? Also, the UAS construct would be specific to one DIP-β isoform while flySAM likely would likely express all isoforms. Could this also contribute to the phenotypes observed?

b) The Glial-GS>DIP-β flySAM flies without RU-486 have significantly shorter lifespans (Figure 2C) than their UAS-DIP-β counterparts. flySAM is lethal when expressed under the control of tubulin-GAL4 (Jia et al. 2018) likely due to toxicity of such high levels of overexpression. Is it possible that larger increase in lifespan is due to the already reduced viability of these flies?

c) Statistics: It is stated in the Methods that "statistical methods used are described in the figure legend of each relevant panel." However, there is no description of the statistics or sample sizes used in Figure 2.

(2) Figure 3: The authors use a glial GeneSwitch (GS) to knock down and overexpress candidate genes. In Figure 3A, they look at glial-GS>UAS-GFP with and without RU. Without RU, there is no GFP expression, as expected. With RU, there is GFP expression. It is expected that all cell body GFP signal should colocalize with a glial nuclear marker (Repo). However, there is some signal that does not appear to be glia. Also, some many glia do not express GFP, suggesting the glial GS driver does not label all glia. This could impact which glia are being targeted in several experiments.

(3) It is interesting that sex-specific lifespan effects were observed in the candidate screen.

a) The authors should provide a discussion about these sex-specific differences and their thoughts about why these were observed.

b) The authors should also provide information regarding the sex of the flies used in the glial cell surface proteome study.

c) Also, beyond the scope of this study, examining sex-specific glial proteomes could reveal additional insights into age-related pathways affecting males and females differentially.

(4) The behavioral assay used in this study (climbing) tests locomotion driven by motor neurons. The proteomic analysis was performed with the central adult brain, which does not include the nerve cord where motor neurons reside. While likely beyond the scope of this study, it would be informative to test other behaviors including learning, circadian rhythms, etc.

(5) It is surprising that overexpressing a CAM in glia has such a broad impact on the transcriptomes of so many different cell types. Could this be due to DIP-β OE maintaining the brain in a "younger" state and indirectly influencing the transcriptomes? Instead of DIP-β OE in glia directly influencing cell-cell interactions? Can the authors comment on this?

Comments on revisions:

The authors have conducted additional experiments, updated text/figures, and included discussions to address the concerns raised by the reviewers. I commend the authors on a thorough, rigorous study that will undoubtedly impact the field and spawn many projects for years to come.

One minor comment: In Figure S2, the figure legend states "A-C"; however, the figure itself only has an A and B.

Reviewer #3 (Public review):

Summary:

Nigro et al examine how the locus coeruleus (LC) influences the medial prefrontal cortex (mPFC) during attentional shifts required for behavioral flexibility. Specifically, they propose that LC-mPFC inputs enable mice to shift attention effectively from texture to odor cues to optimize behavior. The LC and its noradrenergic projections to the mPFC have previously been implicated in this behavior. The authors further establish this by using chemogenetics to inhibit LC terminals in mPFC and show a selective deficit in extradimensional set shifting behavior. But the study's primary innovation is the simultaneous inhibition of LC while recording multineuron patterns of activity in mPFC. Analysis at the single neuron and population levels revealed broadened tuning properties, less distinct population dynamics, and disrupted predictive encoding when LC is inhibited. These findings add to our understanding of how neuromodulatory inputs shape attentional encoding in mPFC and are an important advance. There are some methodological limitations and/or caveats that should be considered when interpreting the findings and these are described below.

Strengths:

The naturalistic set-shifting task in freely-moving animals is a major strength, and the inclusion of localized suppression of LC-mPFC terminals builds confidence in the specificity of the behavioral effect. Combining chemogenetic inhibition of LC while simultaneously recording neural activity in mPFC with miniscopes is state-of-the-art. The authors apply analyses to population dynamics, in particular, that can advance our understanding of how the LC modifies patterns of mPFC neural activity. The authors show that neural encoding at both the single cell level and the population level are disrupted when LC is inhibited. They also show that activity is less able to predict key aspects of the behavior when the influence of LC is disrupted. This is quite interesting and adds to a growing understanding of how neuromodulatory systems sharpen tuning of mPFC activity.

Weaknesses:

Weaknesses are mostly minor, but there are some caveats that should be considered. First, the authors use a DBH-Cre mouse line and provide histological confirmation of overlap between HM4Di expression and TH immunostaining. While this strongly suggests modulation of noradrenergic circuit activity, the results should be interpreted conservatively as there is no independent confirmation that norepinephrine (NE) release is suppressed and these neurons are known to release other neurotransmitters and signaling peptides. In the absence of additional control experiments, it is important to recognize that effects on mPFC activity may or may not be directly due to LC-mPFC NE.

Another caveat is that the imaging analyses are entirely from the extradimensional shift session. Without analyzing activity data from the intradimensional shift (IDS) session, one cannot be certain that the observed changes are to some feature of activity that is specific to extradimensional shifts. Future experiments should examine animals with LC suppression during the IDS as well, which would show whether the observed effects are specific to an extradimensional shift and might explain behavioral effects.

Comments on revisions:

The authors overall do a nice job of addressing reviewer comments, and I believe the manuscript is significantly improved.

Reviewer #1 (Public review):

Genetically encoded fluorescent proteins expressed in specific cell types allow recognising them in vivo and, if the protein is a functional indicator, as in the case of genetically encoded calcium indicators (GECIs), to record activity from the same cellular ensemble. Ideally, if proteins (fluorophores) have perfectly distinct spectral properties, signals can be distinguished from as many cell types as the number of employed fluorophores. In practice, fluorescent proteins have non-negligible crosstalk both in absorption and emission bands. In addition, fluorescence contribution of each fluorophore normally varies from cell to cell and therefore spectral properties of cells expressing two or more proteins are different. The work of Phillips et al. addresses this challenge. The authors present an approach defined as "Neuroplex", allowing identification of up to nine cell types from the same number of fluorophores. The fingerprint of each cell is then associated with functional fluorescence from the GECI GCaMP, allowing recording calcium activity from that specific cell. The method is implemented in vivo using head-mounted miniscopes.

The authors used a mouse line expressing GCaMP in cortical pyramidal neurons and developed an experimental pipeline. First, they injected the nine AAV viruses, causing expression of fluorophores in a different brain area. The idea was not to image that area, but a non-infected medial prefrontal cortex (mPFC) section where neurons could be infected by their axons projecting in an injected area, in this way being identified by their targeting region(s). A GRIN lens, allowing spectral analysis, was mounted in the mPFC section, and GCaMP fluorescence was then recorded during behavioural tasks and analysed to identify regions of interest (ROIs) corresponding to neuron somata. After functional imaging, the head of the mouse was fixed, spectral analysis was performed, and after necessary correction for chromatic distortions, the fluorophore contribution was determined for each ROI (neuron) from where GCaMP signals were detected. Notably, the procedures for estimation and correction of chromatic aberration and light transmission (described in Figure 2) were a major challenge in their technical achievements. The selection of the nine fluorophores was another big effort. This was done by combining computer simulations and direct measurement of spectra from individual proteins expressed in HEK293 cells. It is important to say that the authors could simulate arbitrary combinations of two or more different fluorophores and evaluate the ability of their algorithm to detect the correct proteins against wrong estimations of false-negative (absence of an expressed protein) or false-positive (presence of a non-expressed protein). Not surprisingly, this ability decreases with the level of GCaMP expression. The authors underline that most errors were false-negatives, which have a milder impact in terms of result interpretation, but the rate of false positives was, nevertheless, relevant in detecting a second fluorophore from a cell expressing only one protein. The experimental profiles of fluorophores were dependent both on the specific fluorescent protein and on the projecting area, and the distribution of double-labelled did not match anatomical evidence. This result should be taken as the limitation of the present pioneering experiments, presented as proof-of-principle of the approach, but Neuroplex may provide far improved precision under different experimental conditions.

In my view, the work of Phillips et al. represents a significant advance in the state-of-the-art of the field. The rigorous analysis of limitations in the use of Neuroplex must be considered an important guideline for future uses of this approach.

Comments on revision:

The authors have adequately addressed my comments.

Reviewer #1 (Public review):

In this study, the authors investigated a specific subtype of SST-INs (layer 5 Chrna2-expressing Martinotti cells) and examined its functional role in motor learning.

Most of the issues remain unaddressed. The findings across experiments are inconsistent, and it is unclear how the authors performed their analyses or why specific time points and comparisons were chosen. The study will require major re-analyzing and additional experiments to substantiate its conclusions.

After reading the reviewers' responses, my major concerns about the manuscript remain unresolved, particularly regarding the arbitrarily defined stages of learning in the motor learning task and how the calcium imaging data align with the animal's movements.

- In line 331, the authors refer to session 5 as "training," describing it as the final spoon session, and session 6 as "re-training," because it is the first session in which the pellet is presented on the plate rather than on the spoon. However, in Fig. 1F-H, even in the Ctrl group, it is clear that the performance drops significantly in session 5, which is supposed to be the easiest session before switching to the more difficult plate condition.

- In the classic pellet-reaching task, the spoon sessions would typically be considered "shaping", while the plate sessions would represent the actual training phase. However, in this manuscript, the authors still insist on referring to session 2 as "learning" and session 5 as "training." I don't understand the difference between session 2 and session 5, especially when session 5's performance is lower than session 2 (even in Fig 1H when you compare succ ratio).

- Since session 6 (on the plate) is considered as "retraining," why don't the authors present the behavioral results beyond session 6? As a result, it remains unclear whether the animals improved their performance during the retraining phase.

- Lastly, in Fig. 4B the authors present only the success ratio and claim that performance improves with CLZ application. However, when comparing sessions 8-10 between the Ctrl and Cre⁺ groups, there already appears to be a baseline difference. CLZ treatment in Cre⁺ mice seem to bring performance only to the WT level rather than producing a clear improvement beyond baseline.

- Regarding the alignment between imaging and behavior, the authors report ~100 prehensions per minute. However, the calcium imaging traces show fewer than 20-30 spikes over 150 seconds (~2.5 min; Fig. 1E). This discrepancy raises concerns about whether the authors can truly isolate calcium signals corresponding to individual prehension events (either successful ones or multiple combined events for unsuccessful attempts). The manuscript still does not present behavioral data that directly aligns prehension events with calcium imaging activity. Although the authors performed analyses suggesting that prehension-related activity does not systematically alter non-prehension epochs, this claim is difficult to evaluate without seeing the underlying traces. It is therefore unclear how the authors selected the example calcium traces aligned to prehension onset, given that there are more than 100 prehension events per minute.

- In Fig. 1I, the authors also did not address why neural activity during successful trials is already lower one second before movement onset. The longer traces provided do not help to explain this observation or clarify the origin of this pre-movement reduction in activity. It actually further suggests that there may be some artifacts in the imaging that could affect the analysis.

- Overall, because it remains difficult to understand exactly what the authors are analyzing (and because the definitions of the motor learning stages appear arbitrary) it is difficult to agree with the authors' conclusion that Ma2s cells reduce PyrN cell assembly plasticity during learning, thereby possibly facilitating already acquired motor skills.

Reviewer #1 (Public review):

Nio and colleagues address an important question about how the cerebellum and ventral tegmental area (VTA) contribute to extinction learning of conditioned fear associations. This work tackles a critical gap in the existing literature and provides new insights into this question in humans through the use of high-field neuroimaging with robust methodology. The presented results are novel and will broadly interest both the extinction learning and cerebellar research communities. As such, this is a very timely and important contribution.

Strengths:

The core finding - coupling of cerebellum and VTA as a reward-like prediction errors during fear extinction - is novel and addresses a genuine gap in the literature. Also the paradigm spanning several sessions, a well-powered sample, 7T imaging and complementary analytical approaches to target the question is commendable.

Weaknesses:

The authors have satisfactorily addressed the concerns raised in the previous version of the manuscript. Several results, as well as conclusions drawn from them, still rest on trend-level evidence, although the revised presentation of the results now provides a more balanced interpretation of these findings.

Reviewer #1 (Public review):

Summary:

The aim of this paper is to model the spontaneous emergence of sequences in networks of plastic spiking neurons. By spontaneous, they mean that the inputs have no structure, no sequences, but the network nevertheless generates sequences. To obtain this, they assume several synaptic plasticity and single neuron plasticity rules. The primary findings are that sequences can emerge, that they slowly drift over time, that weights also constantly change over time, but that very strong weights are more stable. The main driver of this result is the plasticity rules assumed.

Strengths:

The paper is based on simulations of a relatively large network of conductance based integrate and fire neurons. There are two different pair-based STDP rules assumed for excitatory-to-excitatory synapses and for inhibitory-to-excitatory synapses. In addition, weights are normalized, and there is an adaptation due to plasticity of the spiking threshold. The network is analyzed via simulations and data processing akin to what would be done for physiological data. The simulations are extensive, and the analysis seems rigorous.

Weaknesses:

There are several fundamental problems with the paper:

(1) The plasticity mechanisms used assumed that pair-based STDP is sufficient to account for synaptic plasticity in vivo. This is unrealistic. Various different papers have shown that pair-based STDP models do not account well for experimental data. If this model is a simulation of the visual cortex (unclear), then firing rates can be sufficiently high, such that firing rates are more important than spike times. We already know that firing rates matter due to the original Markram et al paper from 1997. Even if pair-based STDP is used, we already know from Bi and Poo 1998 that there is a weight dependence of synaptic plasticity such that strong weights potentiate less and decay more. This additional assumption alone might completely change the results in this study. We don't really know how to model realistic synaptic plasticity, but we know pair-based STDP is a bad model. Would these results be robust enough for a change in the learning rule, for example, to triplet-based, calcium-based, or voltage-based? Are the results shown even robust enough to include slight modifications to the learning rule, for example, weight dependence of pair-based STDP?

(2) The first stage of training, in which the network reaches a steady state, is unclear. What type of activity is exhibited in this network? Does most of it arise from the external inputs? What firing rates are obtained? What are the spike statistics? This is important because this activity is responsible for generating the emergent sequences, and also depends (I think) on the plasticity mechanisms. Does the 'spontaneous activity' in the network depend strongly on the external input? Figure 1E is where we see a raster plot, but we see only neurons within a sequence, and it seems neurons within the sequence fire almost only once. Before showing sequences that more general structure of the spiking activity and how it evolves should be explained and quantified.

(3) Do these sequences really emerge without structured inputs? Is there any evidence to suggest that such sequences emerge without a structured input? If yes, please cite it. It makes sense that it would, because the time scale of these sequences is much faster than the sensory or behavioral time scale. However, experimental evidence to support this will make the paper much more interesting.

(4) This paper is a phenomenological paper. It does not really say what these sequences might be good for, except for a cite or two, and it does not model any specific experiment. There is a medium here (a plastic spiking network) which generates a phenomenon (sequences). It also generates other measurable phenomena, such as connectivity motifs. Such motifs have been quantified in animals. It would be natural to compare the motif statistics found here to motifs characterized experimentally. This would make these results more substantial.

(5) There are implicit predictions in the work. For example, about the stability of strong vs. weak efficacies or the stability of different motifs. Such predictions should be made more explicit.

Reviewer #1 (Public review):

The wide-ranging serotonergic projections emerging from the Dorsal Raphe nucleus (DRN) are suggestive of a central role in regulating brain-wide activity and behavioural states. DRN activity has been associated with diverse functions, ranging from mood, motivation and pain regulation to sleep and cognitive flexibility. Its far-reaching connectivity made it challenging to assess the brain-wide effect of its activation, especially during behaviour.

The present study by Qi et al. addresses these challenges by combining state-of-the-art tracking microscopy with the whole-brain accessibility of the larval zebrafish model. To investigate the effect of DRN activation, the authors leveraged the Tg(tph2:ChrimsonR) line to optogenetically activate tph2-positive neurons in the DRN, while monitoring changes in brain-wide activity, locomotion and auditory-stimuli evoked responses.

Optogenetic activation had a suppressing effect on locomotion, which the authors distinguished from inducing sleep by the maintenance of posture and its sleep disturbing effect of nighttime stimulations. Further, the authors report a distinct effect of DRN activation on motor-related, but not auditory-related neuronal subspaces, identified by demixed principal component analysis.

In addition, rather than affecting all motor-correlated neurons similarly, tph2+ DRN-mediated suppression focused on neurons encoding high-amplitude or turning motion.

In summary, the work of Qi et al. provides solid evidence for a predominant role of the DRN in wake-state motor suppression by aptly combining the vast data-acquisition possibilities of the larval zebrafish model with computational methods to extract relevant information.

The brain-wide scope of the analysis is a key strength, reducing bias, confirming the involvement of known motor and auditory regions, and providing a valuable dataset for future analyses.

While the results well support the conclusion of the authors, certain biological and technical aspects demand discussion.

Reviewer #1 (Public review):

Summary:

This article investigates the application of commonly employed analytic methods in electrophysiological neuroscience to the speech envelope taken from 17 different languages' audio corpora. The findings indicate that features observed in speech-brain tracking responses, specifically theta and gamma oscillations, as well as their phase-amplitude coupling, are actually present within the speech envelope itself. This suggests that the neural data recorded in response to speech primarily reflects an evoked response to the temporal statistical properties of the envelope, rather than an inherent neural mechanism. Data from 18 individuals with epilepsy listening to French speech further support this interpretation: theta and gamma oscillations, along with their phase-amplitude coupling, are absent at rest and are linearly driven by the acoustic envelope during speech perception.

Strengths:

I find these results very interesting and convincing, with a strong take-home message: we should exercise caution when interpreting observed theta/gamma activity and the associated phase-amplitude coupling during speech comprehension tasks.

Weaknesses:

I mostly have comments on clarifications regarding the methods, specifically on the criteria for language exclusion, and on the statistical testing and reporting.

(1) Clarification is needed regarding the rationale for the number of languages analysed: initially, 17 languages were considered, six were excluded due to the absence of PAC in the high gamma range, yet the analysis was ultimately conducted on only nine languages, not eleven. Could you please explain this discrepancy?

(2) Considering the six languages that did not exhibit any statistically significant high-frequency PAC, do you have potential reasons for this result? Might it be related to the fundamental frequency (F0) of the speakers' voices? If six languages out of seventeen do not show PAC, can we argue that this feature is universal across languages?

(3) How is inter-subject variability addressed within the SEEG analysis? The authors report the percentage of SEEG independent components showing significant effects in power spectral changes, PAC, and other measures, but it is unclear whether these components are consistent across participants or whether only a few participants drive the effect. It would be helpful to report how many participants are retained for each selection of SEEG-ICs in the article. Currently, the statistical testing of the SEEG-ICs also appears to assume independent samples. It would be helpful to include group-level statistical tests across subjects, for instance by performing mixed-effects models and including participant as a random factor.

Reviewer #1 (Public review):

Summary:

The authors report results from an EEG study investigating neural oscillations in 8-month-old infants, as well as an adult control group. Participants were presented with cartoon figures flickering at different frequencies, as well as a broadband condition. While adults showed the well-known dominant response at 10 Hz, infants showed dominance resonance at 4 Hz, irrespective of stimulation frequency. The authors interpret this finding as evidence for the fundamental role of 4 Hz oscillations in early development and discuss two conflicting theories regarding the underlying functionality.

Strengths:

Overall, this is a very well-designed and rigorous study, and the results significantly add to our understanding of a very fundamental aspect of early brain activity. The study is embedded in a coherent theoretical framework, and the authors discuss possible implications and next steps with great clarity.

Weaknesses:

I see relatively few weaknesses in this paper. It does not statistically compare infant and adult responses, which would add to the argument that infant responses actually differ from adult ones, but I don't think this is necessary at this point for the authors' argument.

In contrast, I actually like about the paper that the authors had a very clear vision of what they wanted to look at - 4 Hz oscillation responses in 8-month-olds - and this is exactly what they did. Yes, this does not answer all questions one might have, especially about the function of 4-Hz-oscillations in infants, but it goes a long way in characterising properties in 4 Hz oscillations, which provides the starting point for several potential future lines of research.

Reviewer #1 (Public review):

Summary and Strengths:

Shin et al deepen our understanding of high-frequency oscillations in the frontal cortex during REM in a manner that sheds important light on the roles of these events. In particular, they reveal that cortical HFOs are modulated by theta oscillations, occur in chains and recruit cortical neuronal activation patterns in a manner that is distinct from other high-frequency events during non-REM or in the hippocampus. They also show that these events occur during increased oscillatory cross-talk between hippocampus and cortex and may protect cortical neurons from downregulation of firing during sleep. Overall, this is important work with several novel observations pointing towards an important role for these events that will become increasingly understood over time.

I also wanted to comment that 2D is a beautiful illustration of separate and essentially exclusive communication channels used during HF events in NREM vs REM. They almost perfectly complement each other's frequencies.

Weaknesses:

I have only one major scientific critique: I believe we need to see quantification of how phasic REM theta waves with versus without HFOs differ. What do REM HFOs add to the "normal" theta oscillation? Without this comparison, it is more difficult to interpret the meaning of these events. Given that HFO chains have IEIs around the time of a theta cycle duration, are the repeating spiking activities stronger during HFO repeats than during adjacent theta waves without HFOs? What percentage of theta waves contain HFOs, and what is the firing rate during those theta waves with vs without HFOs? Is there differential firing rate modulation? The authors may even consider that all REM-HFO-specific quantifications should be shown as differential from phasic theta cycles without HFOs.

As a non-scientific comment on the manuscript itself: unfortunately, the paper is difficult to read and understand at times, requiring great effort by the reader. This is to an extent that communication is hindered. The paper is dense with changing methods, often from panel to panel. Unfortunately, the panel quantifications are not explained in the results section in a manner that readers can understand without going to read the methods, often for each individual panel. These measures should be explained in a way that lets readers understand the conclusions of each panel and what gross calculations were used to reach those. Instead, too much jargon is used rather than clear descriptions of the overall calculations being done for each panel. 


The authors mention in the discussion section that they see increased functional connectivity between mPFC and CA1, but most data suggesting this seems to be based on LFP rather than spiking. Functional connectivity is best defined by spiking-spiking relationships. And these authors have spiking data. So I believe either the descriptive language should be pulled back to something like "oscillatory coupling" or more analyses should be dedicated to showing spike-spike coordination across regions.

Reviewer #1 (Public review):

Summary:

The manuscript presents a three-dimensional and molecular atlas of the adult hagfish brain to investigate the evolutionary origin and early diversification of vertebrate brain organization. Using whole-brain tissue clearing, light-sheet microscopy, and computational reconstruction, the authors generate a high-resolution 3D anatomical model of the hagfish brain. They complement this structural analysis with gene-expression profiling of neurotransmitter systems and receptors, including glutamatergic, GABAergic, cholinergic, serotonergic, and dopaminergic markers.

Strengths:

Together, the work aims to establish a modern neuroanatomical reference for the hagfish. Given the phylogenetic importance of hagfish as one of two extant species of cyclostomes (the other being lamprey), and the fact that the hagfish brain has barely been studied in contrast to the lamprey, the atlas provides a foundational resource and should be of interest to evolutionary and comparative neurobiology.

Weaknesses:

However, there are several places where both data presentation and the narrative can be improved and clarified, and particularly some of the homology and evolutionary claims seem to be superlative and need to be toned down. I present more detailed comments below:

(1) The authors spend too much effort trying to convince readers of the monophyly of hagfish and lamprey to stress its importance for evolutionary comparisons. This is now well accepted; instead, there could be more details on some of the specific, unique features of the hagfish brain relevant to a comparative atlas. For instance, the unusual fusion of the telencephalon anteriorly with the olfactory bulb and posteriorly with the diencephalon (Wicht and Northcutt, 1992), the degenerate visual system, the absence of the pineal gland, and the oculomotor system can be discussed in reference to the generated atlas and examined marker expression in related structures and their possible identity.

(2) The assertion that the MGE is absent in the lamprey is incorrect based on Sugahara et al. (2016; 2017), who identified lamprey paralogues of Nkx2.1/2.4 that are expressed in the ventral subpallium. This should be corrected.

(3) The major contribution of this study, in my mind, is the "three-dimensional atlas" of the hagfish brain. However, the atlas itself is not presented; A video of the 3D reconstructed Nissl-stained hagfish brain would be an important data resource and should be added. Annotations of forebrain, midbrain and hindbrain regions and constituent major structures can also be illustrated, which will be a useful resource.

(4) In the pallium, there seems to be an inner GABAergic cell layer and inner and outer glutamatergic cell layers, as noticed in lampreys (Suryanarayana et al., 2017). What are the overall proportions of glutamatergic and GABA neurons? In the images, it does seem that vGlut neurons are present in both P2 and P4, while there appear to be more GAD neurons in P4.

