Reviewer #2 (Public review):

I have completed a thorough review of this paper, which seeks to use the large datasets of species occurrences available through GBIF to estimate variation in how large numbers of plant and animal species are associated with urbanization throughout the world, describing what they call the "species urbanness distribution" or SUD. They explore how these SUDs differ between regions and different taxonomic levels. They then calculate a measure of urban tolerance and seek to explore whether organism size predicts variation in tolerance among species and across regions.

The study is impressive in many respects. Over the course of several papers, Callaghan and coauthors have been leaders in using "big [biodiversity] data" to create metrics of how species' occurrence data are associated with urban environments, and in describing variation in urban tolerance among taxa and regions. This work has been creative, novel, and it has pushed the boundaries of understanding how urbanization affects a wide diversity of taxa. The current paper takes this to a new level by performing analyses on over 94000 observations from >30,000 species of plants and animals, across more than 370 plant and animal taxonomic families. All of these analyses were focused on answering two main questions:<br /> (1) What is the shape of species' urban tolerance distributions within regional communities?<br /> (2) Does body size consistently correlate with species' urban tolerance across taxonomic groups and biogeographic contexts?

Overall, I think the questions are interesting and important, the size and scope of the data and analyses are impressive, and this paper has a potentially large contribution to make in pushing forward urban macroecology specifically and urban ecology and evolution more generally.

Despite my enthusiasm for this paper and its potential impact, there are aspects that could be improved, and I believe the paper requires major revision.

Some of these revisions ideally involve being clearer about the methodology or arguments being made. In other cases, I think their metrics of urban tolerance are flawed and need to be rethought and recalculated, and some of the conclusions are inaccurate. I hope the authors will address these comments carefully and thoroughly. I recognize that there is no obligation for authors to make revisions. However, revising the paper along the lines of the comments made below would increase the impact of the paper and its clarity to a broad readership.

Major Comments:

(1) Subrealms

Where does the concept of "subrealms" come from? No citation is given, and it could be said that this sounds like an idea straight out of Middle Earth. How do subrealms relate to known bioclimatic designations like Koppen Climate classifications, which would arguably be more appropriate? Or are subrealms more socio-ecologically oriented? From what I can tell, each subrealm lumps together climatically diverse areas. It might be better and more tractable to break things in terms of continents, as the rationale for subrealms is unclear, and it makes the analyses and results more confusing. The authors rationalized the use of subrealms to account for potential intraspecific differences in species' response to urbanization, but that is never a core part of the questions or interpretation in the paper, and averaging across subrealms also accounts for intraspecific variation. Another issue with using the subrealm approach is that the authors only included a species if it had 100 observations in a given subrealm, leading to a focus on only the most common species, which may be biased in their SUD distribution. How many more species would be included if they did their analysis at the continental or global scale, and would this change the shape of SUDs?

(2) Methods - urban score

The authors describe their "urban score" as being calculated as "the mean of the distribution of VIIRS values as a relative species-specific measure of a response to urban land cover."

I don't understand how this is a "relative species-specific measure". What is it relative to? Figures S4 and S5 show the mean distribution of VIIRS for various taxa, and this mean looks to be an absolute measure. Mean VIIRS for a given species would be fine and appropriate as an "urban score", but the authors then state in the next sentence: "this urban score represents the relative ranking of that species to other species in response to urban land cover".

That doesn't follow from the description of how this is calculated. Something is missing here. Please clarify and add an explicit equation for how the urban score is calculated because the text is unclear and confusing.

(3) Methods - urban tolerance

How the authors are defining and calculating tolerance is unclear, confusing, and flawed in my opinion.

Tolerance is a common concept in ecology, evolution, and physiology, typically defined as the ability for an organism to maintain some measure of performance (e.g., fitness, growth, physiological homeostasis) in the presence versus absence of some stressor. As one example, in the herbivory literature, tolerance is often measured as the absolute or relative difference in fitness of plants that are damaged versus undamaged (e.g., https://academic.oup.com/evolut/article/62/9/2429/6853425?login=true).

On line 309, after describing the calculation of urban scores across subrealms, they write: "Therefore, a species could be represented across multiple subrealms with differing measures of urban tolerance (Fig. S4). Importantly, this continuous metric of urban tolerance is a relative measure of a species' preference, or affinity, to urban areas: it should be interpreted only within each subrealm".

This is problematic on several fronts. First, the authors never define what they mean by the term "tolerance". Second, they refer to urban tolerance throughout the paper, but don't describe the calculation until lines 315-319, where they write (text in [ ] is from the reviewer):

"Within each subrealm, we further accounted for the potential of different levels of urbanization by scaling each species' urban score by subtracting the mean VIIRS of all observations in the subrealm (this value is hereafter referred to as urban tolerance). This 'urban tolerance' (Fig. S5) value can be negative - when species under-occupy urban areas [relative to the average across all species] suggesting they actively avoid them-or positive-when species over-occupy urban areas [relative to the average across all species] suggesting they prefer them (i.e., ranging from urban avoiders to urban exploiters, respectively).<br /> They are taking a relativized urban score and then subtracting the mean VIIRS of all observations across species in a subrealm. How exactly one interprets the magnitude isn't clear and they admit this metric is "not interpretative across subrealms".

This is not a true measure of tolerance, at least not in the conventional sense of how tolerance is typically defined. The problem is that a species distribution isn't being compared to some metric of urbanness, but instead it is relative to other species' urban scores, where species may, on average, be highly urban or highly nonurban in their distribution, and this may vary from subrealm to subrealm. A measure of urban tolerance should be independent of how other species are responding, and should be interpretable across subrealms, continents, and the globe.

I propose the authors use one of two metrics of urban tolerance:

(i) Absolute Urban Tolerance = Mean VIIRS of species_i - Mean VIIRS of city centers<br /> Here, the mean VIIRS of city centers could be taken from the center of multiple cities throughout a subrealm, across a continent, or across the world. Here, the units are in the original VIIRS units where 0 would correspond to species being centered on the most extreme urban habitats, and the most extreme negative values would correspond to species that occupy the most non-urban habitats (i.e., no artificial light at night). In essence, this measure of tolerance would quantify how far a species' distribution is shifted relative to the most highly urbanized habitat available.

(ii) % Urban Tolerance = (Mean VIIRS of species_i - Mean VIIRS of city centers)/MeanVIIRS of city centers * 100%<br /> This metric provides a % change in species mean VIIRS distribution relative to the most urban habitats. This value could theoretically be negative or positive, but will typically be negative, with -100% being completely non-urban, and 0% being completely urban tolerant.

Both of these metrics can be compared across the world, as it would provide either absolute (equation 1) or relative (equation 2) metrics of urban tolerance that are comparable and easily interpretable in any region.

In summary, the definition of tolerance should be clear, the metric should be a true measure of tolerance that is comparable across regions, and an equation should be given.

(4) Figure 1: The figure does not stand alone. For example, what is the hypothesis for thermophily or the temperature-size rule? The authors should expand the legend slightly to make the hypotheses being illustrated clearer.

(5) SUDs: I don't agree with the conclusion given on line 83 ("pattern was consistent across subrealms and several taxonomic levels") or in the legend of Figure 2 ("there were consistent patterns for kingdoms, classes, and orders, as shown by generally similar density histograms shapes for each of these").

The shapes of the curves are quite different, especially for the two Kingdoms and the different classes. I agree they are relatively consistent for the different taxonomic Orders of insects.

Comments on revised version:

I believe their response is thorough and thoughtful. I still disagree with them on some fundamental points of their methodology. However, I would prefer to let my review and their response stand as is. This will allow engaged readers to see both sides of the arguments and judge for themselves whether they believe the revisions are sufficient and if my concerns are valid.

Reviewer #1 (Public review):

Summary:

This study demonstrates, through a series of EEG and MEG experiments, that the human brain automatically categorizes words from alphabetic and non-alphabetic languages, and it unpacks the neural mechanisms of this process from multiple angles. The work examines not only univariate repetition-suppression (RS) effects, but also how repeating or alternating languages influences the representational similarity of words within and across language categories.

Strengths:

The univariate RS effects across multiple experiments lend support to some of the main conclusions.

Comments on revised version.

The authors have made appropriate revisions and supplements in response to the issues I raised, which has largely resolved my concerns.

Reviewer #1 (Public review):

Summary

This manuscript addresses an important question in auditory neuroscience and neuroprosthetics: whether cortical responses to cochlear implant stimulation resemble those evoked by natural acoustic stimulation, or whether electrical stimulation engages a distinct cortical representation. The authors use high-density intracranial EEG recordings in rats to compare responses to pure tones in normal-hearing animals with responses to single-channel cochlear implant stimulation in deafened animals. They combine analyses of event-related potentials, high-gamma activity, trial-by-trial variability, PCA/TCA-based dimensionality reduction, and decoder-based measures of stimulus information.

Strengths

A major strength of the study is the question it addresses. Understanding how electrical cochlear stimulation is represented centrally is highly relevant for cochlear implant design, fitting strategies, and rehabilitation. The comparison between acoustic and electrical stimulation, including within-animal comparisons in a subset of cases, is valuable because it directly addresses whether implant-evoked activity can be interpreted within the framework of normal acoustic tonotopy.

The methodological approach is also a strength. Dense cortical surface recordings provide simultaneous access to spatial and temporal features of auditory cortical responses. The combination of PCA, TCA, and decoder analyses gives complementary views of the data, and the information-transfer analysis provides an interesting way to ask whether representations learned from acoustic stimulation generalize to electrical stimulation.

Weaknesses:

The main weakness is that the evidence for spatial organization remains difficult to interpret. In Figure 2, the authors argue that both tone-evoked and cochlear implant-evoked responses are spatially organized, but the slope analyses are not significant for the cochlear implant condition. The revised vector-strength analysis supports the presence of non-random spatial structure, but this is not the same as demonstrating a clear graded cochleotopic organization. The manuscript would be strongest if it consistently distinguished between non-random spatial structure, coarse topography, and true graded tonotopy or cochleotopy.

A related issue is that some figure titles and interpretive statements still appear stronger than the data justify. For example, the TCA results in Figure 7 are described as revealing topographically organized latent spatial factors, but the statistical support appears strongest for normal-hearing high-gamma responses, with weaker or non-significant results in other conditions. These data remain interesting, but they would be better framed as evidence for weak or coarse spatial structure rather than robust topographic organization across all modalities.

The decoder analyses are improved, especially with the added tone-to-tone control. This control supports the conclusion that poor acoustic-to-CI transfer is not simply a failure of the TCA/LDA pipeline. However, the analysis remains model-dependent, and the absolute information transfer values are low. It would be helpful either to include an analogous analysis using raw ERP/high-gamma features or to explain more explicitly why the TCA-based approach is the appropriate primary test. The data support poor generalization between acoustic and implant-evoked cortical responses, but claims about perceptual qualities should remain speculative because perception is not directly measured in these experiments.

Finally, although methodological reporting is much improved, some verification remains indirect. The authors provide useful implantation criteria and cite prior validation of their deafening approach, but the manuscript would be clearer if it explicitly distinguished between validation performed in the present animals and validation based on previous cohorts. This distinction is important because surgical variability, implantation efficacy, and deafening completeness can influence the interpretation of cochlear implant experiments.

Comments on revised version.

The revised manuscript is considerably improved. The authors have clarified several methodological details, added a statistical framework that better accommodates both paired and unpaired animals, provided a clearer account of animal cohorts, added peripheral ECAP/forward-masking data to support the cochlear specificity of implant stimulation, and included a useful positive control for the cross-modal decoder analysis. These additions make the manuscript stronger and help readers interpret the main findings more confidently.

The results support the conclusion that acoustic and cochlear implant stimulation evoke cortical responses with different properties. In particular, acoustic responses support better single-trial stimulus decoding than cochlear implant responses, and decoders trained on acoustic responses transfer poorly to implant-evoked responses. The evidence for spatial organization is more nuanced. The cochlear implant condition shows evidence of non-random spatial structure, but not a clear graded cochleotopic map. The normal-hearing condition is also less visually clear than might be expected from prior tonotopy studies, although the added analyses and comparisons to previous work help contextualize this result. Overall, the study makes a valuable contribution, provided that the claims about spatial organization and perceptual interpretation remain appropriately cautious.

The revision addresses several important concerns from the original version. The use of mixed-effects models better matches the partially paired experimental design. The expanded Methods improve reproducibility. The new cohort schematic helps clarify which animals contributed to behavioral and neural datasets. The ECAP forward-masking measurements add useful peripheral validation, and the within-modality decoder control strengthens the interpretation of the poor cross-modal transfer result. Together, these changes substantially improve the manuscript.

The work is likely to be of interest to auditory neuroscientists, cochlear implant researchers, and neuroengineers. Even where some conclusions require cautious wording, the dataset and analytical framework may be useful for future studies aiming to relate cortical responses to implant programming, perceptual learning, or closed-loop neuroprosthetic approaches.

Overall, the revised manuscript is stronger and addresses an important problem with useful methods and analyses. The results most convincingly show that acoustic responses support better single-trial decoding than acute cochlear implant responses, and that acoustic-trained decoders generalize poorly to implant-evoked activity. The evidence for robust spatial organization, especially in the cochlear implant condition, is more limited and should be presented with appropriate caution.

Reviewer #1 (Public review):

Summary:

This study investigates the impact of Pink1 loss on glial function and neuronal health in a Drosophila model, highlighting the role of mitochondria-organelle contacts and key genes such as Ccz1, Vps13, Mon1, and Rab7. The work provides insights into cellular processes underlying neurodegenerative diseases, with a focus on glia-neuron interactions.

Comments on revised version:

I have reviewed the revised manuscript and the authors' responses to previous comments. The authors have addressed the key concerns raised by the reviewers, including validation of the Mz-GAL4 line and additional control experiments. The remaining issues caused by experimental constraints are understandable in this study.

However, several concerns remain. Notably, some key results were removed due to the use of inadequately characterized fly lines, and the lack of follow-up experiments to address these issues raises concerns regarding the validity and reliability of the findings. Furthermore, the absence of experiments examining Rab7-mediated membrane trafficking or the interactions between mitochondria and lysosomes in the Pink1 mutant presents a limitation. These missing elements reduce the clarity and interpretability of Figure 5 for readers.

On a positive note, the data showing that reducing Vps35/Vps13 enhances neuronal function and rescues Pink1 mutant phenotypes in ensheathing glia contributes meaningfully to the overall narrative.

Despite these limitations, this research addresses an important question in neuroscience using the Drosophila model. It provides a novel perspective on Parkinson's disease and neurodegeneration by exploring mechanisms underlying Pink1 loss and suggesting a role for mitochondria-organelle interactions in ensheathing glia, potentially regulated via Vps35/Vps13-mediated pathways.

Overall, the current version presents a clear and meaningful contribution to the field.

Reviewer #1 (Public review):

Summary:

In this study entitled "Linking Germline Telomere Removal to Global Programmed DNA Elimination in Tetrahymena Genome Differentiation" Nagao and colleagues examine the fate of germline chromosome ends during somatic genome differentiation in the ciliate Tetrahymena thermophila. During sexual reproduction, a new somatic genome is created from a zygotic, germline-derived genome by extensive programmed DNA elimination events. It has been known for some time that the terminii of the germline chromosomes are eliminated, but the exact process and kinetics of the elimination events has not been thoroughly investigated. The authors first use germline-specific telomere probes to show that the loss of these chromosome ends occurs with similar timing as other DNA elimination events. By comparative analysis of the assembled germline and somatic genomes, the authors find the ends of each of the germline chromosomes are composed of few hundred kilobases of micronuclear limited sequences (MLS) that are removed starting around 14 hours after the start of conjugation, which initiates sexual development. They then develop an in-situ hybridization assay to track the fate of one end of chromosome 4 while simultaneously following the adjacent macronuclear destined sequence (MDS) retained in the new somatic genome. This allows the authors to more clearly show that these adjacent chromosomal segments are initially amplified in the developing genome before the terminal MLS is eliminated. Finally, they mutate the chromosome breakage sequence (CBS) that normally separates the MLS terminus from the adjacent MDS region as show that strains that develop with only one mutant chromosome can produce viable sexual progeny, but it appears that both the MLS and the MDS from the mutant chromosome are lost. If both chromosome copies have the CBS mutation, the cells arrest during development and do not eliminate many germline limited sequences and fail to produce viable progeny. Overall, this study provides many new insights into the fate of germline chromosome ends during somatic genome remodeling and suggests extensive coordination of different DNA elimination events in Tetrahymena.

Strengths:

Overall, the experiments were well executed with appropriate controls. The findings are generally robust. Importantly, the study provides several novel findings. First, the authors provide a fairly comprehensive characterization of the size of the MLS at the end of each germline chromosome. They also report on the highly repetitive composition of these chromosome terminii. Second, the authors develop a novel method to study the fate of chromosome terminii during development and use it conclusively track the elimination of these terminii. Third, the authors show that the elimination of these terminii appears to occur concurrently with most other DNA elimination events during somatic genome differentiation. And fourth, the authors show that failure to separate these eliminated sequences from the normally retained chromosome alters the fate of these adjacent MDS and loss of the cells ability to produce viable progeny. The authors initially hypothesized that DNA elimination may be blocked due to inappropriate silencing of genes in the MDS region when the CBS is mutant, but gene expression analysis showed that this is not the case.

Weaknesses:

After revising the manuscript based on the initial reviewers' critique, most weaknesses have been addressed. On weakness remaining is that since the authors only mutated the end of one germline chromosome, it is not clear whether the elimination of the MDS adjacent to the terminal MLS on chromosome 4 when the CBS is mutated is a general phenomenon, i.e. would happen at all chromosome ends, or is unique to the situation at Chromosome 4R. Knowing whether it is a general phenomenon or not would provide important insight into the authors findings. The authors did attempt to look at other chromosome ends, but technical limitations currently stymie this effort.

The other weakness is that it remains unclear how failure to carry out DNA elimination appears to induce a checkpoint during development, but this open question is not unique to this study.

Comments on revised version.

The authors have significantly improved the study. The addition of the RNA-seq analysis allowed these researchers to show that their initial hypothesis - that loss of a CBS leads to inappropriate gene silencing in the neighboring MDS region - appears not to be the case. I do not have further suggestions for the authors.

Reviewer #1 (Public review):

[Editor's note: This version has been assessed by the Reviewing Editor without further input from the original reviewers. The authors have addressed all concerns raised by the reviewers; no further changes are required at this point.]

Summary:

The manuscript by Yang et al. investigates the relationship between multi-unit activity in the locus coeruleus, putatively noradrenergic locus coeruleus, hippocampus (HP) sharp-wave ripples (SWR) and spindles using multi-site electrophysiology in freely behaving male rats. The study focuses on SWR during quiet wake and non-REM sleep, and their relation to cortical states (identified using EEG recordings in frontal areas) and LC units.