(5) As a general comment, homology claims should be toned down throughout the manuscript. This would at least require some connectivity data or transcriptomic analysis for any possible suggestions; the current data, with few markers, are insufficient for any reasonable comparisons.

(6) Expression of Pax6 and AChE is not sufficient to suggest a cerebellum-like structure. While it is true that embryonic Pax6 expression in the rhombic lip of the hagfish embryo is more comparable to other vertebrates than lamprey, and the presence of a rudimentary cerebellum-like structure would be of great interest, the evidence is too limited for such claims and should be toned down.

(7) Again, expression of Tbr1 and GAD1 in NCvl neurons does not suggest that these could be hippocampal neurons. One would at least need to rule out expression of prethalamic markers and demonstrate the presence of pallial markers through transcriptomic data (as in Lamanna et al., 2023).

(8) Presence of GABAergic neurons in the striatum - is there any data on expression of dopamine receptors, particularly given the seeming loss of the D2 receptor subtype in the hagfish?

Reviewer #1 (Public review):

Summary:

The manuscript provides a well‑argued discussion of the misalignment between common predictive performance evaluations reported in the literature and actually measuring clinical utility in the context of predictive psychiatry. Specifically, the authors discuss measurement reliability and prevalence as two neglected factors which can substantially inflate the assessment of model performance for clinical practice. To mitigate this, the authors offer a concrete framework and an accompanying web tool, with which to adjust performance metrics and additional predictive‑value and decision‑analytic measures.

Strengths:

The manuscript speaks convincingly about the risk of face validity and the practical irrelevance of seemingly promising predictive models in psychiatry. The authors outline how predictive performance estimations often fail to generalize to clinical contexts and thereby potentially mislead scientific efforts. In the face of ubiquitous biomarker models and incremental improvements in the literature, the reader is reminded that, irrespective of the glory of the proposed model, low reliability of clinical measurements fundamentally affects (and limits) both effect sizes and predictive performance ("garbage in, garbage out"), and that neglecting this can ultimately lead to misinformed decisions in the treatment of individual patients. The provision of an online tool with a user‑friendly interface and clearly worked examples is a major practical asset that will facilitate the adoption of the proposed framework beyond quantitative methodologists.

Weaknesses:

While the outlined issues highlight important aspects in the translational gap, the suggested solutions remain somewhat theoretical. For example, the use of prevalence might not reflect what a model would see in practice, assuming that population prevalence and the composition of actual clinical cohorts are aligned. Accounting for who presents to care, and under which referral or triage patterns, is a crucial determinant of effective base rates. While the authors do acknowledge the importance of using base rates from the target population, these nuances could be emphasized more prominently at the points where practical recommendations are made. Relatedly, the analytical context and the methodological assumptions are not clearly specified. Many arguments and demonstrations are derived in univariate, group‑comparison settings and then discussed in a way that can be read as broadly applicable.

Reviewer #1 (Public review):

Summary:

Here the authors attempted to test whether the function of Mettl5 in sleep regulation was conserved in Drosophila, and if so, by which molecular mechanisms. To do so they performed sleep analysis, as well as RNA-seq and ribo-seq in order to identify the downstream targets. They found that the loss of one copy of Mettl5 affects sleep, and that its catalytic activity is important for this function. Transcriptional and proteomic analyses show that multiple pathways were altered, including the clock signaling pathway and the proteasome. Based on these changes the authors propose that Mettl5 modulate sleep through regulation of the clock genes, both at the level of their production and degradation, possibly by altering the usage of Aspartate codon.

Comments on revisions:

The authors addressed all my comments satisfactorily.

Reviewer #1 (Public review):

Summary:

This study aims to clarify MATR3's function and molecular mechanism in oocyte growth and maturation, explore its association with OMA, and its potential as a diagnostic and therapeutic target using specific knockout mouse models, human OMA samples, and multi-omics technologies. And it has fully achieved preset objectives with results strongly supporting conclusions. Specifically, it addresses the gap in the synergistic mechanism of epigenetic and secretory signals regulated by RNA-binding proteins (RBPs) in oocyte growth and enriches the molecular etiological spectrum of oocyte maturation disorders. It is the first time the conservative function of MATR3 has been revealed in multiple species, providing a paradigm for cross-species research on RBPs in the field of reproductive biology. It also provides a new candidate target for OMA, a clinically refractory infertility disease, and is expected to promote the optimization of assisted reproductive technology and the development of precision medicine.

Strengths:

The strengths of this study are significant and prominent. First, the research system is comprehensive, integrating knockout mouse models, in vitro knockdown models, multi-species (mouse, porcine, and human) verification, combined with scRNA-seq, LACE-seq, CO-IP, and other multi-omics and molecular biology technologies, forming a complete and progressive evidence chain. Second, the mechanism analysis is in-depth, clarifying the dual molecular mechanisms of MATR3 regulating the transcriptional synthesis and secretion of GDF9 through "recruiting KDM3B to regulate H3K9me2 demethylation" and "directly binding to Rdx mRNA", with a clear logical closed loop. Third, the clinical correlation is close. It is the first time to find abnormal nuclear localization of MATR3 in oocytes of OMA patients, providing new clues for clinical disease mechanism research, and verifying the downstream function of GDF9 through rescue experiments, effectively enhancing the translational value of the results.

Weaknesses:

This study included only one OMA patient's oocyte sample. Without clinical screening for MATR3 mutations or abnormal expression, establishing a causal relationship between MATR3 and OMA remains difficult.

Reviewer #1 (Public review):

The manuscript by Fisher et al describes the molecular mechanism underlying how G beta gamma subunits engage with the beta 3 isoform of PLC. The paper used a combination of cryo EM, BRET assays, and biochemical assays of PLC beta activity. A key discovery is that G beta gamma is not sufficient to drive membrane binding by itself, and instead promotes G alpha activation. The work is important, but suffers slightly from some ambiguity in the actual interface that is present in their cryo EM model, as crosslinkers could stabilise a transient and non-native complex. This is somewhat abrogated by the careful mutational analysis, which shows that mutation of any of these three sites does somewhat block PLC beta G beta gamma activation. However, there could be some improvement in the presentation of this data, as well as possible mutant selection. Overall, this paper is a nice complement to the Falzone et al paper, showing the membrane-bound complex of PLCB3 on membranes, with this work building on this work, highlighting the importance this will have in our full understanding of PLC beta activation.

Major concerns:

My biggest concern is the potential that this interface is artefactual based on the crosslinking strategy utilised. Here are thoughts on how this could be better validated, presented in a more convincing way.

(1) The authors' main claim is that there is a degree of plasticity of G beta gamma binding to the PLC beta 3 isoform, with three possible binding sites. The main complication of this is, of course, the possibility that the crosslinking stabilises a non-native complex, driven by a mutated cysteine.

Because of this, any other additional details about this interface are going to be critical for the scientific audience to judge if this is accurate.

What would greatly help Figure 1 is an evolutionary conservation analysis of the novel Gbg interface in PLC, to see how well this is conserved, and compare this to the conservation of the previously annotated sites. Conservation of these sites on both the G beta gamma and PLC side would help justify this as a native complex.

This will also help orient the reader to the identity of the mutated residues assayed in Figure 3.

(2) The g beta gamma orientation is also different than what I have observed in previous g beta gamma effector structures. Is there any precedent for this as an effector interface? A supplemental figure comparing this structure to other g beta gamma interfaces from other enzymes, for example recent Tesmer structure with PI3K.

(3) The mutational analysis in Figure 2D-G seems to give some strange results, and I have some question why certain residues were chosen rather than others. Mutation of the Gbg side will be more complicated, as of course that can affect any of the three surfaces. My main question is that, from the way Figure 2A is oriented, the main salt bridge in their novel interface to me looks like R199-D228, with K183 being in the wrong orientation to E226, and D167 being far from any charged residues. Why did the authors not make the corresponding R199 to D or E mutation?

(4) To help the reader's interpretation of Figure 2A, I would recommend a supplemental figure showing the density for interfacial residues, as that also would increase confidence in the interface.

Reviewer #1 (Public review):

Summary:

The authors set out to understand the complex regulation of the assembly of the Type 3 Secretion System of S. typhimurium. They found that the gene synteny as well as specific mRNA stem loops were important for the translational coupling of sctS and sctT. Without this regulation, SctT self-oligomerizes, which disrupts the export of effector proteins and leads to a decreased fitness of the pathogen. The work was done using a variety of convincing methods and leads to an updated picture of how T3SS assembly occurs. Since the same genetic synteny is found in a large majority of T3SS in different bacteria, it is likely that this is a general mechanism, but one that needs to be further experimentally validated.

Strengths:

The paper uses an impressive amount of experiments, with different techniques, to describe how they identified the genetic regulation of SctT production.

Weaknesses:

Only minor weaknesses are found.

(1) Regarding the use of the complex being unique. It is not well explained what makes this a unique complex.

(2) The paper would benefit from a discussion regarding how regulation might work in the minority of bacterial strains where the T3SS gene synteny is largely different. One would expect that those bacteria would have a different way of regulating T3SS assembly, but that is not discussed at all by the authors.

Reviewer #1 (Public review):

Summary:

This is an interesting and well-written manuscript in which the authors set out to answer a simple, old question with a modern toolkit: where in crab evolution did sideways walking arise, how often has it been lost or regained, and is it plausibly linked to the ecological and taxonomic success of true crabs. To do this, they record locomotion from 50 live species, convert each species' movements into a quantitative index that compares forward versus sideways bouts, and then map the resulting states onto a recent crab phylogeny to infer the most likely evolutionary history of locomotor direction.

Strengths:

The strongest part of the study is the dataset itself. Comparable behavioral measurements across dozens of crab species are rare. The authors have done the field and husbandry work needed to make this possible. The overall pattern they recover, that most true crabs are strongly biased toward sideways movement (while a smaller set of lineages move predominantly forward), is interesting and likely to be useful to others. The phylogenetic mapping is also a reasonable way to address the "how many times" question (although this is peripheral to my expertise). The manuscript makes a convincing case that sideways locomotion is not simply a trivial byproduct of a crab-like body plan.

Weaknesses:

Where I am less convinced is in how strongly the authors describe the discreteness of the behavioral categories and the absence of intermediates. The manuscript states that the Forward-Sideways Index shows a clear separation between two locomotor types with little evidence for intermediates, and it cites a statistical test rejecting a single peak in the distribution. However, the histogram in Figure 3 appears structured within each labeled category, with subclusters inside both the forward and sideways groups rather than a single tight peak per group. This matters because the index is built by first placing each movement bout into "forward" versus "sideways" bins using a fixed angle boundary and then collapsing the result into a single ratio. That approach is simple and transparent enough, but it can also hide mixed strategies. For example, a species that produces substantial amounts of both forward and sideways walking can still end up with a strongly positive or negative index, and therefore be classified as a pure "type," even though the underlying behavior is mixed. In that context, rejecting a single peak in the across-species distribution does not, by itself, justify the stronger claim that intermediates are rare or absent.

Related to this, a key methodological choice is the use of 60 degrees as the cutoff between forward and sideways bouts. This boundary may be reasonable as a convention, but the paper does not explain why it is the right place to draw the line, and there is a plausible biological concern that a fixed angular cutoff does not mean the same thing across taxa.

Crabs vary in body shape and in how the legs are arranged around the body. In my own comparative work, for example, some species show an elliptical stance pattern elongated along the preferred direction of travel, while others show a more circular leg arrangement, and the latter can express more mixed forward and sideways behavior. When limb arrangement and body geometry differ across species, the same measured angle can correspond to different underlying mechanics and different functional "degree of sidewaysness." The practical implication is that the reported binary separation may partly reflect the imposed classification rule, rather than a sharp biological divide.

Another limitation that affects interpretation is the decision to use one individual per species. I understand the logistics, and for some questions, a single representative individual can be a reasonable first pass. But it is not strong support for negative claims about intermediates, especially in a group where individuals can change substantially with growth and allometry. Crabs can grow dramatically, often with pronounced allometric shifts in limb proportions that can alter the center of mass location. Size alone can alter the kinematics and choice of locomotor behaviors in crustaceans. In species where appendage proportions change with size, or where certain legs become disproportionately large (or calcified), it is plausible that locomotor direction and the distribution of movement angles shift across ontogeny. That makes it hard to treat a single individual as a complete description of a species-level strategy, particularly for species that fall closer to the boundary between categories.

In sum, this is a valuable and useful behavioral comparative study with a dataset that many in the field will appreciate. The main conclusions about the likely evolutionary placement of sideways walking are plausible, but several of the stronger claims about discrete locomotor types, the absence of intermediates, and the relationship to diversification would be more convincing if the analysis were less dependent on a fixed angular cutoff and on single individuals per species, or if the manuscript framed those points more cautiously so the conclusions track the strength of the evidence.

Reviewer #1 (Public review):

[Editors' note: this version has been assessed by the Reviewing Editor without further input from the original reviewers. The authors have submitted a second revision, largely to address a comment from Reviewer 2, which was "The failure to model the neural data with an explicit model is a missed opportunity." The authors have now included a computational model.]

This study makes a fundamental contribution to our understanding of interocular suppression, particularly continuous flash suppression (CFS). Using neuroimaging data from two macaque monkeys, the study provides compelling evidence that CFS suppresses orientation responses in neurons within V1. These findings enrich the CFS literature by demonstrating that neural activity under CFS may prevent high-level visual and cognitive processing.

Comments on previous revisions:

The authors have addressed all my previous comments.

Reviewer #1 (Public review):

In this paper, Stanojcic and colleagues attempt to map sites of DNA replication initiation in the genome of the African trypanosome, Trypanosoma brucei. Their approach to this mapping is to isolate 'short-nascent strands' (SNSs), a strategy adopted previously in other eukaryotes (including in the related parasite Leishmania major), which involves isolation of DNA molecules whose termini contain replication-priming RNA. By mapping the isolated and sequenced SNSs to the genome (SNS-seq), the authors suggest that they have identified origins, which they localise to intergenic (strictly, inter-CDS) regions within polycistronic transcription units and suggest display very extensive overlap with previously mapped R-loops in the same loci. Finally, having defined locations of SNS-seq mapping, they suggest they have identified G4 and nucleosome features of origins, again using previously generated data. Though there is merit in applying a new approach to understand DNA replication initiation in T. brucei, where previous work has used MFA-seq and ChIP of a subunit of the Origin Replication Complex (ORC), there are two significant deficiencies in the study that must be addressed to ensure rigour and accuracy.

(i) The suggestion that the SNS-seq data is mapping DNA replication origins that are present in inter-CDS regions of the polycistronic transcription units of T. brucei is novel and does not agree with existing data on the localisation of ORC1/CDC6, and it is very unclear if it agrees with previous mapping of DNA replication by MFA-seq due to the way the authors have presented this correlation. For these reasons, the findings essentially rely on a single experimental approach, which must be further tested to ensure SNS-seq is truly detecting origins. Indeed, in this regard, the very extensive overlap of SNS-seq signal with RNA-DNA hybrids should be tested further to rule out the possibility that the approach is mapping these structures and not origins.

(ii) The authors' presentation of their SNS-seq data is too limited and therefore potentially provides a misleading view of DNA replication in the genome of T. brucei. The work is presented through a narrow focus on SNS-seq signal in the inter-CDS regions within polycistronic transcription units, which constitute only part of the genome, ignoring both the transcription start and stop sites at the ends of the units and the large subtelomeres, which are mainly transcriptionally silent. The authors must present a fuller and more balanced view of SNS-seq mapping, across the whole genome, to ensure full understanding and clarity.

In the revised manuscript, the authors have improved the presentation and analysis of their data, expanding the description of SNS-seq mapping across the genome, and more clearly assessing to what extent there is correlation between SNS-seq signal and previous mapping approaches to predict origins (by MFA-seq and ChiP-chip of ORC1/CDC6). With regard the correlation between SNS-seq and ORC/1CDC6 ChIP-chip, it should be noted that two datasets were generated in distinct strains of T. brucei (Lister 427 and TREU927, respectively), and it is unclear if the latter dataset can be accurately mapped to the strain used here. Notwithstanding this concern, these improvements clarify a number of aspects of the SNS-seq mapping: (1) the signal is more prevalent in the transcribed core of the genome than in the largely transcriptionally silent subtelomeres; and (2) whereas previous work revealed strong correlation between ORC1/CDC6 localisation and MFA-seq peaks at the ends of multigene transcription units, neither of these data show significant overlap with SNS-seq signal, which is not seen at transcription start or stop sites ('SSRs'; supplementary Fig.8D) and shows marked depletion at predicted ORC1/CDC6 sites (supplementary Fig.8C). To the authors' credit, they acknowledge this lack of correlation in the discussion.

The authors have not provided any new data to substantiate their assertion that SNS-seq accurately detects origins in T. brucei, and therefore the work rests on a single experimental approach, without validation. As a result, the suggestion of abundant, previously undetected origins in the intergenic regions of multigene transcription remains a prediction. One key untested limitation of the work lies in the observation that the very large majority of SNS-seq signal overlaps with previously RNA-DNA hybrids; without an experimental test, the suggestion that the authors have 'disclosed for the first time a strong link between RNA:DNA hybrid formation and DNA replication initiation' remains conjecture.

Reviewer #1 (Public review):

Summary:

The manuscript "Adapting Clinical Chemistry Plasma as a Source for Liquid Biopsies" addresses a timely and practical question: whether residual plasma from heparin separator tubes can serve as a source of cfDNA for molecular profiling. This idea is attractive, since such samples are routinely generated in clinical chemistry labs and would represent a vast and accessible resource for liquid biopsy applications. The preliminary results are encouraging, and likely to benefit the research community.

Comments on revisions:

The concerns raised have been addressed. The heparin separator-based cfDNA method described in this study is likely to benefit the research community. I have no further scientific concerns.

Reviewer #1 (Public review):

Summary:

This manuscript investigates the biological mechanism underlying the assembly and transport of the AcrAB-TolC efflux pump complex. By combining endogenous protein purification with cryo-EM analysis, the authors show that the AcrB trimer adopts three distinct conformations simultaneously and identify a previously uncharacterized lipoprotein, YbjP, as a potential additional component of the complex. The work aims to advance our understanding of the AcrAB-TolC efflux system in near-native conditions and may have broader implications for elucidating its physiological mechanism.

Strengths:

Overall, the manuscript is clearly presented, and several of the datasets are of high quality. The use of natively isolated complex is a major strength, as it minimizes artifacts associated with reconstituted systems and enables the discovery of a novel subunit. The authors also distinguish two major assemblies-the TolC-YbjP sub-complex and the complete pump-which appear to correspond to the closed and open channel states, respectively. The conceptual advance is potentially meaningful, and the findings could be of broad interest to the field.

Weaknesses:

(1) As the identification of YbjP is a key contribution of this work, a deeper comparison with functional "anchor" proteins in other efflux pumps is needed. Including an additional supplementary figure illustrating these structural comparisons would be valuable.

(2) The observation of the LTO states in the presence of TolC represents an important extension of previous findings. A more detailed discussion comparing these LTO states to those reported in earlier structural and biochemical studies would improve the clarity and significance of this point.

Comments on revisions:

In the revision, the authors have addressed the above concerns to improve this study.

Reviewer #1 (Public review):

Summary:

Witte et al. examined whether canonical behavioral functions attributed to the cerebellum decline with age. To test this, they recruited younger, old, and older-old adults in a comprehensive battery of tasks previously identified as cerebellar-dependent in the literature. Remarkably, they found that cerebellar function is largely preserved across the lifespan-and in some cases even enhanced. Structural imaging confirmed that their older adult cohort was representative in terms of both cerebellar gray- and white-matter volume. Overall, this is an important study with strong theoretical implications and compelling evidence supporting the motor reserve hypothesis, demonstrating that cerebellar-dependent measures remain largely intact with aging.

Strengths:

(1) Relatively large sample size.

(2) Most comprehensive behavioral battery to date assessing cerebellar-dependent behavior.

(3) Structural MRI confirmation of age-related decline in cerebellar gray and white matter, ensuring representativeness of the sample.

Weaknesses:

The absence of a voxel-based morphometry (VBM) analysis limits the anatomical and functional specificity of the conclusions. Such an analysis would help identify which functions are truly cerebellar-dependent, rather than relying primarily on inferences drawn from prior neuropsychological literature. Notably, the authors have undertaken this analysis in a separate manuscript.

As acknowledged in the Discussion, the classification of tasks as "cerebellar-dependent" versus "general" remains somewhat ambiguous. Some measures labeled as "general" may still engage cerebellar processes. Moreover, analyses in the authors' forthcoming manuscript show weak structure-behavior correlations, casting further doubt on how clearly cerebellar-specific functions can be distinguished from more general processes.

Reviewer #1 (Public review):

This is an important article, which represents the culmination of 25 years of research on the spore coat protein, SafA. Reading this paper is not necessarily easy because it requires time, patience, and attention to detail, but it is truly rewarding. The attentive reader will certainly appreciate the description of a biochemical tour de force, providing convincing experimental evidence for every aspect of a step-by-step inner coat assembly model. It was previously known that SafA was a coat morphogenetic protein responsible for the assembly of the inner layer of the spore coat in Bacillus subtilis, and SafA was already viewed as a hub that directly or indirectly recruited several dozens of coat proteins to the spore envelope. It was also known that there were isoforms of SafA (the most important being the C30 form), and SafA was a substrate of Tgl, a transglutaminase involved in crosslinking some of the coat proteins, especially those found in the inner coat. Several studies have combined genetics and various types of microscopy approaches, including fluorescence microscopy, to decipher the mechanism of coat assembly, but the current study brings top-notch biochemistry into the picture and, therefore, is able to go much further into the molecular characterization of this important mechanism. It should be noted that spore coat assembly is a notoriously difficult process to study biochemically. It was also suspected to be a complex mechanism, because coat assembly is a protracted process involving at least 80 different proteins, whose production is controlled both temporally and spatially, but the current paper manages to connect specific chemical reactions to well-known stages of spore formation. The authors did so by generating several constructs with specific substitutions of Cys and Lys residues, interfering with the completion of disulfide bond formation and crosslinking events, thus determining the order of events and the structural consequences when one of these steps is impaired. Importantly, their conclusions are consistent with previous work. In the updated model, self-assembly of SafA is the first step, promoted by disulfide bond formation between C30 complexes. This is followed by recruitment of inner coat proteins and, finally, transglutamination to stabilize the scaffold structure (referred to as a "spotwelding activity".

The work is extremely thorough. I did not identify any weaknesses and could not think of any experiment that would have been omitted.

Reviewer #1 (Public review):

Summary:

In this manuscript, Frangos at al. used a transcriptomic and proteomic approach to characterise changes in HER2-driven mammary tumours compared to healthy mammary tissue in mice. They observed that mitochondrial genes, including OXPHOS regulators, were among the most down-regulated genes and proteins in their datasets. Surprisingly, these were associated with higher mitochondrial respiration, in response to a variety of carbon sources. In addition, there seems to be a reduction in mitochondrial fusion and an increase in fission in tumour tissues compared to healthy tissues.

Strengths:

The data are clearly presented and described.

The author reported very similar trends in proteomic and transcriptomic data. Such approaches are essential to have a better understanding of the changes in cancer cell metabolism associated with tumorigenesis.

The authors provided a direct link between HER2 inhibition and OXPHOS, strengthening the mechanistic aspect of the work.

Weaknesses:

The manuscript would have benefited from more ex-vivo approaches to further dissect mechanistic links and resolve the contradiction of elevated respiration with reduced expression of most associated proteins (but these points are clearly articulated in the discussion).

The results presented support the authors' conclusions, and limitations are addressed in the discussion. This work will likely impact the progression of the field, and the provided data will benefit the scientific community.

Comments on revisions:

The authors addressed all my concerns.

Reviewer #1 (Public review):

Summary:

The study investigates the role of vascular mural cells, specifically pericytes and vascular smooth muscle cells (vSMCs), in maintaining blood-brain barrier (BBB) integrity and regulating vascular patterning. Analyzing zebrafish pdgfrb mutants that lack brain pericytes and vSMCs, the show that mural cell deficiency does not impair BBB establishment or maintenance during larval and early juvenile stages. However mural cells seem to be crucial for preventing vascular aneurysms and hemorrhage in adulthood as focal leakage, basement membrane disruption and increased caveolae formation are observed in adult zebrafish at aneurysm hotspots. The authors challenge the paradigm that mural cells are essential for BBB regulation in early development while highlighting their importance for long-term vascular stability.

Strengths:

Previous studies have established that the zebrafish BBB shares molecular and morphological homology with e.g. the mammalian BBB and therefore represents a suitable model. By examining mural cell roles across different life stages-from larval to adult zebrafish-the study provides an unprecedented comprehensive developmental analysis of brain vascular development and of how mural cells influence BBB integrity and vascular stability over time. The use of live imaging, whole-brain clearing, and electron microscopy offers high-resolution insights into cerebrovascular patterning, aneurysm development, and structural changes in endothelial cells and basement membranes. By analyzing "leakage hotspots" and their association with structural endothelial defects in adults the presented findings add novel insights into how mural cell loss may lead to vascular instability.

Reviewer #3 (Public review):

This manuscript provides novel insights into altered glucose metabolism and KC status during early MASLD. The authors propose that hyperactivated glycolysis drives a spatially patterned KC depletion that is more pronounced than the loss of hepatocytes or hepatic stellate cells. This concept significantly enhances our understanding of early MASLD progression and KC metabolic phenotype.

Through a combination of TUNEL staining and MS-based metabolomic analyses of KCs from HFHC-fed mice, the authors show increased KC apoptosis alongside dysregulation of glycolysis and the pentose phosphate pathway. Using in vitro culture systems and KC-specific ablation of Chil1, a regulator of glycolytic flux, they further show that elevated glycolysis can promote KC apoptosis.

However, it remains unclear whether the observed metabolic dysregulation directly causes KC death or whether secondary factors, such as low-grade inflammation or macrophage activation, also contribute significantly. Nonetheless, the results, particularly those derived from the Chil1-ablated model, point to a new potential target for the early prevention of KC death during MASLD progression.

The manuscript is clearly written and thoughtfully addresses key limitations in the field, especially the focus on glycolytic intermediates rather than fatty acid oxidation. The authors acknowledge the missing mechanistic link between increased glycolysis and KC death. A few things require clarification.

Strengths:

• The study presents the novel observation of profound metabolic dysregulation in KCs during early MASLD and identifies these cells as undergoing apoptosis. The finding that Chil1 ablation aggravates this phenotype opens new avenues for exploring therapeutic strategies to mitigate or reverse MASLD progression.

• The authors provide a comprehensive metabolic profile of KCs following HFHC diet exposure, including quantification of individual metabolites. They further delineate alterations in glycolysis and the pentose phosphate pathway in Chil1-deficient cells, substantiating enhanced glycolytic flux through 13C-glucose tracing experiments.

• The data underscore the critical importance of maintaining balanced glucose metabolism in both in vitro and in vivo contexts to prevent KC apoptosis, emphasizing the high metabolic specialization of these cells.

• The observed increase in KC death in Chil1-deficient KCs demonstrates their dependence on tightly regulated glycolysis, particularly under pathological conditions such as early MASLD.

Weaknesses:

• The TUNEL staining in the overview in Figure 2 is not convincing. Typically the signal overlaps with DAPI, which is mostly not the case in the figures shown.

• The mechanistic link between elevated glycolytic flux and KC death remains unclear.

• Figure S5: shows deltadelta CT values, not relative values. What are the housekeeping genes? There should be at least 2, and they should not have metabolically related functions such as Gapdh.

• Figure 1C: shows WT and KO gating side by side

• The following point has not been answered: "While BMDMs from Chil1 knockout mice are used to demonstrate enhanced glycolytic flux, it remains unclear whether Chil1 deficiency affects macrophage differentiation itself." Expression of certain genes that indicate function does not show whether BMDMs isolated from these KO mice are fully differentiated. Here, counting BM input/ BMDM output, flow cytometry on BMDMs, morphology etc. should be tested.

Reviewer #1 (Public review):

In this manuscript, the authors aimed to identify the molecular target and mechanism by which α-Mangostin, a xanthone from Garcinia mangostana, produces vasorelaxation that could explain the antihypertensive effects. Building on on prior reports of vascular relaxation and ion channel modulation, the authors convincingly show that large-conductance potassium BK channels are the primary site of action. Using electrophysiological, pharmacological, and computational evidence, the authors achieved their aims and showed that BK channels are the critical molecular determinant of mangostin's vasodiltory effects, even though the vascular studies are quite preliminary in nature.

Strengths:

(1) The broad pharmacological profiling of mangostin across potassium channel families, revealing BK channels - and the vascular BK-alpha/beta1 complex - as the potently activated target in a concentration-dependent manner.

(2) Detailed gating analyses showing large negative shifts in voltage-dependence of activation and altered activation and deactivation kinetics.

(3) High-quality single-channel recordings for open probability and dwell times.

(4) Convincing activation in reconstituted BKα/β1-Caᵥ nanodomains mimicking physiological condition and functional proof-of-concept validation in mouse aortic rings.

Weaknesses are minor:

(1) Some mutagenesis data (e.g., partial loss at L312A) could benefit from complementary structural validation.

The author's rebuttal provides alphafold3 models for mutants. While there are interesting preliminary observations, the authors decided not to include these in the main manuscript, awaiting further structual validation. I concur.

(2) While Cav-BK nanodomains were reconstituted, direct measurement of calcium signals after mangostin application onto native smooth muscle could be valuable.

In their response, the authors acknowledge the importance of measuring Ca2+ sparks in smooth muscle cells to further validate their findings. However, this is not provided in the manuscript. Part of my earlier comment alludes to the possibility of α-Mangostin directly affecting Cav1.2 or ryanodine receptor activity, and therefore BK activity would go up. With the current provided evidence, these possibilities cannot be excluded and need to be acknowledged.

(3) The work has impact for ion channel physiology and pharmacology, providing a mechanistic link between a natural product and vasodilation. Datasets include electrophysiology traces, mutagenesis scans, docking analyses, and aortic tension recordings. The latter however are preliminary in nature.

The authors acknowledge that additional vascular physiology experiments would strengthen the argument they make. They are however unable to provide such evidence in the present manuscript. Therefore, I strongly suggest that the authors tune down the physiological implications of α-Mangostin that they include in the manuscript. I'd also suggest that "vasorelaxation" is removed from the manuscript title, given the preliminary nature of the findings.

Reviewer #1 (Public review):

Summary:

The authors introduce ImPaqT, a modular toolkit for zebrafish transgenesis, utilizing the Golden Gate cloning approach with the rare-cutting enzyme PaqCI. The toolkit is designed to streamline the construction of transgenes with broad applications, particularly for immunological studies. By providing a versatile platform, the study aims to address limitations in generating plasmids for zebrafish transgenesis.

Strengths:

The ImPaqT toolkit offers a modular method for constructing transgenes tailored to specific research needs. By employing Golden Gate cloning, the system simplifies the assembly process, allowing seamless integration of multiple genetic elements while maintaining scalability for complex designs. The toolkit's utility is evident from its inclusion of a diverse range of promoters, genetic tools, and fluorescent markers, which cater to both immunological and general zebrafish research needs. Even small DNA fragements, such as the viral 2a sequence, can be cloned into a multi-component plasmid in one step. The components can be assembled from PCR fragments or synthesized DNA fragments, forgoing the need for "entry" vectors. Further, the authors show that the exisiting PaqCI sites can be domesticated to improve the versatility of the system. The validation provided in the manuscript is Convincing, demonstrating the successful generation of several functional transgenic lines. These examples highlight the toolkit's efficacy, particularly for immune-focused applications.

Comments on revisions:

The authors have addressed all the concerns raised in the first review. Congratulations to the authors for their effort.

Reviewer #1 (Public review):

Summary:

For each of three key transcription factor (TF) proteins in E. coli, the authors generate a large library of TF binding site (TFBS) sequences on plasmids, such that each TFBS is coupled to the expression of a fluorescence reporter. By sorting the fluorescence of individual cells and sequencing their plasmids to identify each cell's TFBS sequence (sort-seq), they are able to map the landscape of these TFBSs to the gene expression level they regulate. The authors then study the topographical features of these landscapes, especially the number and distribution of local maxima, as well as the statistical properties of evolutionary paths on these landscapes. They find the landscapes to be highly rugged, with about as many local peaks as a random landscape would have, and with those peaks distributed approximately randomly in sequence space. This is quite different from previous work on landscapes for eukaryotic TFBSs, which tend to be rather smooth. The authors find that there are a number of peaks that produce regulation stronger than that of the wild-type sequence for each TF, and that it is not too unlikely to reach one of those "high peaks" from a random starting sequence. Nevertheless, the basins of attraction for different peaks have significant overlap, which means that chance plays a major role in determining which peak a population will evolve to.

Strengths:

(1) The apparent differences in landscape topography between prokaryotic TFBSs and other molecular landscapes is a fascinating discovery to add to the field of genotype-phenotype maps. I am really excited to learn the molecular mechanisms of this in the future.

(2) The experiments and analysis of this paper are very well-executed and, by and large, very thorough. I appreciated the systematic nature of the project, both the large-scale experiments done on three TFs with replicates, and the systematic analysis of the resulting landscapes. This not only makes the paper easy to follow, but also inspires confidence in their results since there is so much data and so many different ways of analyzing it. It's a great recipe for other studies of genotype-phenotype landscapes to follow.

(3) Considering how technical the project was, I am really impressed at how easy to read I found the paper, and the authors deserve a lot of credit for making it so. They do a great job of building up the experiments and analyses step-by-step, and explaining enough of the basics of the experimental design and essence of each analysis in the main text without getting too complicated with details that can be left to the Methods or SI.

Weaknesses:

(1) Regarding the effect of measurement uncertainties, one way in which they attempt to test their effect is to simulate dynamics on noisy and noise-free versions of the landscape and measure visitation frequencies. While they show that visitation frequencies are highly correlated between these cases, I'd prefer a more direct test of epistasis or navigability (e..g, number of local peaks), since that's how they are characterizing the landscapes, and the connection between that and visitation frequency of individual states is unclear.

(2) I am still a little concerned about the fraction of sequences missing from the data due to filtering, although I appreciate the difficulties in testing the importance of this (requiring additional assumptions) and the authors' good-faith efforts to do their best with the data they have.

Reviewer #1 (Public review):

The work presented by Cheung et al. used a quantitative proteomics method to capture molecular changes in B cells exposed to LPS and IL-4, a combination of stimuli activating naive B cells. Amino acid transporters, cholesterol biosynthetic enzymes, ribosomal components, and other proteins involved in cell proliferation were found to increase in stimulated B cells. Experiments involving genetic loss-of-function (SLC7A5), pharmacological inhibition (HMGCR, SQLE, prenylation), and functional rescue by metabolites (mevalonate, GGPP) validated the proteomics data and revealed that amino acid uptake, cholesterol/mevalonate biosynthesis, and cholesterol uptake played a crucial role in B cell proliferation, survival, biogenesis, and immunoglobulin class switching. Experiments involving cholesterol-free medium showed that both biosynthesis and LDLR-mediated uptake catered to the cholesterol demand of LPS/IL-4-stimulated B cells. A role for protein prenylation in LDLR-mediated cholesterol uptake was postulated and backed by divergent effects of GGPP rescue in the presence and absence of cholesterol in culture medium.

Strengths:

The discovery was made by proteome-wide profiling and unbiased computational analysis. The discovered proteins were functionally validated using appropriate tools and approaches. The metabolic processes identified and prioritized from this comprehensive survey and systematic validation highly likely represent mechanisms of high importance and influence. Analysis of immune cell metabolism at the protein level is relatively compared to transcriptomic and metabolomic analysis.

The conclusions from functional validation experiments were supported by clear data and based on rational interpretations. This was enabled by well-established readouts/analytical methods used to determine cell proliferation, viability, size, cholesterol content, and transporter/enzyme function. The data generated from these experiments strongly support the conclusions.

This work reveals a complex, yet intriguing, relationship between cholesterol metabolism and protein prenylation as they serve to promote B cell activation. The effects of pharmacological inhibition and metabolite replenishment on the cholesterol content and activation of B cells were determined and logically interpreted.

Weaknesses:

The findings of this study were obtained almost exclusively from ex vivo B cell stimulation experiments. Their contribution to B cell state and B cell-mediated immune responses in vivo was not explored. Without in vivo data, the study still provides valuable mechanistic information and insights, but it remains unknown, and there is no discussion about, how the identified mechanisms may play out in B cell immunity.

The role of HMGCR, SQLE, and prenylation in B cell activation was assessed using pharmacological inhibitors. Evidence from other loss-of-function approaches, which could strengthen the conclusions, does not exist. This is a moderate weakness and somewhat offset by other data, including those obtained from the tests involving multiple distinct pharmacological inhibitors and the metabolite replenishment experiments.

Reviewer #1 (Public review):

Summary:

Adult laboratory mice produce ultrasonic vocalizations during free social interactions, as well as lower-frequency, voiced calls (squeaks) during aversive contexts. The question of whether mice possess a more complex repertoire of vocalizations has been of great interest to scientists studying rodent vocal behavior. In the current study, the authors analyze the rates and acoustic features of vocalizations produced by pairs of mice that are allowed to interact across a barrier, which prevents direct physical interaction. In this context, they find that same-sex (but not opposite-sex) pairs of mice produce vocalizations that are lower in frequency than the typical 70 kHz ultrasonic vocalizations produced during free interactions and that are also distinct from squeaks. These lower frequency vocalizations were observed in both male-male and female-female pairs, as well as in same-sex pairs from multiple mouse strains. The authors also report that call rates and acoustic features are not affected in male-male pairs that have been treated with the anxiolytic drug buspirone, suggesting that anxiety is not a major driver of vocalization in this behavioral context.

Strengths:

(1) The observation that same-sex pairs of mice produce lower frequency (<70 kHz) vocalizations in this behavioral context is novel.

(2) The consideration of multiple types of pairs (female-female, male-male, and female-male), as well as the inclusion of multiple strains of mice and barriers with different hole diameters, are all strengths of the study.

(3) The authors include detailed analyses of vocalization acoustic features, as well as detailed tracking of mouse positions relative to the barrier.

Weaknesses:

The categorization applied to vocalizations based on their mean frequencies is poorly supported and ignores the distinction in laryngeal production mechanism between voiced and ultrasonic vocalizations. Specifically, the authors are likely lumping together voiced and ultrasonic vocalizations into their "low frequency" (< 30 kHz) category, while they reserve the term "ultrasonic" exclusively for the subset of ultrasonic vocalizations with the highest mean frequencies (> 50 kHz). This categorization scheme also does not align well with past work on lower frequency rodent vocalizations, which complicates the comparison of the present findings to that past work.

In some analyses, the authors report that different groups of mice produce different relative proportions of vocalization types (as defined by mean frequency) but then compare acoustic features of vocalizations between groups after pooling all vocalizations together. The analyses of acoustic features conducted in this way may be confounded by the different proportions of vocalization types across groups.

Reviewer #1 (Public review):

Summary:

The authors aimed to uncover novel therapeutic vulnerabilities in APC-mutant colorectal cancer (CRC), which constitutes the majority of CRC cases. They hypothesized that modulating oxygen-sensing pathways (via PHD inhibition) could disrupt adaptive stress responses in these tumours.

Strengths:

The study employs a powerful, two-pronged approach to identify Molidustat's targets. By using both Thermal Proteome Profiling (TPP) and an orthogonal chemical proteomic competition assay, the authors provide compelling evidence that GSTP1 is a genuine, direct off-target, effectively addressing the common limitation of indirect effects in proteomic screens.

Weaknesses:

(1) In Figure 1, the current data rely on a single guide RNA (sgRNA). To make the data solid, at least two independent sgRNAs targeting different regions of PHD2 should be used.

(2) Figure 3E: Asn205 site should be mutated to prove that whether Molidustat inhibits GSTP1 activity via Asn205 or not.

(3) Figure 5B and 5C: The metabolic imbalance phenotype observed upon dual knockout of PHD2 and GSTP1 requires rescue experiments to confirm on-target specificity.

Reviewer #1 (Public review):

Summary:

The study examines human biases in a regime-change task, in which participants have to report the probability of a regime change in the face of noisy data. The behavioral results indicate that humans display systematic biases, in particular, overreaction in stable but noisy environments and underreaction in volatile settings with more certain signals. fMRI results suggest that a frontoparietal brain network is selectively involved in representing subjective sensitivity to noise, while the vmPFC selectively represents sensitivity to the rate of change.

Strengths:

- The study relies on a task that measures regime-change detection primarily based on descriptive information about the noisiness and rate of change. This distinguishes the study from prior work using reversal-learning or change-point tasks in which participants are required to learn these parameters from experiences. The authors discuss these differences comprehensively.

- The study uses a simple Bayes-optimal model combined with model fitting, which seems to describe the data well. The model is comprehensively validated.

- The authors apply model-based fMRI analyses that provide a close link to behavioral results, offering an elegant way to examine individual biases.

Weaknesses:

The authors have adequately addressed my prior concerns.

Reviewer #3 (Public review):

Summary

In this manuscript, Zhang et al. investigate the conduction and inhibition mechanisms of the Kv2.1 channel, with a particular focus on the distinct effects of TEA and RY785 on Kv2 potassium channels. Using microsecond-scale molecular dynamics simulations, the authors characterize K⁺ ion permeation and RY785-mediated inhibition within the central pore. Their results reveal an inhibition mechanism that differs from those described for other Kv channel inhibitors.

Strengths

The study identifies a distinctive inhibitory mode for RY785, which binds along the channel walls in the open-state structure while still permitting a reduced level of K⁺ conduction. In addition, the authors propose a long-range allosteric coupling between RY785 binding in the central pore and changes in the structural dynamics of Kv2.1. Overall, this is a well-organized and carefully executed study, employing robust simulation and analysis methodologies. The work provides novel mechanistic insights into voltage-gated potassium channel inhibition and may offer useful guidance for future structure-based drug design efforts.

Weaknesses:

As noted in the Discussion, this study focuses primarily on the major binding site within the central pore and was not designed to systematically assess other potential allosteric binding sites for RY785. A more comprehensive structural and biophysical evaluation of possible additional binding sites would be a valuable direction for future investigations.

Comments on revisions:

The authors have addressed my comments.

Reviewer #1 (Public review):

Summary:

In many vertebrates, the neural tube closes by folding, elevation, and fusion of bilateral neural folds. Loss of the actin-binding protein Vinculin causes failed cranial neural tube closure in mice and is associated with neural tube defects in human patients, but it was not known how Vinculin contributes to neural tube closure. Here, Prudhomme and colleagues find that neural fold elevation and the apical constriction that drives it initiate normally in Vinculin-deficient mouse embryos, but both arrest before the neural folds fuse. The time of failure coincides with increased mechanical tension within the cranial neural plate. They find that Vinculin localizes to areas of high mechanical stress in the WT neural plate, including multi-cellular junctions and dividing cells, and in the absence of Vinculin, recruitment of Myosin and Apical junction proteins is reduced at these sites. These data support a model in which Vinculin recruits junctional proteins to high-stress areas to maintain junctional integrity during neural tube closure.

Strengths:

The data presented are thorough, rigorous, and convincing. The combination of live imaging and transgenic fluorescent reporters enables direct observation of junctional behaviors within the mouse cranial neural plate and detailed analysis of how these behaviors are disrupted upon loss of Vinculin. The authors make good use of an ESC transplant approach to efficiently generate mutant and transgenic embryos for analysis.

Weaknesses:

Although the loss of junctional integrity, especially at multi-cellular junctions, is clearly and convincingly demonstrated in Vinculin-deficient embryos, it is not clear precisely how this disrupts the elevation of the neural folds to cause exencephaly.

Reviewer #1 (Public review):

Summary:

Using electron microscopy, the authors report discontinuities in the plasma membrane of C. elegans embryos. They associate these discontinuities with cell division and speculate that membrane rupture and subsequent resealing contribute to cytokinesis. They further discuss the proximity of these sites to vesicles and propose a role for vesicle-mediated membrane extension.

Weaknesses:

(1) The possibility that the membrane discontinuity is an artifact

Although the authors focus on discontinuities in the plasma membrane, similar discontinuities are also observed in mitochondria, the nuclear envelope, and yolk granules. This raises concerns about whether the electron micrographs presented are suitable for assessing membrane continuity.

Electron micrographs result from a lengthy sample preparation process, including high-pressure freezing, freeze substitution in acetone containing OsO4, gradual warming, uranyl acetate staining, resin embedding, and ultrathin sectioning. In general, lipids are soluble in acetone at temperatures above −30 {degree sign}C, and preservation of membrane structures relies heavily on efficient OsO4 fixation. Insufficient OsO4 treatment would be expected to reduce membrane contrast.

C. elegans embryos are encapsulated by an eggshell that forms at fertilization and gradually develops during the first few cell divisions. It is unclear how efficiently OsO4 in acetone penetrates the eggshell during freeze substitution, raising further concern about plasma membrane preservation under the conditions used.

(2) Lack of evidence linking membrane discontinuity to cell division

The reported plasma membrane discontinuities are not specific to mitotic cells. If this were a physiological process playing an important role in cytokinesis, it should occur in a temporally and spatially coordinated manner with nuclear division. However, it remains unclear at what stage of the cell cycle the membrane rupture occurs and where it is located relative to chromosomes and the mitotic spindle.

(3) Lack of evidence for extension of the separated membrane

Although the authors speculate that resealing of the ruptured membrane occurs via extension of the separated membrane, no direct evidence supporting this mechanism is presented. Proximity to vesicles alone does not demonstrate that membrane extension occurs through vesicle fusion. More direct evidence is required to support this claim.

(4) Inconsistency with published work

Numerous studies have examined cell division in developing C. elegans embryos using the GFP::PH(PLC1δ1) marker expressed from the ltIs38 transgene [pAA1; pie-1::GFP::PH(PLC1δ1) + unc-119(+)], generated by the Oegema lab (https://wormbase.org/species/c_elegans/transgene/WBTransgene00000911#01--10 ). To date, no study has reported membrane ruptures of the magnitude described here. The complexity of cell surface morphology from the 8- to 12-cell stages onward has been well documented, for example, by Fu et al. (2016) using light-sheet microscopy and 3D reconstruction (doi:10.1038/ncomms11088).

Supplementary Movies 5, 6, and 10 of this paper illustrate how single-plane images can easily produce apparent membrane discontinuities, for example, due to membrane orientations nearly parallel to the imaging plane.

The three single-plane images from only three embryos presented in Figure 6 are insufficient to support the authors' strong conclusions. Raw 3D data should be provided.

Reviewer #1 (Public review):

[Editors' note: This version has been assessed by the Reviewing Editor without further input from the original reviewers. The authors have addressed the comments raised in the previous round of review.]

Summary:

In their paper entitled "Alpha-Band Phase Modulates Perceptual Sensitivity by Changing Internal Noise and Sensory Tuning," Pilipenko et al. investigate how pre-stimulus alpha phase influences near-threshold visual perception. The authors aim to clarify whether alpha phase primarily shifts the criterion, multiplicatively amplifies signals, or changes the effective variance and tuning of sensory evidence. Six observers completed many thousands of trials in a double-pass Gabor-in-noise detection task while an EEG was recorded. The authors combine signal detection theory, phase-resolved analyses, and reverse correlation to test mechanistic predictions. The experimental design and analysis pipeline provide a clear conceptual scaffold, with SDT-based schematic models that make the empirical results accessible even for readers who are not specialists in classification-image methods.

Strengths:

The study presents a coherent and well-executed investigation with several notable strengths. First, the main behavioral and EEG results in Figure 2 demonstrate robust pre-stimulus coupling between alpha phase and d′ across a substantial portion of the pre-stimulus interval, with little evidence that the criterion is modulated to a comparable extent. The inverse phasic relationship between hit and false-alarm rates maps clearly onto the variance-reduction account, and the response-consistency analysis offers an intuitive behavioral complement: when two identical stimuli are both presented at the participant's optimal phase, responses are more consistent than when one or both occur at suboptimal phases. The frontal-occipital phase-difference result suggests a coordinated rather than purely local phase mechanism, supporting the central claim that alpha phase is linked to changes in sensitivity that behave like changes in internal variability rather than simple gain or criterion shifts. Supplementary analyses showing that alpha power has only a limited relationship with d′ and confidence reassure readers that the main effects are genuinely phase-linked rather than a recasting of amplitude differences.

Second, the reverse-correlation results in Figure 3 extend this story in a satisfying way. The classification images and their Gaussian fits show that at the optimal phase, the weighting of stimulus energy is more sharply concentrated around target-relevant spatial frequencies and orientations, and the bootstrapped parameter distributions indicate that the suboptimal phase is best described by broader tuning and a modest change in gain rather than a pure criterion account. The authors' interpretation that optimal-phase perception reflects both reduced effective internal noise and sharpened sensory tuning is reasonable and well-supported. Overall, the data and figures largely achieve the stated aims, and the work is likely to have an impact both by clarifying the interpretation of alpha-phase effects and by illustrating a useful analytic framework that other groups can adopt.