The manuscript highlights differential modulation of LC units as a function of HP-cortical communication during wake and sleep. They establish that ripples and LC units are inversely correlated to levels of arousal: wake, i.e. higher arousal correlates with higher LC unit activity and lower ripple rates. The authors show that LC neuron activity is strongly inhibited just before SWR detected during wake. During non-REM sleep, they distinguish "isolated" ripples from SWR coupled to spindles and show that inhibition of LC neuron activity is absent before spindle-coupled ripples but not before isolated ripples, suggesting a mechanism where noradrenaline (NA) tone is modulated by HP-cortical coupling. This result has interesting implications for the roles of noradrenaline in the modulation of sleep-dependent memory consolidation, as ripple-spindle coupling is a mechanism favoring consolidation. The authors further show that NA neuronal activity is downregulated before spindles.

Strengths:

In continuity with previous work from the laboratory, this work expands our understanding of the activity of neuromodulatory systems in relation to vigilance states and brain oscillations, an area of research that is timely and impactful. The manuscript presents strong results suggesting that NA tone varies differentially depending on coupling of HP SWR with cortical spindles. The authors place their findings back in the context of identified roles of HP ripples and coupling to cortical oscillations for memory formation in a very interesting discussion. The distinction of LC neuron activity between awake, ripple-spindle coupled events and isolated ripples is an exciting result and its relation to arousal and memory opens fascinating lines of research.

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 this study, the authors propose that HSV-1 infection degrades the class I histone deacetylases HDAC1 and HDAC2. The MDM2 E3 ubiquitin ligase from the DNA damage response pathway is responsible for ubiquitinating these HDACs that are subsequently degraded via proteasomes. The authors hypothesize that HDAC degradation will cause hyperacetylation of viral chromatin and enable viral gene transcription.

Strengths:

The ubiquitination of HDAC1 & HDAC2 by Mdm2 and the mapping studies are clear.

Reviewer #1 (Public review):

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

Summary:

In the manuscript "Pathogen-Phage Geomapping to Overcome Resistance," Do et al. present an impressive demonstration of using geographical sampling and metagenomics to guide sample choice for enrichment in human-associated microbes and the pathogen of interest to increase the chances of success for isolating phages active against highly resistant bacterial strains. The authors document many notable successes (17!) with highly resistant bacterial isolates and share a thoughtfully structured phage discovery effort, potentially opening the door to similar geomapping efforts across the field. While the work is methodologically strong and valuable for the community, there are a few areas where additional clarification and analysis could better align the claims with the data presented.

Strengths:

(1) The manuscript describes a well-executed and transparent example of overcoming a major obstacle in therapeutic virus identification, providing a practical success story that will resonate with researchers in microbiology and medicine.

(2) Many phage researchers have anecdotally experienced a similar phenomenon, that a particular wastewater treatment plant always seems to have the pathogens you need. Quantifying this with metagenomics modernizes and adds evidence to this phenomenon in a way that could help researchers reproduce this success in a methodical way.

(3) The methodology of combining environmental sampling, viral screening, and host-range analysis is clearly articulated and reproducible, offering a valuable blueprint for others in the field.

(4) The data are presented with appropriate analytical rigor, and the results include robust sequencing and metagenomic profiling that deepen understanding of local viral communities.

(5) The 17 successes yielding 35 phages have a lot of phylogenetic novelty beyond what the Tailor labs have typically found with previous methods.

(6) The work highlights a practical and innovative solution to an increasingly important clinical problem, supporting the development of personalized antiviral strategies.

Trump may be mystery patient in odd case of 79yo getting experimental obesity drug<br /> by [[Beth Mole]] in Ars Technica<br /> accessed on 2026-06-23T21:06:22

Reviewer #1 (Public review):

Summary:

Gurnani et al. explore how dynamical properties of neural networks influence capacity for and mechanisms of learning. Specifically, they focus on Brain Computer Interface (BCI) learning, in which manipulations are applied to a decoder that maps neural activity onto computer cursors. This paradigm was introduced by Sadtler et al. 2014, and has become an influential part of the neuroscience motor learning literature. A particularly fascinating outcome of that body of work is the observation that "within-manifold" perturbations (WMPs), which preserve covariance structure in the neural population, are easier to learn than "outside-manifold" perturbations (OMPs), which break this. Since deep network parameter access is challenging (to say the least) in monkey experiments, the intuition for this split in learnability is ripe for modeling and theory work. Indeed, the authors here introduce a feedback-driven recurrent neural network model whose output drives a simulation of a neural decoder commonly used in BCI studies like the Sadtler paper. While there have now been several modeling studies exploring how neural networks could solve this task, the feedback control perspective gives the authors' new model an interesting niche. Overall, this is a thoroughly done and well-written modeling study, and a solid contribution to the literature on within- and outside-manifold perturbations.

Strengths:

Reframing the OMP and WMP learning from a feedback-driven dynamical systems perspective, not just a geometric one, is an interesting take. The controllability analysis (along with the clear difference in input-driven and recurrence-driven learning) is quite a cool result that helps better frame what might be happening in the primate brain during similar tasks.

Weaknesses:

Some of the more interesting aspects, especially the controllability) and the differences between input-driven and recurrence-driven learning could be further developed, either by showing more analyses or running more comparisons. A few sections could benefit from some additional clarity on the strength and significance of results.

I like this text because it talks about how college can be challenging and uncomfortable at times. Growth usually happens when people are pushed outside of their comfort zones and try new things. It a good reminder that feeling stressed or unsure sometimes does not mean your failing, it means your learning.

This section helps me think about college differently because it reminds me that success is not just about being smart. There's going to be challenges and being able to keep going when things get difficult is important. I think developing resilience will help me handle setbacks and stay focused on my goals.

Reviewer #1 (Public review):

Summary:

This study investigates the role of the medial prefrontal cortex (mPFC) in generating goal-directed actions under threat, using a progressive behavioral paradigm, neural recordings, and optogenetic inhibition in mice. The authors demonstrate that while mPFC GABAergic neurons strongly encode cues, actions, and errors, particularly under high cognitive demand, this neural activity is not causally required for executing avoidance behaviors. By rigorously controlling for movement and arousal, the researchers found that much of the observed mPFC signaling actually reflects baseline behavioral states rather than the generation of the actions themselves. This dissociation between encoding and causality challenges traditional views of mPFC as an executive controller of action and provides a nuanced understanding of its role in evaluative and contextual processing.

Strengths:

The behavioral paradigm employed in this study is one of its greatest strengths, offering a rigorous, progressive, and well-controlled framework to dissect the neural mechanisms underlying avoidance under threat. This three-phase task design is particularly well-suited to tease apart the contributions of learning, discrimination, and cognitive load to both behavior and neural activity.

By tracking movement (speed, rotations) and including it as a covariate in statistical models, the authors also underscore the need to control for movement and baseline activity when interpreting cortical signals, which is relevant for all studies of brain-behavior relationships, ensuring that behavioral changes are not due to general arousal or motor activity.

Finally, the study combines multiple advanced techniques-fiber photometry, single-cell calcium imaging (miniscopes), and two distinct optogenetic inhibition methods-to provide a comprehensive look at both neural encoding and causal necessity.

Comments on revised version.

The authors adequately addressed all of the reviewers' comments and made great improvements to the manuscript, particularly enhancing the methods and figures to significantly improve clarity and readability.

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:

Morgan et al. studied how paternal dietary alteration influenced testicular phenotype, placental and fetal growth using a mouse model of paternal low protein diet (LPD) or Western Diet (WD) feeding, with or without supplementation of methyl-donors and carriers (MD). They found diet- and sex-specific effects of paternal diet alteration. All experimental diets decreased paternal body weight and the number of spermatogonial stem cells, while fertility was unaffected. WD males (irrespective of MD) showed signs of adiposity and metabolic dysfunction, abnormal seminiferous tubules and dysregulation of testicular genes related to chromatin homeostasis. Conversely, LPD induced abnormalities in the early placental cone, fetal growth restriction and placental insufficiency, which was partly ameliorated by MD. The paternal diets changed placental transcriptome in a sex-specific manner and led to a loss of sexual dimorphism in the placental transcriptome. These data provide a novel insight on how paternal health can affect the outcome of pregnancies, which is often overlooked in prenatal care.

Strengths:

The authors have performed a well-designed study using commonly used mouse models of paternal underfeeding (low protein) and overfeeding (Western diet). They performed comprehensive phenotyping at multiple timepoints including of the fathers, the early placenta and late gestation feto-placental unit. The inclusion of both testicular and placental morphological and transcriptomic analysis is a powerful non-biased tool for such exploratory observational studies. The authors describe changes in testicular gene expression revolving around histone (methylation) pathways that are linked to altered offspring development (H3.3 and H3K4), which is in line with hypothesised paternal contributions to offspring health. The authors report sex differences in control placentas that mimic those in humans, providing potential for translatability of the findings. The exploration of sexual dimorphism (often overlooked) and its absence in response to dietary modification is novel and contributes to the evidence-base for the inclusion of both sexes in developmental studies.

Comments on revised version:

The authors have done a great job addressing my concerns. The description of the data analysis and the figures are now much clearer. The inclusion of the potential links between the microbiome and male reproductive fitness is informative and improves the flow of the discussion.

Joint Public Review:

[Editor's Note: The previous reviewers comments were felt to be addressed by the reviewers and myself and have improved the work.]