Reviewer #1 (Public review):

Summary:

In the manuscript "Heat Shock Factor Regulation of Antimicrobial Peptides Expression Suggests a Conserved Defense Mechanism Induced by Febrile Temperature in Arthropods," Xiao and colleagues examine the role of the shrimp Litopenaeus vannamei HSF1 ortholog (LvHSF1) in the response to viral infection. The authors provide compelling support for their conclusions that the activation of LvHSF1 limits viral load at high temperatures. Specifically, the authors convincingly show that (i) LvHSF1 mRNA and protein are induced in response to viral infection at high temperatures, (ii) increased LvHSF1 levels can directly induce the expression of the nSWD (and directly or indirectly other antibacterial peptides, AMPs), (ii) nSWD's antimicrobial activities can limit viral load, and, (iv) LvHSF1 protects survival at high temperatures following virus infection. These data thus provide a model by which an increase in HSF1 levels limits viral load through the transcription of antimicrobial peptides, and provide a rationale for the febrile response as a conserved response to viral infection.

Strengths:

The large body of careful time series experiments, tissue profiling, and validation of RNA-seq data is convincing. Several experimental methodologies are used to support the author's conclusions that nSWD is an LvHSf1 target and increased LvHSF1 alone can explain increased levels of nSWD. Similar carefully conducted experiments also conclusively implicate nSWD protein in limiting WSSV viral loads.

Weaknesses:

As with any complex biological phenomenon, several aspects remain incompletely explained. Nevertheless, in their revision, the authors provide additional analyses supporting the authors model that losing LvHSF1 is not detrimental to survival, by more directly altering viral loads. In addition, their revised manuscript clarifies the complex interactions between infection, the role of HSF1, and hormesis. These revisions increase the impact of their findings.

Comments on revisions:

The authors have addressed all comments, and the manuscript is very much improved.

Reviewer #1 (Public review):

[Editors' note: this version has been assessed by the Reviewing Editor without further input from the original reviewers. The authors have addressed the comments raised in the previous round of review.]

Summary:

This study provided key experimental evidence for the "Solstice-as-Phenology-Switch Hypothesis" through two temperature manipulation experiments.

Strengths:

The research is data-rich, particularly in exploring the effects of pre- and post-solstice cooling, as well as daytime versus nighttime cooling, on bud set timing, showcasing significant innovation. The article is well-written, logically clear, and is likely to attract a wide readership.

Reviewer #1 (Public review):

Summary:

The authors use a gambling task with momentary mood ratings from Rutledge et al. and compare computational models of choice and mood to identify markers of decisional and affective impairments underlying risk-prone behavior in adolescents with suicidal thoughts and behaviors (STB). The results show that adolescents with STB show enhanced gambling behavior (choosing the gamble rather than the sure amount), and this is driven by a bias towards the largest possible win rather than insensitivity to possible losses. Moreover, this group shows a diminished effect of receiving a certain reward (in the non-gambling trials) on mood. The results were replicated in a general online sample where participants were divided into groups with or without STB based on their self-report of suicidal ideation on one question in the Beck Depression Inventory self-report instrument. The authors suggest, therefore, that adolescents diagnosed with depression or anxiety with decreased sensitivity to certain rewards may need to be monitored more closely for STB due to their increased propensity to take risky decisions aimed at (expected) gains (such as relief from an unbearable situation through suicide) regardless of the potential losses. However, such a result was only found in the clinical sample and cannot be generalized more broadly based on the current findings.

Strengths:

(1) The study uses a previously validated task design and replicates previously found results through well-explained model-free and model-based analyses.

(2) Sampling of adolescents at high risk can help target early preventative diagnoses and treatments for suicide.

(3) Replication of the results in an online cohort increases confidence in the findings.

(4) The models considered for comparison are thorough and well-motivated. The chosen models allow for teasing apart which decision and mood sensitivity parameters relate to risky decision-making across groups based on their hypotheses.

(5) Novel finding of mood (in)sensitivity to non-risky rewards and its relationship with risk behavior in STB.

Weaknesses:

(1) Sample size of 25 for S- group is low-powered, which is explicitly mentioned as a study limitation.

(2) Modeling in the mediation analysis focused on predicting risk behavior in this task from the model-derived bias for gains and suicidal symptom scores. Thus, the implications of this work are more relevant to a basic-science understanding of the etiology of suicidal behavior than they are useful as a predictor of suicidal behavior, and it is not clear that a psychiatrist or psychologist could use this task to potentially determine who is at higher risk of attempting suicide and must be more closely monitored. Indeed, relationships between task parameters and behavior and suicidal behavior was limited to the clinical sample with a diagnosis of depression or anxiety disorder, and did not extend to the online sample. Therefore, the claim that these findings provide "computational markers for general suicidal tendency among adolescents" is unwarranted.

Reviewer #1 (Public review):

Summary

From transcriptomic comparisons of adult mouse cochlear and vestibular hair cells, Xu et al. provide a broad and well-organized overview of differences across 4 established hair cell types (2 cochlear and 2 vestibular). They go on to demonstrate the power of such analyses to provide functional insights by focusing on the differentiated expression of ciliary genes, building to the hypothesis that kinociliary motility occurs in adult vestibular hair cells.

Background

Cilia are prominent in sensory receptors, including vertebrate photoreceptors, olfactory neurons and mechanosensitive hair cells of the inner ear and lateral line. Cilia can be motile or nonmotile depending on their axonemal structure: motile cilia require dynein and the inner 2 singlet microtubules of the 9+2 array. Primary cilia, present early in development, are considered to have sensory functions and to be nonmotile (Mill et al., Nature Rev Gen 2023).

In hair cells, the kinocilium anchors and polarizes the mechanosensitive hair bundle of specialized microvilli. The kinocilium matures from the primary cilium of a newborn hair cell; behind it the bundle of mechanosensory microvilli rises in a descending staircase of rows. During maturation of the mammalian cochlea, all hair cells lose the kinocilium, though not the associated basal body. The consensus for many years has been that most vertebrate kinocilia, and especially mammalian kinocilia, are nonmotile, based largely on the lack of spontaneous motility in excised mammalian vestibular organs, but also on the impression that the rare examples of spontaneous beating motility even in non-mammalian hair cells are associated with deterioration of the preparation (Rüsch & Thurm 1990).

Strengths

In comparing RNA expression across the 4 major types of mouse hair cells - 2 cochlear and 2 vestibular - Xu et al. provide rich data sets for exploration of structure-function differences between these highly specialized cell types. The revised paper significantly improves the organization, interpretation and readability of the presentation of overall findings. smFISH and immuno-staining back up key RNA data, and comparisons are made with published data.

The ciliary motility focus of the rest of the paper is creative and highly interesting. The authors curated the ciliary genes into types associated with different aspects of beating motility, and also investigated the expression of genes typical of primary cilia, which are considered to have sensory and cell signaling functions and to be nonmotile. Their data justify suggesting a role for kinociliary motility (or force generation) in adult mammalian vestibular hair cells, in opposition to a long-held assumption. The results should stimulate investigation of the implications for mechanosensitivity.

Weaknesses

Data

Functional data on kinocilia motility: The technical difficulty in making such measurements in small mouse hair bundles led the authors to work with bullfrog crista bundles. Though not extensively studied here, the ciliary motility shown is convincing. Mouse hair bundle motions are also shown but the evidence connecting the data to kinociliary motion are more suggestive than convincing. But the authors are not dogmatic about these data, and it is reasonable to show them.

Interpretation

The authors take the view that kinociliary motility is likely to be normally present but is rare in their observations because conditions are not right. But while others have described some (rare) kinociliary motility in fish organs (Rusch & Thurm 1990), they interpreted its occurrence as a sign of pathology. Indeed, in this paper, it is not clear what role kinociliary motility would play in mature hair bundles. The authors have added a discussion of this question in the revision.

An underlying rationale for the hypothesis that ciliary motility manifests in mammalian vestibular hair cells seems to rest on the presence of the necessary mRNA and its contrasting absence in cochlear hair cells. Another way to look at this difference could be that evolution acted on cochlear hair cells to shed kinocilia as one of many changes to improve mechanosensitivity at much higher sound frequencies. In vestibular hair cells, kinociliary motion might be useful to enhance mechanostimulation in the developing vestibule (as suggested in this revision) and not so active in maturity. Nevertheless, with their scholarly analysis of the expression of ciliary genes, the authors make a significant argument for further investigation of when and why hair cell kinocilia show active motility.

Reviewer #1 (Public review):

This revised manuscript by Qin and colleagues delineates an important neural mechanism that suppresses the intake of sugar solution in response to internal glucose level (the "brake" mechanism for sugar consumption). They identified a three-step neuropeptidergic system that downregulates the sensitivity of sweet-sensing gustatory sensory neurons, primarily in response to elevated level of circulating glucose. First, neurons that release a neuropeptide Hugin (which is an insect homolog of vertebrate Neuromedin U (NMU)) are activated by a high concentration of hemolymph glucose, which is directly sensed by Hugin-releasing neurons in a cell-autonomous mechanism. Next, Hugin neuropeptides activate Allatostatin A (AstA)-releasing neurons via one of Hugin receptors, PK2-R1. Finally, the released AstA neuropeptide suppresses sugar response in sweet-sensing Gr5a-expressing gustatory sensory neurons through the AstA-R1 receptor. Suppression of sugar response in Gr5a-expressing neurons reduces fly's sugar intake motivation. They also found that NMU-expressing neurons in the ventromedial hypothalamus (VMH) of mice (which project to the rostal nucleus of the solitary tract (rNST)) are also activated by high concentration of circulating glucose, independent of synaptic transmission, and that injection of NMU reduces the glucose-induced activity in the downstream of NMU-expressing neurons in rNST. These data suggest that the function of Hugin neuropeptides in the fly is analogous to the function of NMU in the mouse.

The authors have provided multiple lines of compelling evidence generated through rigorous and comprehensive experiments, which spans genetic abrogation, neuronal manipulation, pharmacology, and functional imaging. The authors are also receptive to the critiques and reframed the central message, such that their conclusions are soundly supported by the presented data. Importantly, the parallel study in mice adds a unique comparative perspective that makes the paper of interest to a wide range of readers.

Reviewer #2 (Public review):

Summary:

The authors goals is to be develop a more accurate system that reports TDP-43 activity as a splicing regulator. Prior to this, most methods employed western blotting or QPCR based assays to determine whether targets of TDP-43 were up or down regulated. The problem with that is the sensitivity. This approach uses an ectopic delivered construct containing splicing elements from CFTR and UNC13A (two known splicing targets) fused to a GFP reporter. Not only does it report TDP-43 function well, but it operates at extremely sensitive TDP-43 levels, requiring only picomolar TDP-43 knockdown for detection. This reporter should supersede the use of current TDP-43 activity assays, its cost-effective, its rapid and reliable.

Strengths:

In general, the experiments are convincing and well designed. The rigor, number of samples and statistics, and gradient of TDP-43 knockdown were all viewed as strengths. In addition, the use of multiple assays to confirm the splicing changes were viewed as complimentary (ie PCR and GFP-fluorescence) adding additional rigor. The final major strength i'll add is the very clever approach to tether TDP-43 to the loss of function cassette such that when TDP-43 is inactive it would autoregulate and induce wild-type TDP-43. This has many implications for the use of other genes, not just TDP-43, but also other protective factors that may need to be re-established upon TDP-43 loss of function.

Weaknesses:

Admittedly, one needs to initially characterize the sensor and the use of cell lines is an obvious advantage, but it begs the question of whether this will work in neurons. Additional future experiments in primary neurons will be needed. The bulk analysis of GFP-positive cells is a bit crude. As mentioned in the manuscript, flow sorting would be an easy and obvious approach to get more accurate homogenous data. This is especially relevant since the GFP signal is quite heterogenous in the image panels, for example Figure 1C, meaning the siRNA is not fully penetrant. Therefore, stating that 1% TDP-43 knockdown achieves the desired sensor regulation might be misleading. Flow sorting would provide a much more accurate quantification of how subtle changes in TDP-43 protein levels track with GFP fluorescence.

Some panels in the manuscript would benefit from additional clarity to make the data easier to visualize. For example, Figure 2D and 2G could be presented in a more clear manner, possibly split into additional graphs since there are too many outputs. Sup Figure 2A image panels would benefit from being labeled, its difficult to tell what antibodies or fluorophores were used. Same with Figure 4B.

Figure 3 is an important addition to this manuscript and in general is convincing showing that TDP-43 loss of function mutants can alter the sensor. However, there is still wild-type endogenous TDP-43 in these cells, and its unclear whether the 5FL mutant is acting as a dominant negative to deplete the total TDP-43 pool, which is what the data would suggest. This could have been clarified. Additional treatment with stressors that inactivate TDP-43 could be tested in future studies.

Overall, the authors definitely achieved their goals by developing a very sensitive readout for TDP-43 function. The results are convincing, rigorous, and support their main conclusions. There are some minor weaknesses listed above, chief of which is the use of flow sorting to improve the data analysis. But regardless, this study will have an immediate impact for those who need a rapid, reliable, and sensitive assessment of TDP-43 activity, and it will be particularly impactful once this reporter can be used in isolated primary cells (ie neurons) and in vivo in animal models. Since TDP-43 loss of function is thought to be a dominant pathological mechanism in ALS/FTD and likely many others disorders, having these type of sensors is a major boost to field and will change our ability to see sub-threshold changes in TDP-43 function that might otherwise not be possible with current approaches.

Comments on revisions:

In the revised version, most of the reviewer's comments have been appropriately addressed with the exception of 1) the use of flow sorting to improve the data analysis and 2) testing this sensor in primary neurons. The latter is the focus of an ongoing separate study. Though flow sorting would significantly strengthen this study and help others in the field to use this sensor, it is still an impactful and innovative study without it.

Reviewer #1 (Public review):

Summary:

Planar cell polarity core proteins Frizzled (Fz)/Dishevelled (Dvl) and Van Gogh-like (Vangl)/Prickle (Pk) are localized on opposite sides of the cell and engage in reciprocal repression to modulate cellular polarity within the plane of static epithelium. In this interesting manuscript, the authors explore how the anterior core proteins (Vangl/Pk) inhibit the posterior core protein (Dvl). The authors propose that Pk assists Vangl2 in sequestering both Dvl2 and Ror2, while Ror2 is essential for Dvl to transition from Vangl to Fz in response to non-canonical Wnt signaling.

Strengths:

The strengths of the manuscript are found in the very interesting and new concept along with supportive data for a model of how non-canonical Wnt induces Dvl to transition from Vangl to Fz with an opposing role for PK and Vangl2 to suppress Dvl during convergent extension movements. Ror is key player required for the transition and antagonizes Vangl.

Weaknesses:

In addition to general whole embryo morphology that is used as evidence for CE defects, two forms of data are presented: co-expression and IP, as well as IF of exogenously expressed proteins. The microscopy would benefit from super-resolution microscopy since in many cases the differences in protein localization are not very pronounced, and Western analysis data often show relatively subtle differences. Thus, future work will determine the strength of the interactions of the model.

Major points.

Overexpression conditions

A possible concern is that most analyses were performed with overexpression conditions. PCP core proteins (Vangl2, Pk, Dvl, and Fz receptors) are known to display polarized subcellular localization in both the neural epithelium and DMZ explants (Ref: PCP and Septins govern the polarized organization of the actin cytoskeleton during convergent extension, Current Biology, 2024). However, in this study, overexpressed PCP core proteins failed to show polarized localization. Thus, one must be careful in interpreting data.

Subtle effects

Several of the reported results show quite modest changes in imaging and immunoprecipitation analyses, which are supportive of the proposed molecular model, but future experiments will be needed to robustly test the model.

Reviewer #1 (Public review):

Summary:

This manuscript presents an end-to-end pipeline, intended to accelerate EM-based connectomics by combining low-resolution imaging for large volumes with synapse-level imaging only in selected regions of interest. In principle, this strategy can substantially reduce imaging time, computational demands, analysis time, and overall cost.

General note:

Overall, I found the manuscript interesting and valuable, particularly as a description of how one laboratory has assembled and applied a practical workflow to reconstruct and analyze the central complex across multiple insect species. In that sense, the work is compelling as an account of a real, functioning strategy for comparative connectomics, and I appreciated reading it. My main reservation is not about the relevance of the biological problem or the utility of the pipeline in the authors' own hands, but about whether the manuscript, in its current form, fully meets the expectations of a paper that is focused on tools and resources. The expectation would be that this paper would be a venue for sharing new techniques, software tools, datasets, and other resources intended to be usable by the community. Here, because much of the pipeline appears to build on existing methods and software, the key value added should be a particularly clear demonstration of how these components were adapted, integrated, validated, and documented for this specific use case in a way that others could realistically reproduce and adopt. At present, that translational and reproducibility-oriented component does not yet seem sufficiently developed, despite the clear promise of the overall approach.

Major comments:

(1) The work is valuable as a practical integration and application of multiple existing tools into a coherent pipeline, together with a new multi-resolution imaging strategy. However, the manuscript at times reads as though it introduces an entirely novel workflow. I would encourage the authors to clarify the contribution more explicitly: which components are genuinely new (for example, the acquisition strategy and the end-to-end integration/validation), and which are adaptations of already established methods or software. This would make the scope and novelty of the paper easier to assess.

(2) The most distinctive element is the multi-resolution acquisition strategy. However, as described, the selection of high-resolution regions seems to be decided a priori based on anatomy (guided by xCT localization of the CX), rather than being determined automatically from the data (i.e., ROI placement is anatomy-driven rather than data-driven). A more data-driven or machine learning-guided ROI strategy would strengthen the methodological contribution and the adaptability to new scenarios, along the lines of approaches such as SmartEM [1].

(3) The manuscript emphasizes open-source availability and reduced barriers to entry, but the current software release, as referenced, does not yet appear to support straightforward external reuse. Since much of the pipeline builds on existing methods, the main added value lies in how these technologies were adapted, combined, and validated for the present problem. A clear and complete explanation of this adaptation is therefore essential, but is currently missing. I would suggest the following concrete improvements:<br /> a) Provide a single landing page or umbrella repository that links each pipeline step in the paper to the corresponding codebase, including version tags/commits and expected inputs/outputs for each step.<br /> b) Include step-by-step tutorials for each component.<br /> c) Provide an example dataset together with a full reproduction walkthrough in a controlled environment.<br /> d) Clearly explain the required parameters and configuration for each step, including how they should be adjusted for other datasets or scenarios.<br /> e) Follow packaging and distribution best practices (for example, PyPI/conda releases, Docker containers, and version pinning).

(4) In my own attempt to set up and run parts of the released code, I encountered issues that currently limit reproducibility. For example, when creating an environment for EMalign (https://github.com/Heinze-lab/EMalign), the required Python version is not specified, and installation did not succeed under Python 3.12 due to dependency constraints. Additionally, synful_312 (https://github.com/Heinze-lab/synful_312) and SegToPCG (https://github.com/Heinze-lab/SegToPCG) appear to be empty despite being referenced in the manuscript. These are fixable issues, but addressing them is important if the paper is to deliver on its "low entry cost" claim.

(5) Table 1 reports acquisition times, which is helpful. However, the multi-resolution approach adds essential processing steps that appear due to the strategy followed (e.g., "XY alignment high-res" and "high-res to low-res alignment"). Please include registration/alignment (and other major post-processing) runtimes and resource requirements, such as storage, in a comparable table so readers can assess true end-to-end cost.

References:

[1] Meirovitch, Y., et al. "SmartEM: machine learning-guided electron microscopy." Nature Methods (2025).

Reviewer #1 (Public review):

Summary:

The authors aimed to determine the neural networks involved in updating behaviour by training mice on a 'go / no go' odour discrimination task, and measuring their brain activity using functional MRI.

Strengths:

The use of the translationally relevant 'go / no go' task is a major strength, as this is a task that can be used as readily in humans as in animals such as mice. The use of fMRI in awake, behaving mice is also a major strength, as this allows the activation of multiple brain regions to be measured while behaviour is ongoing, and also facilitates comparison to human studies. The computational modelling approaches further support these translational aims, again being as readily applied to human data as to animal data.

Weaknesses:

The major weakness of the paper - and one that is potentially addressable - is that the key analysis of the paper, showing that the periaqueductal gray (PAG) is recruited for reversal learning, is only partially supported by the data presented in the paper as it stands. The authors have used a sophisticated way of analysing the behavioural data using 'signal detection theory', in which they collected behavioural data showing correct 'go' responses ('hits'), correct 'no go' responses ('correct rejections'), missed 'go' responses ('misses') and go responses when mice should have withheld a response ('false alarms'). The data presented showing a double dissociation in the activation of the nucleus accumbens for 'hits' but not 'correct rejections' and the PAG for 'correct rejections' but not 'hits' is very interesting; however, it is confounded by the fact that the nucleus accumbens may activate when the animal makes a response, and the PAG when the animal withholds a response. If the authors also included the analysis of nucleus accumbens and PAG activation for 'misses' and 'false alarms', this would allow them to determine whether the activation of these regions reflects the behavioural response or the expectation of reinforcement from the response.

Thus, the paper includes very interesting data and is impressive in its approach to analysing behaviour in a manner that is highly translatable between species. The additional analyses would markedly strengthen the paper and would add depth to the finding that the PAG appears to be involved in behavioural flexibility.

Reviewer #1 (Public review):

Summary:

In their manuscript, Zhou and colleagues present a detailed look at how the JSP functions differently in the various cells of a breast tumor. The authors have effectively shown that the JSP acts as a double-edged sword, as it helps T cells fight cancer but also allows tumor cells to grow and avoid ferroptosis. These findings are important because they identify a useful biomarker to predict how TNBC patients might respond to PD-1 inhibitors.

Strengths:

This work is important because it provides a clear explanation for the conflicting roles of the JSP in the tumor environment. The evidence is solid, as it combines data from thousands of patients with single-cell analysis and lab experiments to confirm the role of STAT4 in cancer progression and immunity.

Weaknesses:

However, there are areas for improvement in the scope of the review, the depth of analysis, and the potential for broader clinical implications. The authors are encouraged to address these issues to enhance the scientific and clinical impact of the study.

Major Issues:

(1) The authors demonstrate that STAT4 upregulates SLC47A1, but this is currently supported only by expression correlation and western blot data. To confirm a direct link, the authors are encouraged to perform ChIP-qPCR or luciferase reporter assays to show that STAT4 binds directly to the SLC47A1 promoter.

(2) The conclusion that the MIF-CD74 axis drives immunosuppression is based on computational inference. To support this, the authors could consider mining publicly available breast cancer spatial transcriptomics data to show the co-localization of MIF and CD74. Alternatively, performing simple dual-color immunofluorescence staining on a few clinical sections would effectively demonstrate the physical proximity of these cells.

(3) TNBC is highly heterogeneous and includes subtypes like mesenchymal and immunomodulatory groups. The authors should analyze whether the JSP score or STAT4 levels vary significantly between these subtypes, as this could further refine the selection of patients for JAK1 inhibitors.

(4) While the JSP score works well in the current datasets, the authors should consider validating its predictive accuracy in additional independent immunotherapy cohorts, such as the TONIC trial, to ensure the biomarker is robust across different treatment settings.

Minor Issue:

The manuscript mentions a U-shaped trajectory of JSP activity during tumor transition. A more detailed biological explanation of why the pathway activity initially drops and then rises would add depth to the discussion.

Reviewer #1 (Public review):

Summary:

Fields et al. investigated the heterogeneity and kinetics of human antibody secreting cell (ASC) differentiation by analyzing ex vivo tonsil samples and using in vitro differentiation modeling. They discovered that a CD30+ intermediate subset emerges in transition from B cell to ASC in both contexts, but not from germinal centers, and they identified cytokines that promote this state. They also identified an isoform of CD44, CD44v9, that is expressed on some ASCs.

Strengths:

The strengths are the novelty of the findings and the identification of two new markers that may be useful for tracking ASC heterogeneity.

Weaknesses:

However, some of this work seems preliminary and would need to be further validated. Some of the data presented was only representative, with limited controls and biological repeats, limiting the interpretation. For example, the role of Mef2c for CD30 expression was not robustly demonstrated. It was not clear if Figure 1 scRNAseq/ATACseq was from multiple donors or just one. Future studies may extend these novel findings and determine the functional relevance of these factors, CD30, and CD44v9 for ASC differentiation and physiology.

Reviewer #1 (Public review):

Summary:

Spinal projection neurons in the anterolateral tract transmit diverse somatosensory signals to the brain, including touch, temperature, itch, and pain. This group of spinal projection neurons is heterogeneous in their molecular identities, projection targets in the brain, and response properties. While most anterolateral tract projection neurons are multimodal (responding to more than one somatosensory modality), it has been shown that cold-selective projection neurons exist in lamina I of the spinal cord dorsal horn. Using a combination of anatomical and physiological approaches, the authors discovered that the cold-selective lamina I projection neurons are heavily innervated by Trpm8+ sensory neuron axons, with calb1+ spinal projection neurons primarily capturing these cold-selective lamina I projection neurons. These neurons project to specific brain targets, including the PBNrel and cPAG. This study adds to the ongoing effort in the field to identify and characterize spinal projection neuron subtypes, their physiology, and functions.

Strengths:

(1) The combination of anatomical and physiological analyses is powerful and offers a comprehensive understanding of the cold-selective lamina I projection neurons in the spinal cord dorsal horn. For example, the authors used detailed anatomical methods, including EM imaging of Trpm8+ axon terminals contacting the Phox2a+ lamina I projection neurons. Additionally, they recorded stimulus-evoked activity in Trpm8-recipient neurons, carefully selected by visual confirmation of tdTomato and GFP juxtaposition, which is technically challenging.

(2) This study identifies, for the first time, a molecular marker (calb1) that labels cold-selective lamina I projection neurons. Although calb1+ projection neurons are not entirely specific to cold-selective neurons, using an intersectional strategy combined with other genes enriched in this ALS group or cold-induced FosTRAP may further enhance specificity in the future.

(3) This study shows that cold-selective lamina I projection neurons specifically innervate certain brain targets of the anterolateral tract, including the NTS, PBNrel, and cPAG. This connectivity provides insights into the role of these neurons in cold sensation, which will be an exciting area for future research.

Weaknesses:

(1) The sample size for the ex vivo electrophysiology conducted on the calb1+ lamina I projection neurons (Figure 5) is limited to a total of six recorded neurons. Given the difficulty and complexity of the preparation, this is understandable. Notably, since approximately 87% of lamina I projection neurons heavily innervated by Trpm8+ terminals are calb1+, these six recordings of such neurons in Figure 4E could also be calb1+.

Reviewer #1 (Public review):

Summary:

Spinal projection neurons in the anterolateral tract transmit diverse somatosensory signals to the brain, including touch, temperature, itch, and pain. This group of spinal projection neurons is heterogeneous in their molecular identities, projection targets in the brain, and response properties. While most anterolateral tract projection neurons are multimodal (responding to more than one somatosensory modality), it has been shown that cold-selective projection neurons exist in lamina I of the spinal cord dorsal horn. Using a combination of anatomical and physiological approaches, the authors discovered that the cold-selective lamina I projection neurons are heavily innervated by Trpm8+ sensory neuron axons, with calb1+ spinal projection neurons primarily capturing these cold-selective lamina I projection neurons. These neurons project to specific brain targets, including the PBNrel and cPAG. This study adds to the ongoing effort in the field to identify and characterize spinal projection neuron subtypes, their physiology, and functions.

Strengths:

(1) The combination of anatomical and physiological analyses is powerful and offers a comprehensive understanding of the cold-selective lamina I projection neurons in the spinal cord dorsal horn. For example, the authors used detailed anatomical methods, including EM imaging of Trpm8+ axon terminals contacting the Phox2a+ lamina I projection neurons. Additionally, they recorded stimulus-evoked activity in Trpm8-recipient neurons, carefully selected by visual confirmation of tdTomato and GFP juxtaposition, which is technically challenging.

(2) This study identifies, for the first time, a molecular marker (calb1) that labels cold-selective lamina I projection neurons. Although calb1+ projection neurons are not entirely specific to cold-selective neurons, using an intersectional strategy combined with other genes enriched in this ALS group or cold-induced FosTRAP may further enhance specificity in the future.

(3) This study shows that cold-selective lamina I projection neurons specifically innervate certain brain targets of the anterolateral tract, including the NTS, PBNrel, and cPAG. This connectivity provides insights into the role of these neurons in cold sensation, which will be an exciting area for future research.

Weaknesses:

(1) The sample size for the ex vivo electrophysiology is small. Given the difficulty and complexity of the preparation, this is understandable. However, a larger sample size would have strengthened the authors' conclusions.

(2) The authors used tdTomato expression to identify brain targets innervated by these cold-selective lamina I projection neurons. Since tdTomato is a soluble fluorescent protein that fills the entire cell, using synaptophysin reporters (e.g., synaptophysin-GFP) would have been more convincing in revealing the synaptic targets of these projection neurons.

(3) The summary cartoon shown in Figure 7 can be misleading because this study did not determine whether these cold-selective lamina I projection neurons have collateral branches to multiple brain targets or if there are anatomical subtypes that may project exclusively to specific targets. For example, a recent study (Ding et al., Neuron, 2025) demonstrated that there are PBN-projecting spinal neurons that do not project to other rostral brain areas. Furthermore, based on the authors' bulk labeling experiments, the three main brain targets are NTS, PBNrel, and cPAG. The VPL projection is very sparse and almost negligible.

Reviewer #1 (Public review):

Summary:

CCK is the most abundant neuropeptide in the brain, and many studies have investigated the role of CCK and inhibitory CCK interneurons in modulating neural circuits, especially in the hippocampus. The manuscript presents interesting questions regarding the role of excitatory CCK+ neurons in the hippocampus, which has been much less studied compared to the well-known roles of inhibitory CCK neurons in regulating network function. The authors adopt several methods including transgenic mice and viruses, optogenetics, chemogenetics, RNAi, and behavioral tasks to explore these less-studied roles of excitatory CCK neurons in CA3. They find that the excitatory CCK neurons are involved in hippocampal-dependent tasks such as spatial learning and memory formation, and that CCK-knockdown impairs these tasks.

However, these questions are very dependent on ensuring that the study is properly targeting excitatory CCK neurons (and thus their specific contributions to behavior).

There needs to be much more characterization of the CCK transgenic mice and viruses to confirm the targeting. Without this, it is unclear whether the study is looking at excitatory CCK neurons or a more general heterogeneous CCK neuron population.

Strengths:

This field has focused mainly on inhibitory CCK+ interneurons and their role in network function and activity, and thus this manuscript raises interesting questions regarding the role of excitatory CCK+ neurons, which have been much less studied.

Weaknesses:

(1a) This manuscript is dependent on ensuring that the study is indeed investigating the role of excitatory CCK-expressing neurons themselves and their specific contribution to behavior. There needs to be much more characterization of the CCK-expressing mice (crossed with Ai14 or transduced with various viruses) to confirm the excitatory-cell targeting. Without this, it is unclear whether the study is looking at excitatory CCK neurons or a more general heterogeneous CCK neuron population.

(2) The methods and figure legends are still extremely sparse, still leading to many questions regarding methodology and accuracy. More details would be useful in evaluating the tools and data, and the lack of proper quantification is still prevalent throughout the paper. In many places, only % values are noted, or only images are presented, and the number of cells counted is almost never reported.

Reviewer #1 (Public review):

Summary:

The authors test whether the frog buccal ventilatory rhythm generator behaves as a discrete, anatomically localized oscillator or as a distributed, state-dependent network. They combine reduced preparations (segment/subsegment work), systematic extracellular unit surveys over a defined grid, and local AMPA/GABA microinjections in a hemisected brainstem preparation. Based on these approaches, the authors conclude that mild global excitation (bath AMPA) broadens the distribution of rhythmically active units and renders a previously defined "buccal area" functionally non-identifiable as a unique necessary/sufficient locus.

The central idea is plausible, and the overall experimental strategy is appropriate for the question being asked. However, in its current form, the manuscript overstates the strength of inference supporting the "expansion" and "loss of necessity/sufficiency" conclusions. This is primarily due to (a) statistical treatment of unit-mapping data that does not respect clustering by preparation/animal, (b) inconsistent statistical reporting across sections, and (c) limited interpretability of focal inhibitory perturbations under a globally excited state.

Strengths:

(1) The manuscript addresses a clear mechanistic question with broader relevance: whether rhythm generation is best conceptualized as a localized kernel or as an emergent distributed property that changes with excitatory state.

(2) The authors use convergent approaches (reduced preparations, mapping, and necessity/sufficiency-style pharmacological perturbations), which is appropriate for circuit-level inference.

(3) A strong element is the within-unit analysis supporting state-dependent changes in phase coupling for a subset of units ("lung" units adopting a buccal-like pattern). The authors' offline PCA-based spike sorting (with cluster-quality selection via silhouette score) provides some reassurance that the reported pre/post injection changes are not simply driven by unit misidentification.

Weaknesses:

(1) Pseudoreplication in unit-survey statistics undermines the main mapping inference. The Methods state that "Units were pooled from multiple preparations" and that chi-squared tests were used to compare proportions across conditions (baseline vs 60 nM AMPA). The Results similarly report proportion changes (e.g., 110 units pooled from three preparations vs 137 units pooled from three additional animals) analyzed with chi-squared tests. Because many units come from the same preparation/animal, independence is unlikely to hold; therefore, inference about state-dependent reorganization at the systems level should be made at the preparation/animal level or via hierarchical models that explicitly account for clustering.

(2) Statistical methods are inconsistently described and need harmonization. In the segment dose-response "Analysis," values are described as compared to zero using a "One-sample t-test." Yet Table 1 is titled as using a "Wilcoxon One-sample Test." These discrepancies must be resolved throughout (Methods, Results, figure legends, and tables), including clear reporting of the unit of n and exact test statistics.

(3) Unit classification and operational definitions raise interpretational concerns. The unit classification scheme defines "buccal units" as those firing during buccal bursts as well as lung bursts, and explicitly notes that "no units were found which fired only during buccal bursts." This is a consequential result, and it currently reads more like a limitation of detection/classification (or state-space sampled) than a robust biological conclusion. Without additional evidence, it weakens claims about a distinct buccal rhythmogenic module and complicates the interpretation of "buccal identity" changes under excitation.

(4) Microinjection mapping: high exclusion rate and alternative explanations for 'loss of necessity' under excitation. The manuscript reports that 15 experiments were conducted, but 9 were excluded because the buccal area was not found or the preparation was "overdriven." This exclusion rate is too high to leave implicit; it raises concerns about selection bias and demands transparent accounting. Moreover, under baseline conditions, GABA (or AMPA-GABA) microinjections reliably reduce/abolish buccal bursts, but under bath 60 nM AMPA, the same injections produce no significant change in instantaneous frequency. This pattern can be interpreted as network redistribution, but it can also reflect state-dependent changes in gain, dynamic range, or local pharmacological impact (e.g., inhibition being comparatively underpowered in the globally excited state). Additional controls/analyses are required to distinguish these explanations.

Reviewer #1 (Public review):

Summary:

Choucri and Treiber have reassessed their previous study on TE-gene chimeric transcripts in neural genes in response to Azad et al (2024). Azad and colleagues argued that, contrary to Choucri and Treiber's findings, chimeric TE-mRNAs are relatively infrequent, and they cautioned that further optimization of bioinformatics pipelines is needed to detect TE insertions from RNAseq accurately. In this short response, Choucri and Treiber clearly demonstrate that differences in the tools used between their study and that of Azad et al. likely account for the contrasting results, along with RT-PCR failure in designing primers that would match the chimeric transcript, and the use of different Drosophila lines. The authors emphasize the need for uniform, standardized criteria in such analysis, which would ultimately strengthen and advance the field.

Strengths:

The addition of a ratio to compute the number of splice reads specific to the chimeric transcript and compare to the exon-exon splice reads is really interesting because it opens the door to finally quantify the contribution of chimeric TEs to the overall gene expression, although this is not the scope of the present article. The clear dissection of chimeric transcripts, along with the results from Azad et al, allows us to understand the differences between the two studies confidently. Finally, the discussion on Drosophila lines is indeed essential, given that the lines and even individuals have high TE polymorphism.

Weaknesses:

I think it is necessary to add more detail to this article, for instance, the differences between TEchim and Tidal could be laid out more precisely. Regarding the roo example, one of the caveats of this family, along with others, is the presence of simple repeats. It would be important to show that the simple repeats are not interfering with the read mapping. Regarding the experiments, if we are looking for a standardized protocol, then we should have a detailed material and methods section, with every experiment, replicate, and PCR temperature clearly defined. Finally, and in my opinion, more importantly, the use of RT negative controls on the RT PCRs, along with DNA PCRs to show insertion presence, is mandatory for testing the presence of chimeric genes. Of course, water negative PCR controls are also needed, and unfortunately, absent from Figure 3.

Reviewer #1 (Public review):

[Editors' note: this version has been assessed by the Reviewing Editor without further input from the original reviewers. The authors have addressed the minor comments raised in the previous round of review.]

Summary:

In this manuscript, Chengjian Zhao et al. focused on the interactions between vascular, biliary, and neural networks in the liver microenvironment, addressing the critical bottleneck that the lack of high-resolution 3D visualization has hindered understanding of these interactions in liver disease.

Strengths:

This study developed a high-resolution multiplex 3D imaging method that integrates multicolor metallic compound nanoparticle (MCNP) perfusion with optimized CUBIC tissue clearing. This method enables the simultaneous 3D visualization of spatial networks of the portal vein, hepatic artery, bile ducts, and central vein in the mouse liver. The authors reported a perivascular structure termed the Periportal Lamellar Complex (PLC), which is identified along the portal vein axis. This study clarifies that the PLC comprises CD34⁺Sca-1⁺ dual-positive endothelial cells with a distinct gene expression profile, and reveals its colocalization with terminal bile duct branches and sympathetic nerve fibers under physiological conditions.

Comments on revisions:

The authors very nicely addressed all concerns from this reviewer. There are no further concerns and comments.

Reviewer #1 (Public review):

This manuscript investigates how dentate gyrus (DG) granule cell subregions, specifically suprapyramidal (SB) and infrapyramidal (IB) blades, are differentially recruited during a high cognitive demand pattern separation task. The authors combine TRAP2 activity labeling, touchscreen-based TUNL behavior, and chemogenetic inhibition of adult-born dentate granule cells (abDGCs) or mature granule cells (mGCs) to dissect circuit contributions.

This manuscript presents an interesting and well-designed investigation into DG activity patterns under varying cognitive demands and the role of abDGCs in shaping mGC activity. The integration of TRAP2-based activity labeling, chemogenetic manipulation, and behavioral assays provides valuable insight into DG subregional organization and functional recruitment. However, several methodological and quantitative issues limit the interpretability of the findings. Addressing the concerns below will greatly strengthen the rigor and clarity of the study.

Major points:

(1) Quantification methods for TRAP+ cells are not applied consistently across panels in Figure 1, making interpretation difficult. Specifically, Figure 1F reports TRAP+ mGCs as density, whereas Figure 1G reports TRAP+ abDGCs as a percentage, hindering direct comparison. Additionally, Figure 1H presents reactivation analysis only for mGCs; a parallel analysis for abDGCs is needed for comparison across cell types.

(2) The anatomical distribution of TRAP+ cells is different between low- and high-cognitive demand conditions (Figure 2). Are these sections from dorsal or ventral DG? Is this specific to dorsal DG, as itis preferentially involved in cognitive function? What happens in ventral DG?

(3) The activity manipulation using chemogenetic inhibition of abDGCs in AsclCreER; hM4 mice was performed; however, because tamoxifen chow was administered for 4 or 7 weeks, the labeled abDGC population was not properly birth-dated. Instead, it consisted of a heterogeneous cohort of cells ranging from 0 to 5-7 weeks old. Thus, caution should be taken when interpreting these results, and the limitations of this approach should be acknowledged.

(4) There is a major issue related to the quantification of the DREADD experiments in Figure 4, Figure 5, Figure 6, and Figure 7. The hM4 mouse line used in this study should be quantified using HA, rather than mCitrine, to reliably identify cells derived from the Ascl lineage. mCitrine expression in this mouse line is not specific to adult-born neurons (off-targets), and its expression does not accurately reflect hM4 expression.

(5) Key markers needed to assess the maturation state of abDGCs are missing from the quantification. Incorporating DCX and NeuN into the analysis would provide essential information about the developmental stage of these cells.

Minor points:

(1) The labeling (Distance from the hilus) in Figure 2B is misleading. Is that the same location as the subgranular zone (SGZ)? If so, it's better to use the term SGZ to avoid confusion.

(2) Cell number information is missing from Figures 2B and 2C; please include this data.

(3) Sample DG images should clearly delineate the borders between the dentate gyrus and the hilus. In several images, this boundary is difficult to discern.

(4) In Figure 6, it is not clear how tamoxifen was administered to selectively inhibit the more mature 6-7-week-old abDGC population, nor how this paradigm differs from the chow-based approach. Please clarify the tamoxifen administration protocol and the rationale for its specificity.

Comments on revisions:

I appreciate the authors' careful and thorough revisions. They have addressed all of my previous concerns satisfactorily, and the manuscript is now significantly strengthened. I have no further concerns.

Reviewer #1 (Public review):

Kong et al.'s work describes a new approach that does exactly what the title states, "Correction of local beam-induced sample motion in cryo-EM images using a 3D spline model." It is, therefore, a more elaborate approach than current methods in the field for the "movie alignment" stage. Additionally, the work uses 2DTM (2D Template Matching)-related measurements to quantify the improvement of the new method compared to other methods in the field. I find both parts very compelling (the new method and the testing approach)

On a "focused" view, the strengths of the work rest on presenting a better approach for motion correction and on measuring their performance very well at the 2D level in a compelling manner

On a more "general" view, the authors introduce the important notion that even one of the most worked-out steps in the processing workflow can still be done better in a measurable way, and that this could lead to better results beyond the 2DTM metrics used for testing, reflecting in better results along the processing pipeline (although the manuscript does not explore further this notion)

On the "usability" side, the method is still CPU-based and is slower than standards in the field. This may pose significant limitations in practical work, although the authors are aware of this issue and are working on it.

Reviewer #2 (Public review):

Summary:

In this study, Bansal et al examine and characterize feeding behaviour in Anopheles stephensi mosquitoes. While sharing some similarities to the well-studied Aedes aegypti mosquito, the authors demonstrate that mated-females, but not unmated (virgin) females, exhibit suppression in their blood-feeding behaviour after imbibing an initial bloodmeal. Using brain transcriptomic analysis comparing sugar fed, blood fed and starved mosquitoes, several candidate genes potentially responsible for influencing blood-feeding behaviour were identified, including two neuropeptides (short NPF and RYamide) that are known to modulate feeding behaviour in other mosquito species. Using molecular tools including in situ hybridization, the authors map the distribution of cells producing these neuropeptides in the nervous system and in the gut. Further, by implementing systemic RNA interference (RNAi), the study suggests that both neuropeptides (particularly in the brain, but not in the abdomen since knockdown outside the brain did not affect feeding behaviour) appear to promote blood-feeding while having no impact on sugar feeding. Interestingly, when either of these two neuropeptide gene transcripts were reduced independently by RNAi, the proportion of females acquiring a blood meal was not affected, whereas simultaneous knockdown of both sNPF and RYa led to a reduction in blood feeding behaviour but did not impact sugar feeding.

Given that the expression of both neuropeptide genes was found in mostly in non-overlapping brain neurons, this suggests that these two neuropeptides may elicit at least partially complementary actions promoting blood feeding in A. stephensi. Indeed, their putative receptors appear to be colocalized within several neurons within the brain, which could explain why knockdown of both sNPF and RYa transcripts was required to affect blood feeding behaviour (although authors could not confirm if either of these neuropeptides act independently as only partial knockdown was achieved in the brain). Finally, while sNPF was mapped to brain neurons and midgut enteroendocrine cells, the authors mapped RYa only in the brain while reporting expression in the abdomen by qPCR, but that was not localized to the midgut EECs (like sNPF). Therefore, the source of RYamide in the abdomen remains unknown in this mosquito species, but could involve the abdominal ganglia where this neuropeptide has been localized in Ae. aegypti.

Strengths and/or weaknesses:

Overall, the manuscript was effectively communicated. Previous concerns and requested clarifications have been addressed in the revised manuscript. While advanced cell-specific tools are lacking in this mosquito species, one weakness here is that peptides could have been applied ectopically in attempts to rescue the deficit in blood feeding behaviour following knockdown by RNAi. Further insight in this regard may be provided in future studies by this and other research groups.

Reviewing editor comment:

Inclusion of a schematic in Supplementary Figure S9B addresses the point raised by reviewer 1 in the previous round.

Reviewer #1 (Public review):

Summary:

The authors aimed to investigate how short-term visual deprivation influences tactile processing in the primary somatosensory cortex (S1) of sighted rats. They justify the study based on previous studies that have shown that long-term blindness can enhance tactile perception, and aim to investigate the change in neural representations underlying rapid, short-term cross-modal effects. The authors recorded local field potentials from S1 as rats encountered different tactile textures (smooth and rough sandpaper) under light and dark conditions. They used deep learning techniques to decode the neural signals and assess how tactile representations changed across the four different conditions. Their goal was to uncover whether the absence of visual cues leads to a rapid reorganization of tactile encoding in the brain.

Strengths:

The study effectively integrates high-density local field potential (LFP) recordings with convolutional neural network (CNN) analysis. This combination allows for decoding high-dimensional population-level signals, revealing changes in neural representations that traditional analyses (e.g., amplitude measures) failed to detect. The custom treadmill paradigm permits independent manipulation of visual and tactile inputs under stable locomotion conditions. Gait analysis confirms that motor behavior was consistent across conditions, strengthening the conclusion that neural changes are due to sensory input rather than movement artifacts.

Weaknesses:

(1) While the study interprets the emergence of more distinct texture representations in the dark as evidence of rapid cross-modal plasticity, the claim rests on correlational data from a short-term manipulation and decoding analysis. The authors show that CNN-derived feature embeddings cluster more clearly by texture in the dark, but this does not directly demonstrate plasticity in the classical sense (e.g., synaptic or circuit-level reorganization). The authors have noted this as a limitation and have clarified that the observed changes reflect functional reorganization rather than structural plasticity.

(2) Although gait was controlled, changes in arousal or exploratory behavior in light versus dark conditions might play a role in the observed neural differences. The authors have controlled for various factors in relation to locomotion, but future studies would benefit from more direct behavioural readouts of arousal states (e.g., via pupillometry or cortical state indicators).

(3) It should be noted that the time course of the observed changes (within 10 minutes) is quite rapid, and while intriguing, the study does not include direct evidence that the underlying circuits were reorganized-only that population-level signals become more discriminable. The authors have adequately discussed this as an avenue for more mechanistic future research.

(4) The authors have adequately discussed that, while these findings are consistent with somatotopy and context-dependent dynamics, they do not provide strong independent evidence for novel spatial or temporal organization.

(5) The authors have also discussed that, while the neural data suggest enhanced tactile representations, the study does not assess whether rats' actual tactile perception improved. Future studies including an assessment of a behavioral readout (e.g., discrimination accuracy), would be insightful.

(6) The authors' discussion about the implications for sensory rehabilitation, including Braille training and haptic feedback enhancement was a bit premature, but they have amended this, and it remains an interesting translational potential to be explored in future studies.

(7) While the CNN showed good performance, more transparent models (e.g., linear classifiers or dimensionality reduction) appear to not exceed chance level. The implications of this are that there is an underlying complex structure in the LFPs that has yet to be fully uncovered, on the mechanistic level. This would be important to push the findings forward in future studies.

Therefore, while the authors raise interesting hypotheses around rapid plasticity, somatotopic dynamics, and rehabilitation, the evidence for each is indirect. Stronger claims will require future causal experiments, behavioral readouts, and mechanistic specificity beyond what the current data provides. However, the work represents an interesting starting point to a more mechanistic understanding in the future.

Reviewer #2 (Public review):

Summary:

An abundant literature documents molecular changes in the rodent hypothalamus that occur during the transition from prepubertal to mature reproductive physiology. Equally well documented is the role of sex steroids and their receptors during this important period of reproductive development, as well as the importance of GABAergic and glutamatergic neurons. The medial preoptic area (MPOA) is known to play a central role in expression of sexually dimorphic reproductive function and previously reported sexually dimorphic patterns of gene expression are consistent with this role. The present manuscript extends this knowledge base and reports the results of a detailed evaluation of transcriptional dynamics in the MPOA during the adolescent transition to maturity with a particular focus on the role of the estrogen receptor gene (Esr1). Both single cell RNA sequencing (scRNseq) and multiplex in situ hybridization methods were employed and the results subjected to detailed computational analyses to demonstrate that the transcriptomic structure of MPOA neurons displays both sex and cell type specific expression profiles. In addition, both hormonal and genetic manipulations of Esr1 signaling during puberty altered the transcriptional profiles of MPOA neurons, and these changes aligned with maturation of hormone-dependent reproductive function. The authors provide this evidence to illustrate Esr1-dependent control of gene regulatory networks required for normal expression of reproductive behaviors expressed during the transition from adolescence to adulthood. The results presented in this manuscript are extensive and represent the most comprehensive evaluation of transcriptomic changes during reproductive maturation to date. The methods appear strong and the results provide a rich data set that will support a good deal of future analysis.

Strengths:

(1) The major strength of this manuscript is the extensive set of images and graphs that illustrate molecular changes that occur in MPOA neurons during adolescence, although additional spatial detail as to locations of the source neurons would be welcome in order to place the changes in the proper circuitry context.