In this study, the authors suggest that DuoHexaBody-CD37, a biparatopic CD37-targeting antibody, can induce direct cytotoxicity in diffuse large B-cell lymphoma (DLBCL) cells through antibody clustering and SHP-1 activation, independent of complement. They further propose that DuoHexaBody-CD37 inhibits cytokine-mediated pro-survival signalling, suggesting a broader role for CD37-directed therapy in disrupting tumour supportive signalling networks.

A strength of the study is the systematic in vitro characterisation of signalling responses to DuoHexaBody-CD37 across both malignant and normal B-cells. The inclusion of phosphoproteomic profiling and mutant constructs provides mechanistic detail, and the findings may be of interest to researchers working on antibody therapeutics in lymphoma.

However, the evidence supporting key mechanistic processes - particularly the specific subtype requirement for Fc receptor crosslinking - is incomplete and would benefit from further functional validation. While CD37 has been explored previously as a therapeutic target, this study does add mechanistic insight into direct cytotoxicity and cytokine modulation. Nevertheless, the exclusive reliance on in vitro systems makes the translational relevance unclear.

Overall, the study provides valuable insight into CD37-mediated signalling in lymphoma cells, but the evidence remains incomplete to support broader conclusions about therapeutic impact. The additional mechanistic data included during revision are informative, but the precise basis of the observed cytotoxic effects remains incompletely defined.

Reviewer #1 (Public review):

The manuscript "Heterozygote advantage cannot explain MHC diversity, but MHC diversity can explain heterozygote advantage" explores two topics. First, it is claimed that the recently published by Mattias Siljestam and Claus Rueffler conclusion (in the following referred to as [SR] for brevity) that heterozygote advantage explains MHC diversity does not withstand an even very slight change in ecological parameters. Second, a modified model that allows an expansion of MHC gene family shows that homozygotes outperform heterozygotes. This is an important topic and could be of potential interest to the readership of eLife if the conclusions are valid and non-trivial.

The resubmitted manuscript addresses several questions from my previous review. In particular, there is a more detailed description of how the code of Siljestam and Rueffler ([SR]) was used for the simulations and the calculation of the factor 2.7 x 10^43 that is the key to the alleged breakdown of the numerical reasoning presented by in [SR].

Yet I think that important aspects of my critique of the first statement of the manuscript about the flaws of [SR] model remain unanswered. I guess the discussion becomes rather general about the universality and robustness of various types of models to parameter changes. My point is that none of the models is totally universal. The model in [SR] is not phenomenological as none of the parameters or functional forms were derived empirically. Instead, it is a proof of principle demonstration that inevitably grossly simplifies the actual immune response. The choice of constants and functions used in Eqs. (1-5) is dictated by the mathematical convenience and works in a limited range of parameter values. It is shown in [SR] that for 3 pathogens and reasonable "virulence " \nu, the alleles branch. These conclusions are supported by the analytically derived Adaptive Dynamics branching criteria (7), which, contrary to the statement is the cover letter (" It is clear from Fig. 4 of Siljestam and Rueffler that the branching condition is far from sufficient for high MHC diversity.") is perfectly confirmed by the simulation data shown in Fig. 4.

The mathematical simplicity of the [SR] model generates various artifacts, such as the mentioned by the Author reduction of the "condition" by an enormous factor 2.7 x 10^43 and the resulting decrease in the "survival" induced by the addition of a new pathogen. This occurs at the very large value of \nu=20, whose effect is enormous due to the Gaussian form of (1), which, once again, was chosen for the mathematical convenience. In reality, a new pathogen cannot reduce the "survival" by such a factor as it would wipe out any resident population. So to compensate for such an artifact, the additional factor c_max was introduced to buffer such an excess. There is no reason to fix c_max once for an arbitrary number of pathogens, because varying c_max basically reflects the observation that a well-adapted individual must have a reasonable survival probability. At the same time, there are many ways in which the numerical simulation may break down when the survival rates become of the order of 10^(-43) instead of one, so it comes to no surprise that the diversification, predicted by the adaptive dynamics, does not readily occur in the scenario with an addition or removal of the 8th pathogen with a very high virulence \nu=20.

I have doubts that the reported breakdown of the [SR] model with fixed c_max remains observable with less extreme values of m and \nu (say, for \nu=7 and m=3 plus or minus 1 used in Fig. 3 in the manuscript).

So I still find the claim that " the phenomenon that leads to high diversity in the simulations of Siljestam and Rueffler depends on finely tuned parameter values" is not well substantiated.

Reviewer #1 (Public review):

In this study, the authors set out to determine how two classes of kinase inhibitors, which stabilise a disease-relevant enzyme in either an active (Type I) or inactive state (Type II), influence its organisation and interactions with microtubule filaments in cells. Using the state-of-the-art in-cell structural imaging approaches, they examine how these compounds affect the formation of protein filaments and their association with microtubules, and succeed in defining the underlying structural basis for these differences.

A major strength of the work is the application of in-cell cryo-electron tomography combined with correlative imaging, which enables direct visualisation of protein organisation in a near-native cellular context. The data convincingly demonstrate that the Type I inhibitor compound stabilising the active state promotes extensive LRRK2 filament formation and microtubule bundling, whereas compounds stabilising the inactive state markedly reduce these interactions. The structural analysis further provides insight into how conformational states relate to filament organisation, including modelling of previously unresolved regions of the protein.

These findings are internally consistent and align well with prior biochemical and structural studies, many of which were performed by the same team.

There are, however, some limitations that should be noted. The experiments rely on overexpression of the I2020T mutant form of the LRRK2 protein, which is a rare variant, in a single cell type (293T cells), which may not fully reflect endogenous behaviour or wild-type LRRK2 in a physiological context. In addition, while the imaging data are compelling, the functional consequences of the observed filament formation and microtubule association remain unclear.

The study therefore provides strong descriptive and structural insight, but more limited evidence linking these observations to cellular or disease-relevant outcomes.

Overall, the authors largely achieve their aims, and the results support their central conclusion that different classes of kinase inhibitors have distinct effects on protein organisation in cells. The work represents an important advance in understanding how small molecules can reshape protein architecture in a cellular environment, with potential implications for therapeutic strategies. The methodological approach will also be of broad interest to the field, as it highlights the power of in-cell structural biology to study dynamic protein assemblies that are difficult to capture using traditional approaches.

Reviewer #1 (Public review):

The authors of this study developed a method to quantify calvarial bone marrow from MRI head scans, enabling the study of its composition in large datasets of adults, usually collected to study the brain. Bone marrow intensity can be semi-quantitatively measured in T1-weighted MRI scans due to the greater signal intensity of fat than watery red marrow. This is an ingenious use of the MRI-produced information for other important phenotypes, such as bone structure and marrow content. Different head types were tested for complying with the model, which is notable.

The model was also successfully validated using several publicly available MRI resources - real data - in (1) a dataset consisting of 30 individuals that were scanned 10 times each at 3-day intervals, and (2) the monozygotic (MZ) twin data from the Human Connectome Project cohort. Then the authors applied this validated method to head-MRI scans from the UK Biobank (n=33,042) to extract information on the spatial distribution of bone marrow adiposity (BMA) in the calvaria, allowing a GWAS to identify associated genes.

The authors revealed high heritability and identified 41 genetic loci significantly associated with the BMA trait, including six sex-specific loci. Of note, statistics estimate that 99% of BMA trait-influencing variants are shared with BMD (497 of 500 variants), which may mean these results demonstrate the biological relevance to bone health. Some of the BMA genes were found related to the Wnt pathway, including WNT16, WNT4, NXN; this is a "positive control", since the Wnt/β-catenin signaling pathway was suggested as an important determinant of BMA. Also, associations in genes (BMP4, DLX5, LGR4, LRP4, SFRP4) that are known to specifically influence adiposity, are encouraging. Integrating mapped genes with bone marrow single-cell RNA-seq data revealed patterns of adipogenic lineage differentiation and lipid loading.

The study also investigated the genetic overlap between BMA and twelve (or 13) "brain and body" traits and identified significant genetic correlations with BMI, cognitive ability, and Parkinson's disease.

In sum, since MRI head scans present a hitherto unexplored opportunity to address unresolved aspects of bone marrow biology, this study is both timely and innovative.

There are, however, some assumptions, findings, and their interpretation, which require more critical focus.

Sex-specificity is well described and studied here. Men have higher BMA than women, but post-menopausal women catch up in the BMA values. The authors believe that calvarial marrow has a number of features that make it particularly well-suited to the study of BMA process - which is clinically important in other bone sites. It has a simple "sandwiched" structure that they are able to model. This is true only to some extent: a condition called "Hyperostosis frontalis interna", of unknown etiology (described by Smith & Hemphill in 1956) - is characterized by irregular overgrowth of the inner table of the frontal bone (symmetric/bilateral). Although not of clinical significance, typically benign, studies report a prevalence of 12%; However, it's most common in postmenopausal women - where prevalences up to 49% in women over the age of 65 - have been reported. Thus, sexual dimorphism is obvious and the effect of estrogen is likely shared with whichever bone - and marrow - age-related pathology. So, for women not using HRT, this new layer of the bone might interfere with the calvarial BMA readings and in turn, affect the BMA-related analyses. The authors suspect that the effect of BMA on BMD may be biased in women; they should comment on those "with low BMD and high BMA" given that hyperostosis frontalis might be an issue. A strong effect of SNPs in the ESR1 chromosomal region might be akin to the above concern.

Then, there is a perfect overlap of the BMA SNPs that are shared with BMD (497 of 500 variants), which may prove a "face validity" of the MRI-derived BMA. However, the BMD in the study was heel-derived eBMD - which is a good proxy for osteoporosis and is mostly driven by trabecular bone. Thus, there might be a concern that the BMA metrics capture some trabecular BMD.

Next, integrating mapped genes with existing bone marrow single-cell RNA-sequencing data revealed patterns of adipogenic lineage differentiation and lipid loading. The problem here is that the scRNAseq studies of the Bone Marrow niche are overwhelmingly mouse. The authors might wish to justify why they are relevant to humans (in the absence of the human-specific scRNAseq).

For genetic correlation analysis, the authors selected 7 body and 6 brain traits. The latter traits reflect cognition (general cognitive ability and educational attainment) and brain-related disorders. This selection might seem arbitrary. The interpretation of genetic correlation with cognitive ability, education, and Parkinson's disease was attributed to the recently discovered vascular channels that link calvarial bone marrow to the meninges. This is a fascinating hypothesis, which requires functional proof. However, there might be simpler explanations. Thus, the diploe and the inner table of the calvarium are drained by the same veins as the dura. From the anatomy textbook, we know that diploic veins connect the pericranial and endocranial venous system through the skull.

Reviewer #1 (Public review):

Summary:

In this manuscript, the authors investigate ubiquitylation of RPS27A/eS31 by the E3 ligase RNF25 in response to translational stress. Previous studies have identified RPS27A/eS31 ubiquitylation at Lys113 under conditions where translation factors are trapped in the ribosomal A-site. Here, the authors extend this work by testing whether additional translational stress conditions, including amino acid deprivation, induce RPS27A/eS31 ubiquitylation. They further show that GCN1 is required and explore a possible competition between RNF25 and GCN2 for GCN1.

Strengths:

This study expands on the range of stress conditions leading to RPS27A/eS31 ubiquitylation, reporting that it occurs in a variety of conditions associated with ribosome stalling, including amino acid deprivation. These observations are useful because they suggest that the RNF25 pathway may not require translation factors trapped in the ribosomal A-site, but may instead respond more broadly to translational perturbations associated with ribosome collisions.

Weaknesses:

The evidence supporting several of the major claims is incomplete, and additional controls and orthogonal approaches would greatly strengthen the evidence presented. In particular:

(1) It is unclear whether the different conditions used to induce translational stress lead to ribosome stalling or collisions. The model presented by the authors seems to rely on ribosomal collisions, but this is not shown. In addition, further investigating amino acid deprivation beyond the removal of Arg or Lys would strengthen the paper.

(2) Ubiquitylation of RPS27A/eS31 by RNF25 is used throughout the paper as a readout of RNF25 activity and is assumed to be on Lys113 based on previous work, but is not formally shown here.

(3) Rescue experiments of the different mutants used in this study with wild-type and different domain deletions (i.e., ΔRWD for RNF25, ΔRWD-binding for GCN1) would help confirm specificity and strengthen the mechanistic claims.

(4) The conclusion that RPS27A/eS31 ubiquitylation supports translation (Figure 4) is based entirely on polysome/monosome ratios, which are difficult to interpret without additional assays of translation output, elongation, or collision.

(5) The idea that RNF25 competes with GCN2 for GCN1 binding is interesting, and related models have recently been proposed in RNA damage. The effect of GCN2 KO on RNF25-dependent ubiquitylation appears modest, and the data would be strengthened by rescue experiments with wild-type GCN2 and GCN2 mutants defective in GCN1 binding. The authors propose: "that the RNF25 pathway acts as a first line of defence to resolve ribosome collisions, outcompeted by GCN2 binding to GCN1 under acute stress." This model would suggest a further increase in RPS27A/eS31 ubiquitylation upon Arg/Lys deprivation in GCN2 KO cells, since this is the condition in which GCN2 is expected to be activated and engaged with GCN1 (i.e., when it would be competing with RNF25), but no further increase in RPS27A ubiquitylation is observed. It is therefore not clear that these data support the proposed model. Contributing to this may be the fact that many of these assays are performed in a USP16 KO background, which may make it difficult to assess changes in RPS27A/eS31 ubiquitylation.

(6) Given that several RWD domain proteins can interact with GCN1, and that DRG2 KO appears to affect RPS27A/eS31 ubiquitylation (Figure S5), the data do not support the GCN2-specific title. The results are more consistent with a broader, incompletely characterized network of GCN1-associated RWD domain-containing proteins that seems to affect RNF25-dependent ubiquitylation rather than with a demonstrated RNF25-GCN2 competition mechanism. Further characterization of GCN2-dependent ISR activation (p-eIF2a and ATF4 WB) in the absence of RNF25 in Arg/Lys starvation will help shed light on the RNF25-GCN2 competition. The authors use K113R, but this is not shown to prevent RNF25 engagement with GCN1, so a RNF25 KO should be used.

Overall, the study contains useful observations, but the mechanistic claims are not yet fully supported.

Reviewer #1 (Public review):

Summary:

This study identifies mutations in alpha-tubulin that suppress Tau-induced neurodegeneration using the C. elegans model of Tauopathy, suggesting a potentially interesting role for microtubule properties in modulating Tau toxicity. These missense mutations cluster in the C-terminal Tau-interacting helix 12 region of alpha-tubulin genes (tba-1, tba-2, and mec-12). Further analysis, particularly using the strongest suppressor tba-2, shows that it rescues Tau-induced behavioral deficits and neuronal loss without significantly altering bulk tau-phosphorylation, aggregation, or binding to soluble tubulin. The authors suggest that altered microtubule properties underlie the neuroprotective effects, and manipulating microtubule properties may have therapeutic potential.

Strengths:

The study is conceptually interesting as it shows that Tau-induced neurotoxicity can, in this model, be partially uncoupled from canonical pathological hallmarks such as Tau-hyperphosphorylation and aggregation. The identification of multiple independent mutations in the same structural region of three alpha-tubulin genes provides support for the functional relevance of helix 12 in modulating Tau-induced toxicity. The authors demonstrate significant rescue of behavioral deficits (using motility and manual thrashing assays) and neuronal loss in both WT-tau and FTLD-associated TauV337M in combination with mutant alpha-tubulins, suggesting a general mechanism for tubulin-regulated modulation of Tau-toxicity. Moreover, the correlation between mutant tubulin expression levels and the extent of rescue supports a causal relationship.

Weaknesses:

One of the major claims of this manuscript is that altered microtubule properties suppress Tau toxicity. The only supporting evidence in this context provided by the authors is reduced taxol-stabilized microtubule mass, which does not fully explain neuronal loss or the rescue of behavioral deficits. What remains unclear is whether these mutations alter microtubule dynamics, catastrophe, lattice stability, or axonal transport.

The authors show that mutant tba-2 reduces total tau levels by ~45%. This level of reduction is likely significant but underexplored in the manuscript. Why are the Tau levels reduced? How is Tau getting cleared- is there enhanced autophagy or ubiquitin-proteasome pathway getting upregulated in tba-2 + Tau animals? Or one or more of the Tau species not detectable by the antibodies used in this study? The observation that the mec-12 mutant rescues Tau-induced phenotypes without altering Tau levels suggests that suppression can occur through Tau-independent mechanisms. This raises an important unresolved question regarding the extent to which suppression is Tau-dependent vs Tau-independent across different mutant alpha-tubulin genes, complicating the interpretation of the rescue phenotypes.

Given that Tau primarily associates with the microtubule lattice in vivo, measuring interactions with soluble tubulin may not fully capture biologically relevant binding dynamics and therefore does not exclude the possibility that these mutations alter tau-microtubule interactions at the lattice level or may affect the binding of other MAPs/regulators, thereby altering stability or trafficking.

A large body of conclusions is drawn from behavioral rescue and biochemical assays. This limits the understanding of how molecular changes in tubulin might affect cellular mechanisms of neuroprotection. Are there changes in the neuronal microtubule organization, Tau localization, or its redistribution in the mutant alpha-tubulin background? Are there differences in soluble vs oligomeric vs insoluble Tau in mutant tba-2 and mec-12 animals?

The suppression of behavior in the co-pathology model is interesting but mechanistically insufficient, mainly because the underlying basis of suppression is not examined in these models. Moreover, it remains unclear whether tubulin-Tau genetically interacts with Aβ or TDP-43, and what cellular mechanisms account for the partial rescue observed in these co-pathology models.

CTLA4 Alteration and Neurologic Manifestations: A New Family with Large Phenotypic Variability and Literature Review

Reviewer #1 (Public review):

Summary:

The protein DELE1 is a critical component to signal mitochondrial stress to the cytosol: under stress conditions, a truncated form of DELE1, termed DELE1(CTD) accumulates in the cytosol as an oligomer, binds the HRI kinase, which triggers the integrated stress response.

Leveraging the structural knowledge of the DELE1(CTD) oligomer, this study attempts to interfere with the oligomerization process, using an AI-designed protein that binds to the DELE1(CTD) oligomerization interface. The starting hypothesis is that such a binder shall selectively inhibit the DELE1-signalled mitochondrial stress response. The authors use established AI pipelines (RFdiffusion) to make a series of such binders, characterize them with biochemical methods and a crystal structure of the binder in its free state. When over-expressing the binders in HEK293T cells, the authors report that mitochondrial stress - induced with a drug - does indeed not lead to triggering the stress response, confirming their starting hypothesis.

The work is an elegant demonstration of how AI-designed proteins can specifically interfere with cellular mechanisms.

The conclusions of the work are mostly well supported by data; there are some mechanistic gaps, however, about the interaction mechanisms.