(2) Targeting Esr1 deletion to MPOA GABA neurons is a good choice, given how these cells have been implicated in sexual differentiation of reproductive behavior previously, and the lack of comparable responses in glutamatergic neurons is convincing. The AAV-frtFlex-Cre virus created by the investigators is a most useful tool for such studies. Profiling distinct transcriptomic trajectories in GABA and glutamatergic neurons during reproductive maturation is impressive and leads to some of the best supported conclusions in this paper.

(3) Cellular and molecular resolution of the transcriptomics data appears excellent, however, because the source tissue for the scRNAseq analysis was obtained by bulk dissection of the MPOA anatomical resolution is limited. This problem is addressed to some extent by careful comparison of scRNAseq results with previously published spatial transcriptomics data. The HM-HCR-FISH analysis clearly documents spatially restricted changes in gene expression, but it is hard to discern where these changes occur based on the images presented or the descriptions included in the Results. The anatomical schematic included in Figure 4 suggests that investigators are not familiar with components of the MPOA (see Allen Mouse Brain Atlas).

Weaknesses:

(1) A major conceptual flaw is that the authors do not distinguish between genetically determined sex differences in patterns of gene expression and differences caused by the fact that MPOA neurons are exposed to different endocrine environments in adolescent males and females, which can cause different transcriptional trajectories independent of genetic sex. This issue does not render their results invalid, but their terminology should address the issue in the discussion and "limitations" section. At the very least the endocrine status of "intact females" should be included.

(2) A major technical flaw is that the MPOA is treated as a functionally distinct brain region (block dissections) with uniform distribution of cell types (FISH data are not illustrated or reported with sufficient spatial detail). Thus, an enormous amount of molecular data is provided that cannot be mapped to distinct neural circuits, thereby limiting the neurobiological impact. This is also a weakness of the FISH data, which is presented with only small regions illustrated without anatomical detail. In fact, some images are compared that appear to illustrate different MPOA structures, although it is impossible to be certain of this due to the lack of morphological landmarks. The analysis of how Esr1 orchestrates regulatory gene networks is impressive and interesting, but the fact that many of the observed transcriptional events occur in neural circuits that do not overlap confounds interpretation.

(3) The locations of the AAV injections should be characterized because deleting Esr1 in multiple distinct parts of the MPOA will likely confound interpretation. This is especially problematic given the limited number of mice used for parts of the RNAscope analysis.

(4) Although the focus of these experiments on adolescence is welcome, neither the Introduction nor the Discussion do a good job of placing these studies in the context of what is already known about brain maturation during puberty. It is true that this is very much a results-focused manuscript, but the scholarship can be improved. Simply stating that your results are consistent with previous reports places an undue burden on the reader to go figure out what is new.

(5) Throughout the manuscript, the authors utilize obscure abbreviations, which often makes reading their text overly cumbersome. This is certainly justified in certain instances where complex names of analytical methods are used repeatedly, but the authors are encouraged to try and simply their use of non-standard abbreviations.

Comments on revisions:

The authors have considered issues raised during the initial review. Although there do not appear to be significant changes to analyses, figures or conclusions, the authors have added important revisions listing limitations in study design and methodology that impact interpretation.

Reviewer #1 (Public review):

Summary:

Overall, this is an interesting and well-written manuscript on a fascinating question in a "charismatic" model system.

Strengths:

1) The Introduction is concise, though it might be helpful to the non-specialist reader to learn a bit more about what is known about the social control of somatic growth across diverse species (including humans), which would help to make this work more generally interesting.

(2) The experiment is well-designed.

(3) The data collected are comprehensive.

(4) The complementary analysis of both feeding and aggression/submission data with and without known social roles is a neat idea and compelling!

Weaknesses:

(1) I was surprised that the HPA/stress axis was not considered here at all. Wouldn't we expect that subordinates have increased stress axis activation, which in turn could inhibit their growth and aggressive behavior?

(2) To what extent are growth, food intake, agonistic behavior, and/or gene expression patterns coordinated across P1 vs P2 pairs? The lack of such an analysis seems like a missed opportunity.

(3) What was the rationale for using whole bodies for the transcriptome analysis? Given the hypotheses, the forebrain or hypothalamus and certain other organ systems (e.g., liver, gonads, skin, etc.) would have been obvious candidate tissues here. I realize that cost is always a consideration, but maybe a focus on the fore-/midbrain could have been prioritized.

(4) Given the preceding point, why was a fold-change threshold used for assessing DEGs (supplementary Figure 3)? There is no biological justification to ever use a fold-change threshold, especially in bulk RNA-seq analysis. This is particularly true here, where whole bodies were used for RNA-seq analysis, which is a bit unusual. Relatively small cell populations (such as hypothalamic neurons that regulate growth or food intake) may show substantial gene expression variation across social types, yet will be masked by the masses of other cells in the whole body sample. However, gene expression may still vary significantly, albeit the fold-difference may be small. I therefore suggest a reanalysis that omits any fold-change threshold.

(5) Why is the analysis of color (hue, saturation) buried in the supplementary materials? Based on the hypotheses that motivated the study, color seems just as relevant as food intake, growth, and agonistic behavior, so even if the results are negative, they should be presented in the main paper.

(6) The Discussion is sometimes difficult to follow. The authors may want to consider including a conceptual graphic that integrates the different aspects of growth and satiety regulation, etc., into a work-in-progress model of sorts, which would also facilitate clearer hypotheses for future research.

Reviewer #1 (Public review):

Summary:

In this study, the authors examine how a developmentally regulated cis-regulatory element controls SOX2 expression during neural differentiation of human stem cells. The results suggest that this highly conserved long-range enhancer mediates neural-specific SOX2 regulation and offer insight into the role of promoter-enhancer contacts in this process. Although the findings are interesting, several limitations need to be addressed.

Strengths:

A central question in developmental biology is how genes are regulated in a context-dependent manner. SOX2, a major pluripotency factor, is expressed in diverse tissues during development, and therefore understanding the mechanisms that control its spatiotemporal expression is critical. This study addresses this important question by examining the functional relevance of a neural-specific, developmentally regulated SOX2 enhancer and its associated promoter-enhancer contacts in driving gene expression during human neural development. Using multiple model systems and techniques, the authors test the requirement of this enhancer by analyzing SOX2 expression in mutant lines, providing evidence for its role in this process.

Weaknesses:

A key limitation of the study is the absence of data from homozygous SOX2 enhancer deletion, which leaves the analysis incomplete and tempers the conclusions that can be drawn. Furthermore, the suitability of teratomas as a model system is questionable, given their limited capacity to recapitulate the spatial patterning, regional specification, and organized developmental processes characteristic of the human forebrain. Finally, the manuscript remains largely descriptive with little mechanistic insight.

Reviewer #1 (Public review):

Summary:

In this work, the authors investigate the mechanisms of low-frequency synaptic depression at cerebellar parallel fiber to interneuron synapses using unitary recordings that allow direct quantification of synaptic vesicle release. They show that sparse stimulation can induce robust synaptic depression even in the absence of substantial vesicle consumption, and that this depressed state is rapidly reversed when stimulation frequency is increased. To account for these observations, the authors propose a model in which low-frequency depression reflects a redistribution of vesicles within the readily releasable pool, in particular, a reduction in docking site occupancy due to vesicle undocking.

Strengths:

I found the experimental work to be of high quality throughout. The use of simple synapse recordings to count individual vesicle release events is particularly powerful in this context and allows questions to be addressed that are difficult to approach with more conventional approaches. The demonstration that low-frequency depression can occur independently of prior vesicle release, together with the rapid recovery observed during high-frequency stimulation, places strong constraints on possible underlying mechanisms and represents a clear strength of the study.

The modeling framework is clearly laid out and helps organize a broad set of observations across stimulation frequencies. Several of the experimental tests appear well-motivated by the model, including the recovery train experiments, the analysis of failures, and the use of doublet stimulation. Taken together, the data provide a coherent phenomenological description of low-frequency depression and its relationship to vesicle availability within the readily releasable pool.

Weaknesses:

While the experimental results are strong, the manuscript would benefit from rebalancing the strength of the mechanistic conclusions drawn from the modeling in light of its limitations. The framework is clearly useful and provides a coherent interpretation of the data, but it is not uniquely constrained by the experimental observations, and alternative models or interpretations could plausibly account for the findings. The use of different model regimes concatenated across time, with substantially different parameter values, highlights the abstract nature of the approach. For these reasons, the model seems best presented as one plausible explanatory framework rather than a definitive biological mechanism. Clarifying the distinction between data-driven observations and model-based inferences would help readers assess which conclusions are strongly supported and which remain more speculative.

The interpretation of the Ca2+-related experiments would benefit from more cautious wording. The absence of detectable changes in presynaptic Ca2+ signals does not exclude more localized or subtle Ca2+-dependent mechanisms, and conclusions regarding Ca2+ independence should therefore be framed accordingly. In addition, while low-frequency depression is still observed at reduced extracellular Ca2+, these experiments appear less diagnostic of the specific model-derived mechanism emphasized elsewhere in the manuscript - namely, a selective reduction in docking-site occupancy - and should be discussed with appropriate qualification in the text.

Major points:

(1) Clarify and qualify mechanistic claims derived from the model.

Throughout the manuscript, changes in model parameters are at times described as if they directly reflected underlying physiological mechanisms. As a result, the conceptual distinction between experimentally observed phenomena, model-derived variables, and biological interpretation is not always clear. Several conclusions in the Results and Discussion are phrased as mechanistic statements, although they rest on assumptions intrinsic to the modeling framework. The authors should systematically review the text and explicitly distinguish between (i) experimentally observed changes in synaptic responses and (ii) inferences about vesicle docking states or transitions within the model.

In particular, statements implying that vesicle undocking is the mechanism underlying low-frequency depression should be rephrased to reflect that this is an interpretation within the proposed framework rather than a uniquely demonstrated biological process. For example, statements such as "Low-frequency depression is caused by synaptic vesicle undocking" should be replaced with formulations such as "Within the framework of our model, low-frequency depression is accounted for by a redistribution of synaptic vesicles away from docking sites" or "Our results are consistent with a model in which changes in vesicle docking-state occupancy contribute to low-frequency depression."

A particularly problematic example is the statement that "these experiments further confirm that LFD only involves a decrease in δ, without accompanying changes in ρ or IP size." Here, an experimentally defined phenomenon (LFD) is directly equated with changes in model-derived variables. Such statements should be revised to make clear that δ, ρ, and IP size are inferred quantities within the model, and that the experimental data are interpreted through this framework rather than directly confirming changes in these parameters. Similarly, over-generalizing statements such as "Undocking therefore represents the key mechanism controlling short-term depression across stimulation frequencies" should be softened to reflect that this conclusion emerges from the model rather than from direct experimental evidence.

(2) Address the biological interpretation of time-dependent model regimes.

The model relies on distinct parameter regimes applied at different time points, with some transitions effectively suppressed in certain regimes. While this approach captures the data well, its biological interpretation remains unclear. The authors should either (i) expand the discussion to outline plausible biological processes that could give rise to such regime changes (for example, calcium-dependent modulation of transition rates or activity-dependent changes in vesicle state stability), or (ii) more explicitly frame this aspect of the model as a descriptive abstraction rather than a mechanistic proposal. This further underscores the need to clearly separate the descriptive role of the model from claims about underlying biological mechanisms.

(3) Reframe conclusions drawn from calcium-related experiments.

The calcium imaging data demonstrate no detectable changes in the measured presynaptic calcium signals under the tested conditions, but they do not rule out that calcium signals contribute in ways undetectable by the assay. Conclusions should therefore be revised to reflect this limitation, avoiding statements that exclude a role for calcium-dependent mechanisms. Wording such as "we did not detect evidence for..." would be more appropriate than conclusions implying the absence of an effect.

Similarly, while low-frequency depression is still observed at reduced extracellular calcium (1.5 mM Ca²⁺), the specific mechanistic signature emphasized elsewhere in the manuscript - namely a selectively reduced first response during a high-frequency recovery train - is no longer apparent. These experiments should therefore be discussed as consistent with the proposed framework, but not as providing independent support for a selective reduction in docking-site occupancy. Explicitly acknowledging this limitation would improve clarity and avoid over-interpreting these data.

(4) Soften interpretations based on non-significant comparisons.

In several places, comparisons that do not reach statistical significance are used to argue for equivalence between conditions (for example, comparisons involving failure versus non-failure trials or different LFD conditions). These conclusions should be revised to emphasize the limits of statistical power and framed as a lack of evidence for a difference rather than evidence of independence.

Reviewer #1 (Public review):

Sensory hair cells of the inner ear convert mechanical sound vibrations into electrical signals through mechano-electrical transduction (MET), a process critically dependent on the specialized organization and lipid composition of their plasma membrane. Although the protein components of the MET complex are relatively well characterized, the role of the lipid environment remains poorly understood and often overlooked. Recent discoveries that core MET proteins TMC1 and TMC2 function as lipid scramblases, disrupting membrane lipid asymmetry, expose a significant gap in our understanding of how lipid homeostasis is regulated in hair cells and how membrane dynamics influence MET function.

In this study, the authors address this gap by identifying the P4-ATPase ATP8B1 and its chaperone TMEM30B as essential regulators of membrane lipid asymmetry in outer hair cells. They also generated HA-tagged knock-in mice to precisely localize the P4-ATPase ATP8B1 and its chaperone TMEM30B within outer hair cells, demonstrating their enrichment in stereocilia, and convincingly demonstrate that loss of these proteins causes phosphatidylserine externalization, hair cell degeneration, and hearing loss in mouse models, phenocopying defects observed in TMC1 mutant mice with constitutive scrambling activity. While these findings establish lipid flippase pathways as critical for hair cell survival and auditory function, they also raise important questions about the precise mechanisms linking lipid asymmetry disruption to MET dysfunction and hair cell pathology.

Overall, the data convincingly support the conclusion that ATP8B1-TMEM30B flippase activity is required to maintain stereocilia lipid asymmetry and auditory function. The study substantially advances understanding of how lipid homeostasis intersects with MET. However, several points require clarification to ensure that localization claims and mechanistic interpretations are fully supported by the presented data.

Revisions considered essential by this reviewer are:

(1) Figure 1D.<br /> The authors should clarify how the qPCR data were normalized and specify the reference (housekeeping) genes used. This information is necessary to evaluate the robustness and comparability of the gene expression data.

(2) Figure 1F.<br /> The lack of F-actin staining at the hair cell base raises the possibility that the permeabilization conditions may have limited antibody access to certain membrane regions. This is especially important given that the authors used a gentle permeabilization agent such as saponin to preserve membrane integrity. Because the authors conclude that ATP8B1 and TMEM30B are localized "almost exclusively to OHC bundles and the apical membrane, with minimal staining in the remaining plasma membrane," (line 128). Including co-labeling with a plasma membrane marker or more comprehensive F-actin visualization of lateral and basal regions would help ensure that the restricted localization is biological rather than technical. In the absence of such controls, the localization claim may be somewhat overstated and should be tempered accordingly.

(3) Figure 7B.<br /> Although quantification of ATP8B1-HA intensity at the bundle appears similar between WT and Cib2 KO samples, the representative image suggests that some bundles lack detectable labeling. To better capture phenotype variability, it would be helpful to include an additional quantification showing the fraction or number of bundles with detectable ATP8B1-HA signal in Cib2 KO mice.

(4) Lines 346-349.<br /> The manuscript suggests that IHCs lack stereocilia-enriched P4-ATPases. However, this conclusion is not directly supported by the presented data. The authors should either provide supporting localization or expression data for other P4-ATPases or soften the statement to indicate that no stereocilia-enriched P4-ATPases were detected under the conditions examined.

Recommendations:

(5) The authors convincingly demonstrate that TMEM30B loss results in ATP8B1 mislocalization. While not essential to the central conclusions, examining TMEM30B localization in ATP8B1 KO hair cells would clarify whether this interdependence is reciprocal, as described for other P4-ATPase-CDC50 complexes.

(6) Lines 359-374.<br /> The discussion of Annexin V labeling is careful and balanced. This paragraph would benefit from referencing other studies that showed minimal Annexin V labeling in healthy P6 organ of Corti, reinforcing that robust PS externalization in the present study is pathological rather than developmental.

(7) Lines 392-399.<br /> The proposed feedback model linking MET activity and ATP8B1-TMEM30B localization is compelling. The discussion could be strengthened by noting that in TMC1/2 double knockout hair cells, PS externalization is not observed, consistent with the idea that flippase activity becomes critical specifically when scrambling occurs. The mislocalization observed in Cib2 KO hair cells further supports the coupling between TMC-mediated scrambling and flippase-mediated membrane restoration.

Reviewer #1 (Public review):

Summary:

This paper examines plasticity in early cortical (V1-V3) areas in an impressively large number of rod monochromats (individuals with achromatopia). The paper examines three things:

(1) Cortical thickness. It is now well established that early complete blindness leads to increases in cortical thickness. This paper shows increased thickness confined to the foveal projection zone within achromats. This paper replicates work by Molz (2022) and Lowndes (2021), but the detailed mapping of cortical thickness as a function of eccentricity and the inclusion of higher retinotopic areas is particularly elegant.

(2) Failure to show largescale reorganization of early visual areas using retinotopic mapping. This is a replication of a very recent study of Molz et al. but I believe, given anatomical variability, the larger n in this study, and how susceptible pRF findings are to small changes in procedure, this replication is also of interest.

(3) Connective field modelling, examining the connections between V3-V1. The paper finds changes in the pattern of connections, and smaller connective fields in individuals with achromatopsia than normally sighted controls, and suggests that these reflect compensatory plasticity, with V3 compensating for the lower resolution V1 signal in individuals with achromatopsia.

This is a carefully done study (both in terms of data collection and analysis) that is an impressive amount of work.

*Effects of eye-movements

The authors have carried out the eye-movement analyses I asked of them. Unfortunately, in 4 individuals they couldn't calibrate the eyetracker (it's impressive they managed in 10). I think this means that 4 of 13 (since a different participant was excluded from head motion) individuals weren't included in correlation analyses. Limiting the correlation analysis to individuals with better fixation has obvious issues. I'd recommend redoing (or additionally including) stats using non-parametric measures while classifying these 4 as having fixation instability of 3 (i.e. greater instability than the participant with the worst fixation who was successfully calibrated).

*Interpreting pRFs

The paper would be strengthened by a little more explicit clarity about what pRFs represent and how that affects their interpretation of their findings as plasticity vs. non-plasticity (I know the authors are aware of this, but I think it would be helpful for readers who are less experienced in pRFs). In the introduction it would be helpful to point out that pRFs represent the collective response of a large population of neurons, and as a result pRF estimates can vary depending on which population of neurons that stimulus drives.

For example, imagine for the sake of argument that rods only project to V1 neurons with larger receptive fields. If one measured pRFs in a control observer under phototopic vs. scotopic conditions one would see smaller pRFs in the photopic conditions. This wouldn't represent 'plasticity' - it would represent the fact that the firing neurons contributing to the pRF signal are a slightly different population because of a change in the stimulus content. This is of course exactly what you see in 2C. And indeed, the authors make this identical point ". In the non-selective condition, the smaller pRFs in controls are in line with the higher spatial resolution of the<br /> cone system, which is not active in the achromat group." But this point would be clearer if more of the conceptual underpinnings were made explicit in the introduction (or at this point in the paper).

Shifts in which population of neurons drive your pRFs can explain main of the more puzzling results in the paper without detracting from your main conclusions. For example, in 2D, I don't think it's differences in S/N driving your results (pRFs are at least theoretically meant to be robust to S/N). If smaller RFs 'drop out' under low luminance and these smaller RFs also tend to be more central, then one would expect the control results of 1D. And I think a similar argument might even be made for the smaller difference in the rod monochromats.

It would be possible to make the point of Figure 4B more simply if Figure 4B was replaced by additional Panels in Figure 2 simply showing V3 pRF sizes/eccentricity distributions. That would make the point that you don't see the same expansion in pRF sizes in V3 in a way that is just as clear, and is closer to the data.

*Interpreting cRFs

Similarly, I think the paper would be improved with more clarity about the underlying signal in CF modeling. Once again, I appreciate that the authors are familiar with this, but it will help the reader in interpretation. (And I do believe thinking carefully about this may alter your interpretations). CF receptive fields 'find' the region in V1 that best predict the V3 signal in a given voxel. In resting state this likely represents a combination of:

(1) visually driven signal - correlations that may or may not reflect connectivity but represent the fact that regions that represent the same region of visual space will be active at the same time.

(2) global bilaterally symmetrical signal consisting of enhanced correlations between iso-eccentric regions (Raemaekers et al., 2014), which may arise from vasculature that symmetrically stems from the posterior cerebral artery (Tong et al., 2013; Tong and Frederick, 2014).

(3) intrinsic neural fluctuations that are more strongly correlated between connected neurons. These are likely quite weak compared to the other contributions.

I think if you ignore 2, (which is not likely to differ between rod mono and controls) and model 1 and 3, you might well see shifts in CFs towards the boundary of the scotoma - essentially the CF's location will be biased towards the region of V1 that has stronger correlations - which = the region which has a visual signal.

I do find convincing the argument that you don't see the same shift in controls in the rod-selective condition. So I think the results of 4A are fine. But a little more clarity about 'what's under the hood' in CF modeling would be nice.

*Interpreting the relationship between pRFs and cRFs

So there's something here that confuses me. We are all agreed that V3 pRF sizes are similar across RM and control. V1 pRFs are larger in RM. It feels intuitive that smaller CFs would compensate but I can't make it make sense to myself when I think it through. Each pRF represents a combination of receptive field location scatter and bandwidth. You want to argue that eccentricity mapping looks pretty normal, so there's no reason to think increased rf scatter, and I can believe that (though I do think this assumption should be discussed explictly).

So far I think we agree.

But let's think about what drives a CF during visual stimulation ... Specifically lets think about 'the pRF of the CF' (the region of visual space represented by the cluster of voxels in the CF). If pRFs for individual voxels in V1 are big, then the pRF for the CF is also going to be large. But we know that pRFs for V3 are normal size. So, the V3 CF will 'find' a smaller number of voxels in V1, in order to try to find the 'correct sized' CF pRF. Note that this explanation is very similar to yours. But doesn't require ANY 'intrinsic' connectivity. It's really just assuming the whole thing is driven by the visual signal and the CF size is determined by the ratio of the pRF sizes in V3 vs. V1.

One possible solution would be to regress out the visual stimulus and redo this analysis based on the residuals.

Reviewer #1 (Public review):

Summary:

The paper presents a three-layered hierarchical model for simulating Drosophila larva locomotion, navigation, and learning. The model consists of a basic locomotory layer that generates crawling and turning using a coupled-oscillator framework, incorporating intermittency in movement through alternating runs and pauses. The intermediate layer enables navigation by allowing larvae to actively sense and respond to odor gradients, facilitating chemotaxis. The adaptive learning layer integrates a spiking neural network model of the Mushroom Body, simulating associative learning where larvae modify their behavior based on past experiences. The model is validated through simulations of free exploration, chemotaxis, and odor preference learning, demonstrating close agreement with empirical behavioral data. This modular framework provides a valuable advance for modeling of larva behavior.

Strengths:

Every modeling paper requires certain assumptions and abstractions. The main strength of this paper lies in its modular and hierarchical approach to modeling behavior, making connections to influential theories of motor control in the brain. The authors also provide a convincing discussion of the experimental evidence supporting their layered behavioral architecture. This abstraction is valuable, offering researchers a useful conceptual framework and marking a significant step forward in the field. Connections to empirical larval movement are another major strength.

Weaknesses:

While the model represents a conceptual advance in the field, some of its assumptions and choices fall behind state-of-the-art approaches. One limitation is the paper's simplified representation of larval neuromechanics, in which the body is reduced to a two-segment structure with basic neural control. Another limitation is the absence of an explicit neuromuscular control system, which would better capture the role of segmental central pattern generators (CPGs) and neuronal circuits in regulating peristalsis and turning in Drosophila larvae. Many detailed neuromechanical models, as cited by the authors, have already been published. These abstractions overlook valuable experimental studies that detail segmental dynamics during crawling and the larval connectome.

The strength of the model could also be its weakness. The model follows a subsumption architecture, where low-level behaviors operate autonomously while higher layers modulate them. However, this approach may underestimate the complexity of real neural circuits, which likely exhibit more intricate feedback mechanisms between sensory input and motor execution.