Strengths:

The study is a nice combination of (i) a clear structure-derived hypothesis on how to interfere with a signalling mechanism, (ii) state-of-the-art protein design tools, (iii) a mostly robust biochemical characterization, and (iv) cellular experiments to demonstrate the effects of the binders.

Weaknesses:

The crystal structure of the binder5, while confirming its AlphaFold model, does not provide direct evidence of the binding mode to DELE1. Direct structure determination, using crystallography (which may require cleaving the MBP domain) would make their mechanistic arguments stronger.

The demonstration that the binders do not inhibit the DELE1-HRI interaction is interesting; however, the underlying mechanism, in particular where the DELE1-HRI binding occurs, is not explored.

While this study opens perspectives on how to interfere with DELE1-signalling, it is unlikely that these binders are actually useful for medical applications (compared to small-molecule drugs), as acknowledged in the manuscript.

Reviewer #1 (Public review):

Summary:

This study investigates epigenetic and three-dimensional chromatin alterations associated with primary trastuzumab resistance in HER2-positive breast cancer using integrated CUT&Tag, RNA-seq, and Micro-C analyses in JIMT1 (resistant) and SKBR3 (sensitive) cell models. The authors identify widespread remodeling of histone modification landscapes, chromatin compartment organization, and promoter-enhancer looping, highlighting SGK1 as a candidate epigenetically activated mediator associated with intrinsic resistance. The manuscript provides a technically solid and extensive multi-omic resource for the study of HER2-positive breast cancer resistance states.

Strengths:

The study integrates multiple state-of-the-art epigenomic and chromatin conformation approaches, including CUT&Tag, RNA-seq, and Micro-C, generating a comprehensive dataset that will likely be valuable to the field. The analyses are generally technically rigorous and well executed, and the manuscript is overall clearly written. The integration of chromatin architecture, enhancer activity, transcriptional regulation, and histone modification profiling provides an informative overview of large-scale epigenomic remodeling associated with resistant versus sensitive HER2-positive breast cancer states. The identification of SGK1-associated chromatin activation and enhancer rewiring is particularly interesting and supported by multiple orthogonal datasets.

The inclusion of both intrinsic and acquired trastuzumab resistance models also strengthens the study conceptually, even if the biological interpretation remains somewhat complex.

Weaknesses:

The major limitation of the study is that many of the central mechanistic conclusions remain largely correlative. Although coordinated changes in chromatin architecture, histone modifications, enhancer activity, and SGK1 expression are observed, direct evidence demonstrating that these epigenetic alterations causally drive SGK1 activation or trastuzumab resistance is currently lacking.

In addition, the interpretation of SGK1 as a broader trastuzumab-resistance driver is somewhat weakened by the analyses in the acquired resistant SKBR3_HR model, where SGK1-associated chromatin and transcriptional changes appear largely absent. This raises the possibility that SGK1 dependency may reflect a lineage- or model-specific vulnerability intrinsic to JIMT1 cells rather than a generalizable resistance mechanism.

The study also remains descriptive in several sections. Numerous chromatin interactions and compartment changes are cataloged without sufficient biological contextualization or mechanistic integration. As a result, parts of the manuscript currently read more as a comprehensive epigenomic profiling resource than a fully mechanistic study of resistance biology.

Finally, the translational impact is limited by the lack of patient-level validation linking SGK1 activation to trastuzumab response or clinical outcome in HER2-positive breast cancer cohorts.

Reviewer #1 (Public review):

Summary:

The authors used a large dataset evaluating gut carriage of Enterobacterales and ESBL organisms from children aged 6-24 months as the basis for a modeling study to investigate what factors are most important for determining the prevalence of ESBL resistance. The modeling incorporated travel, a simple model of carriage duration (short and long), fitness cost of resistance on transmission and clearance, and antibiotic use. They found that antibiotic use is the primary driver of resistance prevalence, with transmissibility of resistant strains also important for setting the prevalence. Travel, while important when prevalence is very low, plays less of a role in maintaining prevalence once it is established (in keeping with other recent work). They estimated the fitness cost of resistance (terming a reduction of 14% on the rate of transmission and an increase of 23% on the rate of clearance as "low"). While the extent of assumptions and simplifications makes me skeptical of the quantitative conclusions, the qualitative ones seem reasonable and reinforce the long-held principles of the field--reducing antibiotic pressure and interrupting transmission--and highlight the importance of understanding the biological factors that shape the duration of carriage and the likelihood of colonization.

Strengths:

This study incorporates many of the factors that might influence the carriage prevalence of ESBL Enterobacterales. This builds on the work led by this group, both in primary data collection and in theory. Overall, it's such a tough problem that I commend the authors for trying to tackle it. The authors take a thoughtful, rigorous approach, acknowledging simplifications and assumptions where they need to, so as to evaluate the various factors shaping ESBL prevalence.

Weaknesses:

Part of the reason it's such a tough problem is that we have limited data to structure and parameterize a complex model.

(1) The data are not sufficiently described.

The primary data source for this modeling exercise comes from a study of 6-24-month-old children who underwent rectal swabs and evaluation of the carriage prevalence of Enterobacterales, and then whether these Enterobacterales were ESBL; moreover, the study included data on travel and on antibiotic use. Could the authors please direct us to these primary data? Could the authors also justify the parameters in their models from these data--for example, could they please provide the distribution of antibiotic use and the associated timing? Could they also explain why they decided to treat all Enterobacterales as if they were E. coli (line 307)? Is there evidence that all Enterobacterales occupy the same niche and compete with each other?

(2) The model should be more fully described and the limitations explored/explained.

- The authors should point to the code and the ODEs.<br /> - I understand the focus on the pediatric population; the authors argue that this is reasonable because ESBL colonization is similar across age groups. But presumably, antibiotic use differs across age groups, and there is colonization pressure from within households.<br /> - The authors only consider resistance to extended-spectrum beta-lactams and use of beta-lactam antibiotics, but ESBL Enterobacterales are often resistant to other antibiotics as well. How much does the use of other antibiotics also select for Enterbacterales that happen to carry ESBL resistance? "One bug/one drug" modeling, as done here, neglects the complexities of the actual patterns of resistance and range of antibiotic use.<br /> - Do the data support the T3 or S3 compartments, which, if I understand correctly, means no exposure to antibiotics can happen during three months after either treatment or travel? What do the data say about the patterns of antibiotic use? I'd imagine that the likelihood of antibiotic use is not homogenous, but instead, there are some who use repeated rounds of antibiotics.<br /> - Why do the authors exclude individuals who used antibiotics in the prior 7 days? What justifies that cutoff? The authors speculate that the impact of excluding these individuals is likely to be minimal; why exclude them, then? Did the authors evaluate the results if they were included?<br /> - What is the basis of "niche differentiation", as described starting on line 221? Why should clearance of one strain be slower when the strain co-occurs in a host with a strain of another type?

Reviewer #1 (Public review):

The study by Epp et al. has indeed gotten a lot of attention. As so often in the fMRI literature, some voices had taken the results out of proportion as if this result would suggest that we cannot trust fMRI. This is so, while informed researchers are aware of the capabilities and challenges of BOLD as a measure of neural activity. The paper was discussed and criticized on many aspects from various angles. E.g. with respect to unestablished models of estimating CMRO2, the 40% figure is being overestimated by the mask definition, and expected neuronal and vascular effects underlying the discordance.

The first publications of these discussions are being shared now. E.g. Chen et al. https://doi.org/10.1038/s41593-026-02288-y. The manuscript at hand augments this discussion. Specifically, the manuscript provides a direct statistical refutation of the recently proposed widespread physiological sign reversal between BOLD and CMRO2.

By reanalyzing a high-profile dataset, the authors demonstrate that the previously reported 40% discordance rate is an artifact of statistical uncertainty rather than a genuine physiological phenomenon. This critical re-evaluation restores some confidence in the canonical interpretation of BOLD signals that was recently challenged. It highlights the necessity of rigorous statistical validation in quantitative fMRI.

The following points should be addressed:

(1) Absence of evidence is taken as evidence of absence

The group-level significance analysis, summarized in the horizontal bar chart and cortical surface maps, labels non-significant voxels as 'CMRO2 not reliable', and the discussion concludes that positive BOLD responses are predominantly concordant with metabolism.

The paper treats voxels with non-significant CMRO2 effects as 'statistically uncertain' rather than as potentially reflecting genuine null metabolic changes, conflating absence of evidence with evidence of absence. Because the 77.2% of voxels shown as light orange could reflect either real null metabolism or insufficient power, the paper cannot distinguish between these. This ambiguity matters because a genuine null metabolic response to positive BOLD would itself be physiologically interesting and would not straightforwardly support 'predominant concordance'.

(2) Contextualization in other current literature

I feel that the introduction of the paper could also consider the embedding of the current literature about biophysical processes in the negative areas.

The negative responses have partly been discussed in the literature on quantitative physiology: e.g., Bohraus et al have been able to pinpoint the source of negative CMRO2 in positively activated voxels to large veins (https://doi.org/10.1016/j.celrep.2023.113341). Huber et al. have found that the neurovascular coupling (arterial venous weighting) is different in positively and negatively activated brain areas, making the interpretation of derived parameters on physiology hard.

(3) Stylistic comments.

In places, the tone of the language could be revised to ensure that it is perceived as making a constructive contribution to the discussion.

Reviewer #1 (Public review):

Summary:

In this study, the authors perform longitudinal mesoscale calcium imaging of visual and other cortical areas following binocular enucleation (blinding through the removal of the eyes) in adult mice. The study is observational and exploratory, and analyzes changes in the frequency distribution of calcium signals during locomotion and quiescence as a function of time after enucleation. They also analyze correlations between calcium signals in different brain regions to ask how apparent connectivity between regions changes over time. The main conclusions are (1) that there are multiple timescales of plasticity; (2) that the coupling between locomotion and activity in visual areas flips sign after enucleation, and (3) that correlations between brain areas are modulated by this long-lasting plasticity. Overall, the data are likely to be useful to researchers studying the impact of injury and catastrophic loss of sensory inputs on brain reorganization, but it is hard to draw firm conclusions from the observations provided beyond the very general conclusions listed above.

Strengths:

(1) The longitudinal imaging of multiple brain areas simultaneously allows the investigators to follow plastic changes in the same animals over time, to address questions about how apparent connectivity and brain state modulation unfold after injury.

(2) The data suggesting a flip in sign of the coupling between movement and "activity" in visual areas is interesting and potentially novel.

Weaknesses:

(1) The mesoscale imaging has limitations. In particular, the authors use words/phrases such as "activity" and "functional connectivity" without ever discussing what the measures they provide with this approach (frequency distribution of summed calcium fluctuations, and the correlation between this measure across brain areas) actually mean, or how they approximate spike-based measures or cellular-resolution Ca signals. The manuscript would benefit from an in-depth discussion of these limitations.

(2) In general, the figures are difficult to follow. In many cases, what is being plotted is hard to extract without a lot of work, and metrics are not well-justified. For example, they calculate the R value between movement power and spectral power of the Ca signal to quantify changes across time in the coupling between movement and activity (Figure 2). But from the example given, this does not look like a continuous relationship, and though R values are significant its not clear that this correlation is a good way of quantifying the change in sign they attempt to document. Figure 7 is impossible to read, and areas quantified are not indicated. The reader should not have to work this hard to figure out what they are plotting.

(3) It would be reassuring to rule out an effect of repeated imaging on the metrics they describe here. Longitudinal imaging of the same duration without enucleation would be the best control. Alternatively, they do have multiple baseline measurements that they collapse into one value in most of their plots.

(4) The discussion is very long. They spend a lot of time trying to relate their findings to the larger literature on visual deprivation, but because of differences in paradigms (enucleation, laser ablation, visual deprivation, binocular vs monocular) and differences in measures (see point 1), it's hard to draw conclusions. In my view, the manuscript would benefit from less speculation about plasticity mechanisms and more discussion of the strengths and weaknesses of their approach.

Reviewer #1 (Public review):

Summary:

This study uses an encoding model approach to compare a range of different deep learning models in predicting functional MRI data, collected while participants played the game "Super Mario Bros" inside the scanner. The fMRI data is rich, within-subject data, with around 15 hours of gameplay for each of five participants who took part in the study. A range of models are compared, including deep RL models (PPO), behaviour cloning (imitation learning), supervised visual models (ResNet), and untrained but structurally equivalent models. The main metric of model comparison is brain prediction (i.e., cross-validated R^2, and within-subject generalisation to out-of-distribution gameplay), rather than focussing on which model features are being encoded.

The core results are:

(1) The deep RL and imitation learning models show a modest improvement in prediction accuracy relative to the untrained and visual models (around a 1-2% increase in R^2). Notably, this is against a background in which the untrained model - essentially random projections of the gameplay pixels - can explain around 6 or 7% of the variance in fMRI data (Figure 2). So, the improvement in model fit is a small (but significant) one, and a major driver of prediction scores appears to be low-level visual stimulation as opposed to gameplay prediction.

(2) There is little variation across layers in prediction accuracy in the trained models. In the untrained model, prediction accuracy drops across layers. This suggests that the prediction accuracy in this untrained model results from its (early-layer) representations being closer to what is presented on screen - as the random weights move the untrained model's representation away from sensory features, it becomes less predictive of the brain. In a trained model, meaningful representations are maintained in deeper layers - and interestingly, there is no clear correspondence between layers of the model and layers of the visual pathway.

(iii) There is a noticeable improvement in brain prediction by both the deep RL and imitation models with model training. In other words, the 1-2% increase in R^2 mentioned in point (i) is a result of the training, rather than any other factor.

(iv) None of the models, including the untrained model, perform well in generalising to out-of-distribution data held out from the training/evaluation. This leads to the claim that the brain's encoding representations are 'brittle'.

Strengths:

(1) A major strength of the dataset is that it contains rich, extended naturalistic gameplay data within individual subjects. This mirrors some of the advantages seen in other naturalistic datasets (e.g., natural scenes dataset, storybook listening, video watching) - but there are very few examples of such data where the subject is controlling or generating the behaviour in the naturalistic task. This allows potentially new questions to be asked about how these representations are learned across time, within individual participants.

(2) A further strength of the manuscript is the clarity with which the aims and hypotheses are articulated in the introduction, and evaluated/discussed throughout the paper. This provides a clear set of objective criteria against which to evaluate the performance of the resulting models; the paper is also written in a very clear and honest way, in that some of the a priori hypotheses are not supported - this makes for a more transparent report than one written in an a posteriori manner.

(3) Finally, although the results in comparing different models are perhaps not as impressive as one might have hoped, the authors have been quite careful in making the models comparable in terms of their architecture and number of parameters, etc. This means that any variation in prediction is likely attributable to the different objective functions used to train the models, rather than other features of the model architecture.

Weaknesses:

(1) The work is currently framed as "training neural networks from scratch...leads to brittle brain encoding" - but I'm not sure that the results fully support this. First, the brittleness is still present in the untrained network (i.e., random projections of pixels), as shown in Figure 5b. This implies that the brittleness may not be a consequence of the network training, but of overfitting to the encoding (ridge regression) model of the fMRI data (as the authors acknowledge when presenting these results). I would instead encourage the authors to shift the emphasis slightly towards the (modest) improvement in prediction using the RL/imitation objectives, and/or the (similarly modest) improvement in prediction with training, rather than foregrounding the brittleness of the encoding.

(2) While the analyses of how model prediction improves with training are nice, it is a shame that there is no consideration of how prediction improves (or otherwise) across the training of the participants. Do participants improve across the 15 hours of gameplay - or do they, for instance, become more predictable by the imitation learning model? Is this more true in the naïve participants than those with extensive past experience of Mario? And does this in any way lead to better alignment with model predictions across sessions? These all seemed like natural questions that could benefit from the unique longitudinal nature of this dataset, and it seemed a shame that they were not touched upon at all.

(3) While there is little variation between the models in terms of predictive performance, it is currently a little unclear whether this is simply due to fitting a set of highly parameterised models to the data, or because the models are themselves fundamentally similar in their representations. One way to address the latter point might be to perform some kind of RSA or CKA (Kornblith et al, arXiv 2019; Williams et al, bioRxiv 2024) across the layer representations within-model, and between-models, to ask how similar (or different) the learned representations are between the different models used for fMRI prediction.

Reviewer #1 (Public review):

This study adds important data identifying how ocular motor neurons are transcriptionally specified and identifies additional genes important in ocular motor neuron function. The evidence supporting the claims is convincing, with bulk and single-cell RNA sequencing as well as functional testing of the vestibulo-ocular reflex. This work will be of interest to developmental biologists and eye movement specialists.

Gershowitz, Hamling, et al investigate genes that specify specific cell populations within cranial motor nuclei III and IV, which control eye movements, by bulk and single-cell RNA sequencing, confirmatory in situ hybridization, and functional studies of vestibulo-ocular reflex in knock-out animals. They take advantage of the timing difference in the generation of dorsal versus ventral cells to selectively mark early-born (dorsal) vs late-born (ventral) cells using the Kaede photolabile protein. They used bulk RNASeq to identify differentially expressed genes between the two populations (which innervate different extraocular muscles). They next used single-cell RNASeq to further identify specific subpopulations of motor neurons and identify 3 main clusters, which broadly map to dorsal CNIII, CNIV, and ventral CNIII. They show that the differentially expressed genes identify subpopulations of neurons, rather than reflecting temporal changes related to cell age via a series of in situ hybridizations across ages. Finally, they show that knock-out of Sim1a, which is unregulated in dorsal nIII neurons, leads to decreased vestibulo-ocular reflex, despite a normal number of neurons in nIII. They tested the knock-out of two other differentially expressed genes, nav2a and onecut1, but found both normal cell number and normal vestibulo-ocular reflex.

The conclusions of this paper are well supported by the data. As the authors acknowledge, additional experiments would add to the interpretation. Since the Sim1a mutants have normal cell numbers, the authors hypothesize that axon guidance may be disrupted, leading to the phenotype. This could be relatively easily assessed using the Isl1-GFP transgenic line and examining innervation patterns in the extraocular muscles. Additionally, testing horizontal eye movements and eye movements in response to visual, rather than vestibular, inputs would further refine the phenotypes and perhaps identify eye movement abnormalities in the mutant fish with normal VOR.

More information on why these specific genes were prioritized for functional testing would be helpful, as it is unclear why these three genes were the top candidates.

The authors should also include a discussion of other subtypes of oculomotor neurons, beyond which muscle they innervate. For example, there are oculomotor neurons that form single neuromuscular junctions on fast, singly-innervated fibers, and there is a separate pool of motor neurons that innervate the slow, multiply-innervated fibers. It would be interesting to note if there were any gene expression differences within the clusters that might represent this subdivision of neurons.

This data is likely to be of great use to the field in further studies of cranial motor neuron biology.