Reviewer #1 (Public review):

Summary:

The authors describe the results of a single study designed to investigate the extent to which horizontal orientation energy plays a key role in supporting view-invariant face recognition. The authors collected behavioral data from adult observers who were asked to complete an old/new face matching task by learning broad-spectrum faces (not orientation filtered) during a familiarization phase and subsequently trying to label filtered faces as previously seen or novel at test. This data revealed a clear bias favoring the use of horizontal orientation energy across viewpoint changes in the target images. The authors then compared different ideal observer models (cross-correlations between target and probe stimuli) to examine how this profile might be reflected in the image-level appearance of their filtered images. This revealed that a model looking for the best matching face within a viewpoint differed substantially from human data, exhibiting a vertical orientation bias for extreme profiles. However, a model forced to match targets to probes at different viewing angles exhibited a consistent horizontal bias in much the same manner as human observers.

Strengths:

I think the question is an important one: The horizontal orientation bias is a great example of a low-level image property being linked to high-level recognition outcomes and understanding the nature of that connection is important. I found the old/new task to be a straightforward task that was implemented ably and that has the benefit of being simple for participants to carry out and simple to analyze. I particularly appreciated that the authors chose to describe human data via a lower-dimensional model (their Gaussian fits to individual data) for further analysis. This was a nice way to express the nature of the tuning function favoring horizontal orientation bias in a way that makes key parameters explicit. Broadly speaking, I also thought that the model comparison they include between the view-selective and view-tolerant models was a great next step. This analysis has the potential to reveal some good insights into how this bias emerges and ask fine-grained questions about the parameters in their model fits to the behavioral data.

Weaknesses:

I'll start with what I think is the biggest difficulty I had with the paper. Much as I liked the model comparison analysis, I also don't quite know what to make of the view-tolerant model. As I understand the authors' description, the key feature of this model is that it does not get to compare target and probe at the same yaw angle, but must instead pick a best match from candidates that are at different yaws. While it is interesting to see that this leads to a very different orientation profile, it also isn't obvious to me why such a comparison would be reflective of what the visual system is probably doing. I can see that the view-specific model is more or less assuming something like an exemplar representation of each face: You have the opportunity to compare a new image to a whole library of viewpoints and presumably it isn't hard to start with some kind of first pass that identifies the best matching view first before trying to identify/match the individual in question. What I don't get about the view-tolerant model is that it seems almost like an anti-exemplar model: You specifically lack the best viewpoint in the library but have to make do with the other options. I sort of understand the reasoning that this enforces tolerance of viewpoint variability, but I'm not clear on whether or not this is a version of face familiarity and recognition that the authors think has an analog in human visual processing.

I do think that this model is interesting in terms of the differential tuning it exhibits, but don't find it easy to align with any theoretical perspective on face recognition. Specifically, do the authors think there is a stage of face processing in which tolerance as they've operationalized it in the model is extant? What I'm looking for is a concrete description of the circumstances that the authors are saying lead to this kind of model potentially being a meaningful analog of face recognition. For example, is the idea that one may become familiar with a face in some very limited set of viewpoints and then be presented with that face in other views?

Alternatively, if the authors prefer to say that they simply thought this was a nice exercise in terms of identifying a different model and that it may not be a meaningful proxy for face recognition. I think that's fine, to be clear! I just still don't see anything in the text that convinces me of the ecological validity of this version of view-tolerance.

Reviewer #1 (Public review):

Summary:

This brief piece by Swartz and colleagues outlines the complexities surrounding the choice of clinical specialty for physician-scientists. It is, in general, clear and well-written, and it will be useful to research-oriented medical students choosing a path and to the mentors who are guiding them.

Strengths:

The writing is clear. The points made are not profound, but they are important and will be of use to the intended audience.

Weaknesses:

I have only minor suggestions for improvement. There are some areas of redundancy where the article could be tightened up by consolidating.

Reviewer #1 (Public review):

This paper investigates how different learning curricula influence the way that humans piece together directly experienced transitions into a broader cognitive map. When adjacent learning trials were grouped within rows or columns of the map, subsequent navigation through the map was weaker than when adjacent learning trials came from disjoint spaces in the map. The authors speculate that the grouped curriculum resulted in mental fragmentation that made navigation across space more difficult later on.

This is an interesting paradigm that contributes useful new findings in the domain of map learning to the growing literature on curriculum learning. The evidence for a difference between conditions is highly compelling, but, as the authors are very transparent in acknowledging in the Discussion, the evidence for their proposed mechanism - mental fragmentation under grouped learning - is somewhat weak. The study thus presents an intriguing empirical result but not an ironclad mechanistic account.

An alternative - by their account, "less interesting" - explanation is that grouped learning was easier because trials in close succession had overlapping elements, and so participants were not trying as hard or as engaged. There is a literature on spaced (as opposed to massed) learning being better for subsequent memory because it increases retrieval effort. It seems very plausible that this could be going on here, and the control experiment reported in the supplement would not help to rule this out. This literature deserves some discussion.

The Introduction focuses entirely on literature showing advantages in grouped over intermixed learning, setting that up as the most well-motivated expectation from the literature. Upon finding the opposite, the Discussion then mentions that interleaving has been found to be useful in "applied domains", but then returns to how surprising this is in light of recent findings in the category learning literature. But there is a substantial earlier literature on interleaved vs blocked curricula in category learning, very often finding advantages for interleaving. See, e.g., Carvalho & Goldstone, 2015, for a review. There is also a paper showing interleaving advantages in associative inference, Zhou et al., 2023, JEP:G, which is very relevant to several of the discussion section paragraphs. Thus, the treatment of the prior curriculum learning literature is currently sparse.

Reviewer #1 (Public review):

Summary:

This work aims to elucidate the molecular mechanisms affected in hypoxic conditions causing reduced cortical interneuron migration. They use human assembloids as a migratory assay of subpallial interneurons into cortical organoids and show substantially reduced migration upon 24 hours hypoxia. Bulk and scRNA-seq shows adrenomedullin (ADM) up-regulation, as well as its receptor RAMP2 confirmed at protein level. Adding ADM to the culture medium after hypoxic conditions rescues the migration deficits, even though the subtype of interneurons affected is not examined. However, the authors demonstrate very clearly that ineffective ADM does not rescue the phenotype and blocking RAMP2 also interferes with the rescue. The authors are also applauded for using 4 different cell lines and using human fetal cortex slices as an independent method to explore the DLXi1/2GFP-labelled iPSC-derived interneuron migration in this substrate with and without ADM addition (after confirming that also in this system ADM is up-regulated). Finally, the authors demonstrate PKA - CREB signalling mediating the effect of ADM addition, and also lead to up-regulation of GABAreceptors. Taken together this is a very carefully done study on an important subject - how hypoxia affects cortical interneuron migration. In my view it would be of great interest for the readers of Elife.

Strengths:

Its strengths are the novelty and the thorough work using several culture methods and 4 independent lines.

Weaknesses:

The main weakness is that we dont know which interneuron subtypes are most affected by hypoxia and which may be rescued in their migration by ADM.

A further weakness is that the few genes confirmed to be regulated after hypoxia do not help determining which statistical cut-off can be considered reliable, given that they didn't compare strongly regulated versus weakly regulated genes.

Comments on revisions:

Unfortunately, the authors did not address my suggestions. While they show example stainings of interneuron subtypes, they do not show if Calretinin, calbinin or somatostatin+ interneurons are differentially affected by hypoxia or the rescue with ADM. I still consider this an important piece of information to add.

Reviewer #2 (Public review):

[Editors' note: This version was assessed by the editors. The authors have addressed a point raised by Reviewer #2, who thought the authors compared cells grown in low-serum and high serum conditions. This has been clarified in the latest version.]

In the manuscript Ruhling et al propose a rapid uptake pathway that is dependent on lysosomal exocytosis, lysosomal Ca2+ and acid sphingomyelinase, and further suggest that the intracellular trafficking and fate of the pathogen is dictated by the mode of entry. Overall, this is manuscript argues for an important mechanism of a 'rapid' cellular entry pathway of S.aureus that is dependent on lysosomal exocytosis and acid sphingomyelinase and links the intracellular fate of bacterium including phagosomal dynamics, cytosolic replication and host cell death to different modes of uptake.

A key strength is the nature of the idea proposed, while continued reliance on inhibitor treatment combined with lack of phenotype / conditional phenotype for genetic knock out is a major weakness.

In the previous version, the authors perform experiments with ASM KO cells to provide genetic evidence of the role for ASM in S. aureus entry through lysosomal modulation.

Reviewer #1 (Public review):

[Editors' note: The article has been improved and several points raised by the reviewers have now been addressed. The authors should ideally further improve the clarity of the figures and the description of the experimental methods. This is particularly important for an article discussing potential confounding factors.]

Summary:

This important article reveals that the Nora virus can colonize the intestinal cells of Drosophila melanogaster, where it persists with minimal immediate impact on its host. However, upon aging, infection, or exposure to toxicants, stem cell activation induces Nora virus proliferation, enabling it to colonize enterocytes. This colonization disrupts enterocyte function, leading to increased gut permeability and a significant reduction in lifespan. Results are convincing and hold significant import for the Drosophila community.

Strengths:

(1) Building on previous studies by Habayeb et al. (2009) and Hanson et al. (2023), this study highlights cryptic Nora virus infection as a crucial factor in aging and gut homeostasis in Drosophila melanogaster.

(2) Consistent with the oral route of Nora virus transmission, the study demonstrates that the virus resides in intestinal stem cells, with its replication directly linked to stem cell proliferation. This process facilitates the colonization of enterocytes, ultimately disrupting intestinal function.

(3) The study establishes a clear connection between stem cell proliferation and virus replication, suggesting that various factors - such as microbiota, aging, diet, and injury - can influence Nora virus dynamics and associated pathology.

(4) The experimental design is robust, comparing infected flies with virus-cured controls to validate findings.

Reviewer #2 (Public review):

This paper describes an analysis of a commercially available panel for a spatial transcriptomic approach and introduces a computational tool to predict potential off-target binding sites for the type of probe used in the aforementioned panel. The performance of the prediction tool was validated by examining a dataset that profiled the same cancer tissue with multiple modalities. Finally, a detailed analysis of the potential pitfalls in a published study communicated by the company that commercialized the spatial transcriptomic platform in question is provided, along with best practice guidelines for future studies to follow.

Strengths:

- The manuscript is clearly written and easy to follow.<br /> - The authors provide clean, organized, and well-documented code in the associated GitHub repository.

Comments on revision:

My impressions from the first round of review haven't really changed. I don't think the software tool is well developed, and failing to incorporate thermodynamics or consider the impact of alignment settings is a major weakness.

I do think the topical area is relevant. The inclusion of the Xenium /Hubmap data modestly strengthens the manuscript relative to the original submission.

Reviewer #1 (Public review):

Summary

Alpha oscillations have been previously proposed to shape the temporal resolution of visual perception, with a higher alpha frequency providing a finer resolution. This study goes beyond by investigating three additional processes that could influence joint visual temporal perception: the aperiodic neural signal, the integration of recent perceptual experience (serial dependence), and subjective confidence. To address their question, they developed a novel task where two Gabor patches oriented in opposite directions are presented in a continuous stream. This allows for testing for robust perceptual integration while avoiding bias from suboptimal perception. Behavioral analyses revealed an association between confidence and individual temporal integration thresholds, and demonstrated that serial dependence biases visual temporal integration as well as its associated confidence. EEG analyses first replicated the previous findings showing that faster IAF provides higher temporal resolution. Interestingly, the aperiodic neural signal was associated with both perceptual and temporal precision. Finally, the authors show that serial dependence is reduced in individuals with faster IAF and enhanced in participants exhibiting a stronger aperiodic component. Together, these findings highlighted that visual temporal integration arises from an interplay between alpha oscillations, the aperiodic signal, serial dependance and subjective confidence.

Strengths:

(1) The novel task proposed in the study represents a substantial improvement over the two-flash fusion task previously used to investigate the role of alpha oscillations in visual temporal perception.

(2) Serial dependence has attracted increasing interest in vision research in recent years. Testing whether recent visual inputs also influence temporal resolution is, therefore, a valuable and timely approach. In this regard, the authors provide evidence for a serial dependence effect.

(3) Although the functional role of brain oscillations has been extensively studied over the past decade, the role of the aperiodic neural signal has long been overlooked. This study revealed that the aperiodic component plays a role in perceptual precision and temporal resolution, thus providing evidence for an important role of the aperiodic neural signal.

(4) The mediation analysis demonstrates that the aperiodic and oscillatory neural components act independently, providing important insights for future studies aimed at understanding their respective role.

Weaknesses

It would have been valuable to record EEG continuously during the experiment to investigate how spontaneous alpha oscillations and aperiodic signal dynamically influence the temporal integration, serial dependance and confidence on a trial-by-trial basis.

Appraisal

The authors employed a novel and thoughtfully designed task, combined with appropriate analyses, to address their research question. Their results are convincing and provide strong support for their conclusions.

Impact

This study provides valuable insights into the role of the aperiodic neural signal in visual temporal integration. This is important because its contribution has likely been underestimated, and future research will likely uncover increasing evidence of its impact across multiple cognitive functions.

It was also very interesting to observe how alpha oscillations are associated with serial dependence and confidence, extending beyond their well-known role in visual temporal resolution. This opens intriguing avenues for future research on the functional role of alpha oscillations.

Reviewer #2 (Public review):

Summary:

The work presented by Zhang and coauthors in this manuscript presents the study of the neuropeptide corazonin in modulating the post-mating response of the brown planthopper, with further validation in Drosophila melanogaster. To obtain their results, the authors used several different techniques that orthogonally demonstrate the involvement of corazonin signalling in regulating the female post-mating response in these species.

They first injected synthetic corazonin peptide into female brown planthoppers, showing altered mating receptivity in virgin females and a higher number of laid eggs after mating. The role of corazonin in controlling these post-mating traits has been further validated by knocking down the expression of the corazonin gene by RNA interference and through CRISPR-Cas9 mutagenesis of the gene. Further proof of the importance of corazonin signaling in regulating the female post-mating response has been achieved by knocking down the expression or mutagenizing the gene coding for the corazonin receptor.

Similar results have been obtained in the fruit fly Drosophila melanogaster, suggesting that corazonin signaling is involved in controlling the female post-mating response in multiple insect species.

The study of the signalling pathways controlling the female post-mating response in insects other than Drosophila is scarce, and this limits the ability of biologists to draw conclusions about the evolution of the post-mating response in female insects. This is particularly relevant in the context of understanding how sexual conflict might work at the molecular and genetic levels, and how, ultimately, speciation might occur at this level. Furthermore, the study of the post-mating response could have practical implications, as it can lead to the development of control techniques, such as sterilization agents.

The study, therefore, expands the knowledge of one of the signalling pathways that control the female post-mating response, the corazonin neuropeptide. This pathway is involved in controlling the post-mating response in both Nilaparvata lugens (the brown planthopper) and Drosophila melanogaster, suggesting its involvement in multiple insect species.

The study uses multiple molecular approaches to convincingly demonstrate that corazonin controls the female post-mating response. The data supporting the main claim of the manuscript are solid and convincing.

Reviewer #1 (Public review):

Summary:

This paper leverages 7T fMRI data from the Natural Scenes Dataset to investigate whether retinotopic coding, the position-selective organization of visual response structures, spontaneous resting-state interactions between the Default Network (DN) and the Dorsal Attention Network (dATN). Using individualized network parcellations and population receptive field (pRF) modeling, the authors show that DN voxels can be split into two subpopulations based on their response to visual stimulation: those with position-specific positive BOLD responses (+pRFs) and those with position-specific negative BOLD responses (-pRFs). Critically, these subpopulations relate differently to the dATN during rest: -pRFs are anticorrelated with the dATN, +pRFs are positively correlated, and non-retinotopic DN voxels show no coupling. The anticorrelation (and positive correlation) is enhanced when DN and dATN voxels share visual field preferences. An event-triggered analysis suggests that retinotopic coding shapes both "top-down" (DN-initiated) and "bottom-up" (dATN-initiated) spontaneous activity transients, supporting the claim that the retinotopic scaffold is intrinsic to the DN. These findings challenge the prevailing view of global DN-dATN antagonism and suggest retinotopic coding as an organizing principle for cross-network communication.

Strengths:

The central finding that what looks like network-level independence between DN and dATN decomposes into structured, bivalent interactions organized by voxel-level visual field preferences is a compelling demonstration that macro-scale network descriptions can hide meaningful substructure. The logic of the analysis is clean: pRF properties are estimated from retinotopic mapping data and then used to predict resting-state coupling in completely independent scanning sessions. This cross-session, cross-modality design rules out many circularity concerns.

The use of individualized multi-session hierarchical Bayesian parcellation (Kong et al.) to define DN and dATN boundaries within each subject is the right methodological choice for this question. Network boundaries in posterior cortex, where DN and dATN interdigitate most closely, vary considerably across individuals, and group-average approaches would introduce exactly the kind of misassignment that would most confound the result.

The matched-vs-random pRF analysis is well-controlled. The authors demonstrate that cortical distance between matched and randomly-matched dATN pRFs does not differ, effectively ruling out spatial proximity on the cortical surface as a confound. tSNR controls further show that signal quality differences do not drive the effect.

The event-triggered analysis (Figure 3) is creative and adds genuine value. Showing that retinotopically-specific coupling persists during DN-initiated activity transients, not only dATN-initiated ones, is the key piece of evidence for the claim that the code is intrinsic to the DN rather than passively inherited through bottom-up visual drive.

The result is observed consistently across all individual participants, which provides strong evidence for the robustness of the qualitative pattern despite the small sample size inherent to densely-sampled designs.

Weaknesses

(1) The nature of negative pRFs requires more scrutiny

The entire interpretive framework depends on treating negative pRFs in the DN as genuine position-selective neural responses (suppression). However, negative BOLD signals are well known to arise from non-neural sources, specifically, vascular stealing (where activation in nearby tissue diverts blood from adjacent voxels) and macrovascular draining vein effects that produce spatially displaced signal inversions. These concerns are amplified at 7T, where T2*-weighted GE-EPI carries substantial macrovascular weighting. The DN and dATN interdigitate extensively in the posterior cortex, often within millimeters. A negative pRF in a DN voxel adjacent to a positive dATN voxel could, in principle, reflect the hemodynamic shadow of its neighbor rather than an independent neural response.

The spatial dispersion control (matched vs. random pRFs have similar cortical distribution) is valuable but addresses long-range confounds, not *local* hemodynamic crosstalk. The reliability of sign and center position across runs is reassuring but does not exclude a vascular origin, as vascular architecture is itself stable across sessions. I would encourage the authors to test whether the matched-vs-random effect survives exclusion of voxels near large pial vessels (identifiable from T2* contrast or the venograms available in the NSD). These analyses would not be dispositive, but they would meaningfully strengthen the neural interpretation.

(2) Amount of retinotopic mapping data and choice of pRF pipeline

The NSD includes 6 runs of retinotopic mapping (~5 minutes each; 3 bar-aperture, 3 wedge/ring). The authors use only the 3 bar-aperture runs (~15 minutes total per subject) and fit their own pRFs using AFNI's 3dNLfim procedure, rather than using the pRF estimates provided as part of the NSD release (which were fitted using the analyzePRF toolbox with all 6 runs).

Fifteen minutes of bar data is quite limited for reliable voxel-wise pRF estimation, especially in regions far from the early visual cortex, where signal-to-noise is inherently lower. Standard recommendations for robust pRF mapping in higher-order regions generally suggest substantially more data. The variance-explained threshold is close to the noise floor by design, meaning that a non-trivial number of the "retinotopic" DN voxels may be poorly estimated. Given that the core analyses depend on both the sign and the center position of these pRFs, the limited data is a significant concern.

The authors do not explain why they chose to re-fit pRFs rather than use the NSD-provided estimates. If the motivation was methodological (e.g., the NSD pRF pipeline does not readily yield signed amplitude, or the bar-only fits were judged more appropriate for detecting negative responses), this should be made explicit. If the NSD-provided pRFs can reproduce the key findings, this would substantially increase confidence in the results. If they cannot, that divergence itself would be important to understand. I would ask the authors to address this choice and, if feasible, to report whether the core results replicate using the NSD-provided pRF estimates and/or whether using all 6 runs of retinotopy data changes the findings.

(3) pRF model adequacy for the Default Network

The isotropic Gaussian pRF model was developed for and validated in early and mid-level visual cortex, where it captures the dominant spatial selectivity of neuronal populations. In DN voxels where the model explains comparatively little variance, it is less clear that the model is capturing the right quantity. Specifically, the negative pRFs could conceivably be described by a model with a dominant suppressive surround (e.g., a difference-of-Gaussians model), in which what appears as a "negative pRF" in the standard model is actually the surround component of a center-surround mechanism whose center is poorly resolved. This distinction matters: a genuine inverted code (negative center response) implies a qualitatively different computation than inherited surround suppression from nearby visual cortex.

The authors should consider discussing why the standard model is sufficient for the questions asked, or ideally, testing whether the sign distinction survives under alternative pRF model specifications.

(4) Interpreting resting-state transients as top-down vs. bottom-up

The event-triggered analysis labels high-amplitude DN pRF activations as "top-down events" and dATN activations as "bottom-up events." This is a reasonable inference given experience-sampling studies showing that rest involves alternation between internal and external attention, but it remains an inference. Without concurrent experience sampling, eye-tracking, or physiological monitoring, we cannot establish that a spontaneous DN transient reflects memory retrieval or internally-directed thought rather than a global arousal fluctuation. Similarly, dATN transients during rest could reflect covert shifts of spatial attention to remembered or imagined locations rather than bottom-up processing per se. I would ask the authors to soften this framing or to discuss what additional data would be needed to validate the top-down/bottom-up attribution.

(5) The "retinotopic code" vs. "visual field bias" distinction

The paper uses the language of a "retinotopic code" throughout and correctly distinguishes this from a "retinotopic map," noting that DN voxels do not form a continuous topographic representation on the cortical surface. This distinction deserves greater emphasis. In vision science, retinotopic maps carry computational significance through their topographic continuity and relationship to cortical wiring. A distributed collection of voxels with coarse visual field preferences but no cortical topography is a fundamentally different organizational feature. Recent reviews have drawn an explicit distinction between *retinotopic maps* and *visual field biases* (Groen, Dekker, Knapen & Silson, TiCS 2022), and the present findings may be more accurately characterized as the latter. Perhaps the authors think that the distinction is merely a signal-to-noise distinction, in which case I would invite them to clearly speak to this interpretation. In any case, this is not a criticism of the findings themselves, but clarity on this point would prevent conflation of two different organizational principles and would help position the work for both the vision and network neuroscience communities.

Reviewer #1 (Public review):

Summary:

Garcia-Alcala, Kratz and Cluzel investigate to what extent our understanding of bacterial physiology in bulk experiments can be applied to single-cell observations. They find that intrinsic noise may be powerful enough to even inverse the trends found in the bulk. The authors hypothesize that the asymmetric distribution of ribosomes to daughter cells during cell division plays the dominant role in the intrinsic noise and is able to generate the observed phenomenon. They do not show it directly, but the data and its agreement with the model are sufficient to support this claim.

Strengths:

The experimental part is convincing: the positive correlation between the elongation rate and promoter activity of unnecessary protein is clear, as well as the negative correlation between the mean values while changing the promoter strength. This was demonstrated in both rich and poor media. The causality between the growth rate and the promoter activity was shown using the negative lag time of the cross-correlation function. A simple, reasonable model accounts well for the data. This paper demonstrates an interesting phenomenon and provides a plausible theory for it, advancing our understanding of bacterial physiology on the single-cell level.

Weaknesses:

(1) Mean-reversion timescales were assumed to be longer than the simulation time and much longer than the cell cycle time. It is not clear whether the results are robust in case mean-reversion timescales become of the order of the cell-cycle or smaller. If not, is there an argument for such practically infinite reversion timescales?

(2) It is not easy to understand the simulation part unless one reads Ref. [14]. k(t) is assumed Equation (1) from Reference [14]? Is it crucial that the ribosome noise appears only at the division? The ribosome noise strength \sigma_R=0.06 - is it lower or higher than the naively expected binomial division? Also, a more intuitive explanation of the Simpson paradox would help the reader.

(3) It would be useful for the reader to see the raw data and not only the filtered one to appreciate the measurement noise level.

(4) Negative lag time of the cross-correlation function is visible, but consider adding a statistical test for it.

(5) Can you make similar cross-correlation plots using the model? Can you infer by using it, whether the data agrees better with the assumption that ribosomal noise appears only at division or continuous fluctuations during the cell cycle?

Reviewer #1 (Public review):

Summary:

Effective decision-making in dynamic environments requires the brain to flexibly adjust how sensory evidence is accumulated over time, a process often modeled as an adaptive "leak." McGaughey and Gold propose that this flexibility is not solely a property of downstream integrators but is also supported by stimulus-specific sensory adaptation in the middle temporal area (MT). By recording single-unit activity in rhesus macaques during a motion direction-discrimination task, the authors found that more rapidly changing environments lead to reduced sensory encoding and discriminability in MT, which they argue accounts partially for a "leakier" integration. Furthermore, the study identifies pupil-linked arousal as a parallel, independent mechanism contributing to this adaptive process.

Strengths:

The study addresses an important question in cognitive neuroscience by exploring the neural substrates of perceptual flexibility. A major strength is the novel focus on how sensory adaptation, rather than just downstream integration, contributes to behavioral changes in dynamic environments. By shifting the perspective toward the encoding stage, the authors provide a more comprehensive account of how the brain manages evidence accumulation. This conceptual advance is supported by a rigorous experimental approach that combines human-like psychophysics with large-scale single-unit recordings in the middle temporal area (MT) and pupillometry.

Weaknesses:

(1) Alternative mechanisms for performance differences

The authors assume that the difference in performance between the low-switch (LS) and high-switch (HS) frequency conditions is explained by a change in the "leakiness" of integration. However, several other mechanisms could potentially explain this effect:

(i) Temporal Uncertainty: Integration might start later in the HS condition, leading to lower performance.

(ii) Reduced Efficiency: Integration could be less efficient in the HS condition (i.e., lower signal-to-noise ratio) without a change in the leak parameter itself.

(iii)Evidence Contamination: Motion information from the adapting stimulus in the HS condition may be integrated rather than ignored, which might be the case since the transition from the adapting to the test stimulus is not externally cued.

To distinguish between these alternatives, I suggest two possible analyses. First, a formal model comparison could be performed, though I acknowledge this may be inconclusive in the absence of response-time data. Second, an analysis of motion energy kernels could be revealing; the leak hypothesis makes the specific prediction that for long test stimuli, early samples should contribute more to the choice in the LS condition than in the HS condition, relative to late samples.

(2) Independence of neural and pupil-linked signals


The authors take the lack of session-wise correlation between context-dependent contributions from neural and pupil terms as evidence that these two signals provide independent contributions to the behavioral effect. However, could this lack of correlation simply be a result of high variability or noise in these estimates? The data shown in Figure 7B suggests that measurements are very noisy, which might obscure a potential relationship.

Reviewer #1 (Public review):

Summary:

This manuscript aims to differentiate between foveal and peripheral attentional mechanisms in visual and frontal brain regions in monkeys engaged in a free-gaze visual search task.

Strengths:

The manuscript is clearly written, the question is important, and the behavioral task is interesting.

Weaknesses:

I have two major concerns.

(1) The authors interpret divergence in neural responses to target vs nontarget as attention. But it is not. The subject has to attend to both target and nontarget stimuli to determine the stimulus category and thereby decide on the next action. Thus, divergence between target and nontarget responses could reflect categorical discrimination, but I am not sure this can be interpreted as attentional modulation. While it may be tempting to suggest that finding a stimulus of a specific category is "feature attention", analogous to, e.g., attending to the red stimulus, I don't believe this is correct. For the former, the animals have to attend to a stimulus, and examine the stimulus to determine the stimulus category, unlike a simpler discrimination, which may pop out. Given this, I am unconvinced that the interpretations in this manuscript are valid.

(2) Regarding the RF classification of foveal and peripheral RFs for IT and PFC, prior work suggests that neurons in IT cortex (especially AIT) and PFC have RFs that largely include the foveal visual field. So, it would be important to include figures that show the RFs of neurons classified as foveal versus peripheral for all three areas.

Reviewer #1 (Public review):

Summary:

This work presents a flexible spike-sorting framework that allows users to run, swap, and benchmark individual modules commonly used in spike sorting. The paper argues and demonstrates that "opening the black box" is essential for understanding which components drive performance differences and for making progress toward more accurate and transparent spike sorting.<br /> Using this modular benchmarking pipeline, the work identifies electrode drift as a primary bottleneck for accurate sorting and introduces an end-to-end sorter ("Lupin") that combines the best-performing modules and is reported to outperform existing spike-sorting packages on their benchmark.

Overall, this is a strong tool/resource contribution with clear potential to accelerate spike-sorting development and enable more rigorous comparisons. However, several claims, particularly around Lupin's or individual modules' superiority, are not yet supported robustly enough for the strength of the conclusions stated.

Strengths:

This work has high community value and practical utility. The effort to make benchmarking and spike sorting modules accessible and standardized is substantial and likely to be broadly useful.<br /> Treating spike sorting as a set of interchangeable modules is a useful approach to some extent, and it enables targeted improvements rather than 'new sorters' popping up, which are difficult to fully understand.

Implementing this resource within SpikeInterface, an already widely used tool, will facilitate uptake and community contributions.

Overall, I am positive about this manuscript as a resource paper. The core framework is compelling and timely.

Weaknesses:

(1) The main concern is the limited support for the claim that 'Lupin' and individual modules' outperform existing spike sorters.

(2) Evidence is primarily from a single benchmark based on an intentionally simplified simulation. While the authors discuss the trade-offs between simulated and real data, the current evaluation does not provide enough diversity to justify claims of superiority.

(3) While improving individual modules that run in a serial fashion could aid overall spike sorting performance, acknowledging that some end-to-end sorters work in an iterative fashion across multiple of these modules would be fair. Perhaps the optimal spike sorter is not a serial set of modules.

(4) There is also a risk of benchmark overfitting. A modular approach makes it easy to select components that excel on specific benchmarks (or a specific project's data characteristics) without generalizing.

Concrete ways to strengthen this work:

(1) Evaluate on multiple simulation regimes, consider adding at least one biophysically detailed simulation, benchmark on multiple probe-geometries with neurons also clustered in different depth profiles (as this will affect drift solutions), and provide real-data validation. Even without full ground truth, real-data can be evaluated with expert curation, functional validation (e.g., refractory violations, quality metrics, unit waveform consistency), agreement across sorters, and consistency across time.

(2) Related to real-data applicability, it is also important to acknowledge that modulatory approaches can enable overfitting to the needs of individual projects. Without real-data benchmarking (or benchmark diversity), it is unclear how the framework will guide users towards generalizable 'best practices' rather than optimized configurations that work for their specific conditions.

Reviewer #1 (Public review):

Summary:

The manuscript by Yang, Wang, and Cléry presents a lightweight pipeline for real-time identification of common marmosets in a laboratory setting. Models were trained and evaluated on data derived from a family of three closely related adults and a set of juvenile twins. Freely moving animals entered an enclosed space fixed to the housing cage door, which permitted the entry of individual animals for data acquisition. Utilizing YOLOv8-nano, identification was improved through the introduction of uniquely colored collar beads. Analyses of facial similarity showed close morphological relatedness amongst individuals and highlighted the need for highly discriminative classification. Overall, the authors offer a framework for identity tracking that prioritizes real-time inference. The authors demonstrate that combining facial detection with visual markers enables adequate identity assignment under controlled laboratory conditions with minimal cross-individual misclassification.

Strengths:

(1) The proposed pipeline offers a solution for real-time identity tracking in common marmosets. Its lightweight design enables deployment across a wide range of hardware configurations. Furthermore, if similar strategies are employed, this methodology is likely adaptable for other species with minimal modification.

(2) Evaluation of closely related individuals provides a necessary stress test for the discrimination of facial identity tracking.

Weaknesses:

(1) The pipeline's reliance on controlled animal isolation and small visual markers raises questions about the approach's generalizability to unconstrained multi-animal environments. The provided confusion matrices (Figures 6-8) indicate that the most common misclassifications are background-related, possibly suggesting that detection specificity is the primary source of error. All things considered, these findings raise concerns about performance in its use in socially dynamic and visually complex environments.

(2) The manuscript claims performance comparable to that of human experimenters but provides no explicit evidence to support these claims. While it is plausible that human experimenters may be less accurate in facial recognition tasks involving closely related marmosets, the authors don't provide evidence. Moreover, while that might be the case, the color-coded beads provide a salient identity cue for the model, which complicates the interpretation of this comparison grounded in facial recognition.

Reviewer #1 (Public review):

In this manuscript, the authors aim to determine the ligand on Plasmodium falciparum-infected erythrocytes for the NK cell integrin, LFA-1, following up on previous evidence that LFA-1 is important for immune cell-mediated recognition of iRBCs.

They start by incubating LFA-1 with iRBCs and show by flow analysis that a substantial population of these iRBCs binds to the LFA-1 (Figure 1C). They do conduct the control with uninfected RBCs, but put this in the supplementary material. As this is a critical control, I think that it should be moved to Figure 1C as it is essential to allow interpretation of the iRBC data. The authors also do not state which strain of P. falciparum they used (line 144). This is critical information as different strains have different variant surface antigens and should be included. With these changes, this data seems convincing.

They next incubated LFA-1 with the iRBCs, cross-linked and conducted a pulldown, identifying GP130 as a binding partner. Using cross-linkers is a dangerous strategy as it risks non-specific cross-linking. Did they try without cross-linking and find an interaction?

They raised antibodies to PfGBP and showed IFA, which reveals that these antibodies stain iRBCs (Figure 2Ciii). This experiment lacks a critical control of uninfected RBCs, which needs to be included to show that the staining is specific. Without this, it is not possible to conclude that there is iRBC-specific staining with PfGBP.

They then conduct a pulldown using LFA-Fc, which does show GP130 only in the presence of the LFA-Fc, but not when empty beads are used. This is convincing. BLI measurements are also used to study this interaction (Figure 2Ci). The BLI data is presented in such a way that any association phase is obscured by the y-axis, which makes it impossible to know whether there is binding here. I think that the data needs to be shown with some baseline before the addition of the ligand so that the association can be seen. The data is also a bit messy with a downward drift and the curves showing different shapes, for example, with the 1.0uM curve seeming to have a different association rate. Also, is this n=1? I think that this data needs to be repeated and replicated. As this is the only data which shows a direct interaction between LFA1 and GBP, as pulldowns are done with lysates, which might mean bridging components. I think that it is important to repeat the BLI or use additional biophysical methods to assess binding, to obtain more convincing data.

The authors next do some modelling of the putative complex. This is done by homology modelling and docking, which is not the most up-to-date method and is overinterpreted. Personally, I would remove this data as I did not find it convincing, and it is not important for the story. If the authors wish to include it, then I think that they should validate the modelling by mutagenesis to show that the residues which the models indicate might bind are involved in the interaction.

They next made GP130 and tested the binding of this to THP-1 cells, which are often used as a model for macrophages. They observe greater binding of PfGBP-Fc to these cells when compared with hIgG and show that LFA-1 siRNA reduces this binding. I was a little confused about how the flow plots related to the graph in the bottom right corner of Figure 3Bii. In the flow plots, hIgG control shows 12.8% of cells in the gated region, while the unstained cells has 5.63%, but the MFI data shows a decrease in binding for hIgG vs unstained cells. How is this consistent? Also, the siRNA reduces the number of cells in the gated region from 66.6% to 25.9%, which is still substantially more that 5.63% in the unstained control. This also doesn't seem quite consistent with the MFI data. Could the authors explain this? Also, perhaps an additional experiment would be to add soluble LFA-1 into this assay as an additional control to determine whether this blocks PfGBP binding to the THP-1 cells? It could be that there are additional mechanisms of binding which indicate why the siRNA has a partial effect. The same is true for the NK cell experiments in Figure 3Ci, in which the siRNA has a partial effect. The authors also test binding to HEK, HepG2 and 'stem' cells and claim 'only background levels of binding', but in each case, there is more binding to these cells by PfGBP-Fc than by hIgG, albeit less than in THP-1 and NK cells. Why have the authors decided that these increases are not significant? All in all, these experiments do indicate a role for the GBP-LFA1 interaction in the binding of immune cells to iRBCs, but perhaps not as absolutely as is suggested.

The authors next produce CHO cells with PfGBP on the surface. These cells bind to LFA-1 specifically. When these cells were incubated with primary NK cells, they did see increases in activation markers, which were reduced by the addition of anti-CD11a, suggesting these to be specific. They also conduct the same experiment with anti-GBP with iRBCs, but this is in a different figure. It would be easier for the reader if Figure 5B were in the same figure as Figure 4B, as it is related data using the same method. I found this data convincing, showing that the LFA1:GBP interaction does contribute to immune cell recognition and activation.

The authors next conduct an experiment in which they assess parasite growth in the presence of NK cells and in the presence of anti-GBP. They use Heochst staining as a measure of parasite growth and claim that NK cells reduce the number of parasites, but that anti-GBP abolishes this effect (Figure 5A). I found this experiment very unconvincing as there are small effects and no demonstration of significance. More commonly used approaches to study parasite growth are lactate dehydrogenase GIA assays or calcein-AM labelling. I did not find this experiment convincing and would either remove or supplement with additional data using a more robust assay, with repeats and tests of statistical significance.

In summary, the authors present a set of data which comes together to indicate an interaction between LFA1 and PfGBP on the Plasmodium-infected erythrocyte surface. Pulldown studies show convincingly that these two proteins co-precipitate, and BLI data suggest that this is direct. Also convincing is that NK cell activation can be reduced using antibodies against either LFA1 or PfGBP, indicating that this interaction does play a role in immune cell recognition of iRBCs.

Reviewer #1 (Public review):

Summary:

This study provided key experimental evidence for the "Solstice-as-Phenology-Switch Hypothesis" through two temperature manipulation experiments.

Strengths:

The research is data-rich, particularly in exploring the effects of pre- and post-solstice cooling, as well as daytime versus nighttime cooling, on bud set timing, showcasing significant innovation. The article is well-written, logically clear, and is likely to attract a wide readership.

Comments on revisions:

This is the second round of review, and I am generally very satisfied with the authors' revisions. However, a few detailed issues still require attention:

The authors identified the summer solstice (June 21) as a phenological "switch point", but the flexibility of this switch point remains poorly understood. A more precise explanation of what "flexibility" means in this context is needed, along with a description of the specific experimental results that would demonstrate this flexibility.

The experiment did not directly measure the specific date of the phenological switch point. Instead, it was inferred by comparing temperature effects before and after the solstice. The manuscript should clearly state that this switch point remains an inferred conceptual node rather than a directly measured variable.

In Experiment 1, the effect of bud type (terminal vs. lateral) was inconsistent across the overall model and the different leafing groups. The authors should provide a more thorough discussion of potential reasons for this inconsistency. In addition, the statistical model for Experiment 1 indicates that the measured variables (summer cooling and leaf emergence date) explain only 23.4% of the variation in bud formation timing. This leaves over 76% of the variation unexplained, suggesting that other important factors are involved. The discussion should address this limitation in greater depth, moving beyond a focus on the measured variables.

Reviewer #1 (Public review):

Naim et al. use genetically engineered mouse models and tissue culture cell lines to investigate the role of the SLAP adaptor protein in colonic epithelium and colon tumour formation. The SLAP adaptor protein is known to be a negative regulator of tyrosine kinase signaling in hematopoietic cells, but its role outside the immune system is less well defined. Here, the authors use genetically engineered SLAP-deficient mice, tissue-specific SLAP KO, and colonic organoids to demonstrate that SLAP is expressed in cells of the colonic epithelium, where it acts as a cell-autonomous regulator of proliferation and differentiation. In addition, they provide biochemical evidence that loss of SLAP expression in cultured colonic organoids results in increased Src family kinase activity and global tyrosine phosphorylation, consistent with its known role as a suppressor of tyrosine kinase activity in immune cells. Consistently, treatment with an SRC kinase inhibitor inhibited the growth of SLAP-deficient organoids. These data provide solid evidence of a cell-autonomous role of SLAP in the colonic epithelium.

This work would be improved by further description and interpretation of the SLAP expression pattern shown in the constitutive and tissue-specific KO to further support the conclusions made. In Supplementary Figure 1, magnification of the colon epithelium areas with SLAP expression shown by b-gal and anti-SLAP staining, highlighting regions of interest, would better support the conclusions regarding SLAP expression in specific regions of the colon epithelium. In Supplementary Figure 1B, the authors should indicate that the SLAP staining referred to is epithelial and in resident immune cells, as is mentioned in the text. Also, magnification of the boxed area of LRG5 staining in Figure 1 would improve this figure.

Using a chemically induced model of colitis-associated cancer, the authors demonstrate that inactivation of SLAP shows a trend toward increased tumor formation (though this did not reach significance) as well as increased Src family kinase activity within tumors. Tumor spheres from SLAP-deficient animals showed enhanced growth that was suppressed by treatment with a Src family kinase inhibitor. Of note, the latter effect was specific to SLAP-deficient tumor spheres. These observations are convincing and support the authors' conclusion that SLAP has a tumor suppressor role in CRC through inhibition of SFK signaling.

Mechanistically, elevated expression of the RTK, EphB2, was detected in immunoblots of SLAP KO colonic crypts, while overexpression of SLAP in CRC cell lines downregulated EphB2 protein levels. Using an EPHB2 inhibitor, the role of EPHB2 in the growth of SLAP-deficient colonic organoids was demonstrated. While these data generally support the authors' conclusion that SLAP limits colonic organoid growth by downregulating RTKS such as EphB2 and downstream Src family kinase activity, they do not show which cell types/regions in the colonic epithelium have increased EPHB2 protein and how this relates to SLAP and phospho-SRC expression, as shown in Figure 1 and Figure S1 immunocytochemistry. The expression of EphB2 and its role in colonic tumorsphere growth were not investigated.

Overall, this work provides evidence of SLAP adaptor function in restricting tyrosine kinase signaling in the colonic epithelium, and suggests that loss of SLAP expression could promote tumorigenesis in this context.

Reviewer #1 (Public Review):

[Editors' note: This version has been assessed by the Reviewing Editor without further input from the original reviewers. Given the time elapsed since the original data collection, the authors have addressed the previous concerns by providing a more nuanced discussion of their results and acknowledging the limitations of the study to ensure the conclusions are supported by the existing data.]

Throughout the paper, the authors do a fantastic job of highlighting caveats in their approach, from image acquisition to analysis. Despite this, some conclusions and viewpoints portrayed in this study do not appear well-supported by the provided data. Furthermore, there are a few technical points regarding the analysis that should be addressed.

(1) Analysis of signaling traces

- Relevance of "modeled signaling level": It is not clear whether this added complexity and potential for error (below) provides benefits over a more simple analysis such as taking the derivative (shown in Figure 3C). Could the authors provide evidence for the benefits? For example, does the "maximal response" given a simpler metric correlate less well with cell fate than that calculated from the fitted response?

- Assumptions for "modeled signaling level": According to equation (1) Kaede levels are monotonically increasing. This is assumed given the stability of the fluorescent protein. However, this only holds for the "totally produced Kaede/fluorescence". Other metrics such as mean fluorescence can very well decrease over time due to growth and division. Does "intensity" mean total fluorescence? Visual inspection of the traces shown in Figure 2 suggests that "fluorescence intensity" can decrease. What does this mean for the inferred traces?

- Estimation of Kaede reporter half-live: It is not clear how the mRNA stability of Kaede is estimated. It sounds like it was just assessed visually, which seems not entirely appropriate given the quantitative aspects of the rest of the study. Also, given that Shh signaling was inhibited on the level of Smoothened, it is not obvious how the dynamics of signaling shutdown affect the estimate. Most results in Figure 7 seem to be quite robust to the estimate of the half-live. That they are, might suggest that the whole analysis is unnecessary in the first place. However, not all are. Thus, it would be important to make this estimate more quantitative.

(2) Assignment of fates and correlations

- Error estimate for cell-type assignment: Trying to correlate signaling traces to cell fate decisions requires accurate cell fate assignment post-tracking. The provided protocol suggests a rather manual, expert-directed process of making those decisions. Can the authors provide any error-bound on those decisions, for example comparing the results obtained by two experts or something comparable? I am particularly concerned about the results regarding the higher degree of variability in the correlation between signaling dynamics and cell fate in the posterior neural tube. Here, the expression of Olig2 does not seem to segregate between different assigned fates, while it does so nicely in the anterior neural tube. This would suggest to me that cells in the posterior neural tube might not yet be fully committed to a fate or that there could be a relatively high error rate in assigning fates. Thus, the results could emerge from technical errors or differences in pure timing. Could the authors please comment on these possibilities?

- Clustering and fates: One approach the authors use to analyze the correlation between signaling and fate is clustering of cell traces and comparison of the fate distributions in those clusters. There is a large number of clusters with only single traces, suggesting that the data (number of traces) might not be sufficient for this analysis. Furthermore, I am skeptical about clustering cells of different anterior-posterior identities together, given potential differences in the timing of signal reception and signaling. I am not convinced that this analysis reveals enough about how signaling maps to fate given the heterogeneity in traces in large clusters and the prevalence of extremely small clusters.

- Signaling vector and hand-picked metrics: As an alternative approach, that might be better suited for their data, the authors then pick three metrics (based on their model-predicted signaling dynamics) and show that the maximal response is a very good predictor of fate for different anterior-posterior identities. Previous information-theoretic analysis of signaling dynamics has found that a whole time-vector of signaling can carry much more information than individual metrics (Selimkhanov et al, 2014, PMID: 25504722). Have the authors tried to use approaches that make use of the whole trace (such as simple classifiers (Granados et al, 2018, PMID: 29784812), or can comment on why this is not feasible for their data? The authors should at least make clear that their results present a lower bound to how accurately cells can make cell-fate decisions based on signaling dynamics.

(3) Consequences of signaling heterogeneity

The authors focus heavily on portraying that signaling dynamics are highly variable, which seems visually true at first glance. However, there is no metric used or a description given of what this actually means. Mainly, the variability seems to relate to the correlation between signaling and fate. However, given the data and analysis, I would argue that the decoding of signaling dynamics into fate is surprisingly accurate. So signaling dynamics that seem quite noisy and variable by visual inspection can actually be very well discriminated by cells, which to me appears very exciting.

Indeed, simple features of signaling traces can predict cell fate as well as position (for anterior progenitors). Given that signaling should be a function of position, it naively seems as if signaling read-out could be almost perfect. It might be interesting to plot dorsal-ventral position vs the signaling metrics, to also investigate how Shh concentration/position maps to signaling dynamics, this would give an even more comprehensive view of signal transmission.

There remains the discrepancy between signaling traces and fate in the posterior neural tube. The authors point towards differences in tissue architecture and difficulties in interpreting a "small" Shh gradient. However, the data seems consistent with differences in timing of cell-fate decisions between anterior and posterior cells. The authors show that fate does initially not correlate well with position in the posterior neural tube. So, signaling dynamics should likely also not, as they should rather be a function of position, given they are downstream of the Shh gradient. As mentioned above, not even Olig2 expression does segregate the assigned fates well. All this points towards a difference in the time of fate assignment between the anterior and posterior. Given likely delays in reporter protein production and maturation, it can thus not be expected that signaling dynamics correlate better with cell fate than the reporter "83%". Can the authors please discuss this possibility in the paper?

Thus, while this paper represents an example of what the community needs to do to gain a better understanding of robust patterning under variability, the provided data is not always sufficient to make clear conclusions regarding the functional consequences of signaling dynamics.

Reviewer #2 (Public review):

Summary:

Almansour et al., investigate whether the proximity of TAD boundaries is directly linked to gene activity. The authors use high-throughput imaging to simultaneously measure the gene activity and physical distances between boundary regions in an allele-specific manner. Using transcriptional inhibitors, expression induction, and acute depletion of CTCF and cohesin, they test whether proximity of boundaries affects, or is affected by, gene activity.

Strengths:

The combined use of DNA and RNA imaging enabled simultaneous measurement of boundary proximity and transcriptional status at individual alleles. This allows single-allele correlation between boundary proximity and gene activity at multiple loci across thousands of alleles.

The use of both transcription inhibitors and transcription stimulation provides compelling and consistent evidence that boundary proximity can be disconnected from a gene's activity. The data convincingly support the conclusion that stable proximity between boundary regions is not required for ongoing transcription at the loci and timescales examined.

This work strengthens the emerging view that genome organization at the level of domain boundaries does not impose a deterministic control over transcription.

Strong disruption of boundary distances is only observed upon depletion of cohesin. Notably, this corresponds with the largest changes in gene activity. In contrast, depletion of CTCF actually had minimal impact on boundary distances and also had minimal impact on gene activity. This makes sense in light of previous work, where live cell imaging demonstrated that cohesin is more important for domain-structure, whereas CTCF is only important for blocking cohesin from continuing on, such that the fully formed loop occurs in a very small percentage of cells. Therefore, the fact that disruption of cohesin (more important for internal domain structure) affects gene activity while disruption of CTCF does not is exceptionally interesting.

Weaknesses:

In untreated cells, the distribution of distance measurements between boundary probes is exceptionally narrow. While depletion of RAD21 clearly demonstrates an ability to detect changes in this distribution, this tight baseline distribution may limit sensitivity to more subtle changes (like those one might expect from transcriptional influences).

This approach primarily tests the role of boundary interactions rather than domain organization as a whole.