Reviewer #1 (Public review):

Summary:

In this article, the authors couple a 3d vertex model to the extracellular matrix and include activity through contractile springs at the edge. They study, sequentially, the distribution of shear stresses in liquid and solid spheroids, the correlation between stress and cell shape, and the spatial distribution of stresses. The authors find that stresses are higher in solid spheroids (somewhat unsurprisingly), but that the stress distributions are wider in the fluid spheroids. Moreover, stress and shape are not correlated with each other in solids (that seems to be due to vertex model peculiarities), but they are for liquids. In contrast, for solids, the stresses are concentrated at the interface.

The authors attribute a lot of the phenomenology to strain-stiffening properties of vertex models as being akin to a network model (correctly in my opinion). Then they strain individual cells and confirm this link, though I missed any explanation of how they did this. Would it have to be within a medium for computational consistency?

Finally, they generate an extended vertex model, where they replace the single face linking cells with a double face and mechanoresponsive springs. This allows for stronger coupling of individual cell motion to eventual movement out of the spheroid.

Strengths:

Coupling a three-dimensional vertex model to the extracellular matrix, modelled as a crosslinked fiber model, is a computational tour-de-force. Adding activity through fluctuations at the interface is also of the correct symmetry (stresses), instead of the self-propulsion which has been used by other authors, and which is not compatible with Newton's 3rd law. This also allows for accurate back-and-forth mechanical coupling between the cells and the ECM.

I would like to highlight that deriving vertex model stress tensors in full three dimensions is an open problem due to the complex topology. Any progress is valuable, and decomposing things into tetrahedra like here will allow for connections with, in particular, finite element approaches. Therefore, adding some of these results (eq. 13) to the main text would strengthen the paper in my opinion.

Adding the nonlinear springs to the VM in the 3rd act is a good idea, and a first step to mechanical feedback. One might argue that at this point, removing the vertex model part would even be an option.

Weaknesses:

The paper is written in a very qualitative manner, with all of the model equations and analysis hidden in the supplementary information. I do not understand this choice, as it makes things fuzzy and hard to read. The conclusion is also very long and simply reiterates the previous points.

At the same time, this paper is rather thin on new results and reads more like a handful of new simulations carried out using the method established in [10] (from largely the same authors). Moving some of the actual results to the main text would help, in particular, the 3d stress formulation and the definitions of different measures.

Vertex models also have a very clear limitation: They cannot model the transition from a confluent to a non-confluent tissue, and individual cells or groups of cells leaving the spheroid. Even having a surface and having significant deformations of the surface are numerically dicey, so the current model is at the edge of what is feasible. The model as written can only do "invasion" by a single cell moving outward, and then another following it a bit (or not).

I strongly suspect that further progress on 3d cell models will need particle-based models or models where cells are fully meshed surfaces (some of which are in development currently).

However, none of these problems is mentioned anywhere in the text. The authors also do not review the increasingly broad zoology of other models.

Reviewer #1 (Public review):

Summary:

In this paper, the authors conduct both experiments and modeling of human cytomegalovirus (HCMV) infection in vitro to study how the infectivity of virus (measured by cell infection) scales with the viral concentration in the inoculum. A naïve thought would be that this is linear in the sense that doubling the virus concentration (and thus the total virus) in the inoculum would lead to double the fraction of infected cells. However, the authors show convincingly that this is not the case for HCMV, using multiple strains, two different target cells, and repeated experiments. In fact, they find that for some regimens (inoculum concentration) infected cells increase faster than the concentration of the inoculum, which they term "apparent cooperativity". The authors then provided possible explanations for this phenomenon and construct mathematical models and simulations to implement these explanations. They show that these ideas do help explain the cooperativity, but can't be conclusive as to what is the correct explanation. In any case, this advances our knowledge of the system and it is very important when quantitative experiments involving MOI are performed.

Strengths:

Careful experiments using state-of-the-art methodologies and advancing multiple competing models to explain the data.

Weaknesses:

Minor weaknesses in explaining the implementation of the model. However, some specific assumptions, which to this reviewer were unclear, could have substantial impact on the results. For example, whether cell infection is independent or not. This is expanded below.

In the revised version, the authors address almost all of these minor weaknesses, strengthening the paper and its reproducibility.

Suggestions to clarify the study:

In the revised version, the authors carefully consider these suggestions and provide further details, clarifications and even some new results. Regarding the question of how infection of a cell with one virus could lead to lower probability for a secondary infection, I think that it is possible that infected cells activate antiviral programs that lead, for example, to lower expression of surface receptors. This has been considered at least in hepatitis C virus infection. However, this is a minor point.

Overall, I think the revised version provides a sound study with relevant conclusions, and I thank the authors for their thoughtful consideration of my previous comments.

Reviewer #1 (Public Review):

This study by Charendoff et al provides interesting observations related to global histone hypermethylation in host cells, during Chlamydia trachomatis infections. The core observation they report is that the host histones are highly hypermethylated during infection, and this appears to be an amplifying effect due to continuous inhibition of demethylases, in part due to a metabolic shift in the host where succinate amounts (which inhibit demethylases) increases. The authors claim specifically due to the bacteria, since antibiotic treatment prevents histone hypermethylation (but leaves you wondering about cause/consequence correlations).

The core observation of hyper methylation is very interesting, and well documented. There are a number of points to consider though in order to fully substantiate the findings, and close out loose ends. My comments are broad - and built around the interpretations (vs the data presented).

(1) Related to observations coming Fig 1C etc, and connecting to Fig 3 - the hyper methylation appears to be across different protein arg/lys residues - and is not histone specific. So, is it just a consequence of high SAM pools and flux in infected cells? i.e. the bacterial infection increases SAM pools in cells, and provides an increase in substrate pools for the methyltransferases, leading to protein hyper methylation. The approach used here only measures steady-state SAM amounts (and not SAM flux or utilisation). For example, reduced SAM amounts in nuclei could be due to increased utilisation of SAM. The experiments done with the demethylase does not actually answer this question - if you decrease demethylase activity, you will get an increase in net methylation. The authors see an increase in net methylation in the infected cells - this would suggest that in addition (or perhaps primarily) to reduced demethylase activity, there could be much higher SAM utilisation/flux. Again, the over expression of JMJ proteins does not resolve this problem.

(2) Adding to this - what happens to SAM pools in the cells treated with the inhibitors? This actually may not look like the slightly reduced SAM pool observed in infected cell nuclei. Also, what is the SAM/SAH ratio (a very useful indicator of methylation activity).

(3) There is a correlation/implication issue here in Fig 2 - cells with C. trachoma's infection show hyper methylation. But these are the only cells with high C. trachomatis. So it is a bit ingenious to say that histone hyper methylation correlates with bacterial proliferation. The cells without bacteria don't have hyper methylation - and that does not have anything to do with the bacterial proliferation.

(4) The claim that demethylase activity is down in infected cells again comes primarily from the increased succinate (2-fold) amounts in infected nuclei - and then correlated with experiments where succinate, (permeable) a-KG are supplemented in excess. While I personally like the hypothesis that the hypermethylation might be a result of an imbalance in cofactors (succinate vs a-KG) in infected cells, the data presented is very premature to make that conclusion. Again, steady state measurements of only succinate cannot provide a clear answer to that question. For example, is there a clear allocation/flux difference (between a-KG, and leading out to glutamate/glutamine, vs flux through the TCA and increased succinate accumulation? Is there a bottleneck/build-up of succinate in cells that might lead to the increase in nuclei? This also opens another direction of possible regulation - increased histone succinylation. When you see a large increase in succinate in the nucleus, before looking at demethylase activity - it becomes obvious if succinate itself increases histone succinylation (through HATs).

(5) What might the authors hypothesise about why this hyper methylation happens? It appears in some ways that hyper methylation happens - potentially due to a metabolic bottleneck that the bacteria triggers (and there is a build-up of SAM and/or succinate, and altered flux out of a-kg). The methylation is just a visible outcome - but may not be central to pathogenesis or viability.

Reviewer #1 (Public review):

Summary:

This study addresses an important question in reinforcement learning and metacognition by distinguishing value confidence from decision confidence and testing how each is computationally represented. The findings are significant because they suggest that value confidence is well captured by Bayesian uncertainty, whereas decision confidence reflects a hybrid computation combining probability correct with broader value certainty. The evidence is promising, supported by multiple datasets and model comparisons.

Strength.

(1) A major strength of the study is that the authors test their hypotheses across multiple datasets, including previously published datasets and newly collected data. This broad empirical approach increases the generality of the findings.

(2) The Bayesian model of value confidence has a clear theoretical basis. The proposed hybrid model of decision confidence is also intuitive. It appears to capture important aspects of the decision confidence data.

(3) The paper provides a useful framework for linking how certainty about value estimates guides the subsequent choice and the corresponding decision confidence.

Weakness

(1) The conceptual link between value confidence and decision confidence is not yet fully established. The manuscript argues that overall value certainty contributes to decision confidence, but this conclusion is based largely on the latent variable that the model infers from the decision confidence experiment alone. A more direct test would require measuring value confidence and decision confidence within the same participants and task, and analysing how these two types of confidence interact.

(2) The individual-difference analyses in Figure 5 are methodologically challenging. The predictors used in these analyses are derived from model fits to the behavioural data and are then correlated to behaviour in the same task. This creates a risk that correlations inevitably arise. Thus, it does not assure that correlations are cognitively meaningful.

(3) The model recovery results suggest that some candidate models are not clearly distinguishable.

(4) The manuscript would benefit from clearer explanations of why specific models capture particular behavioural patterns.

(5) The claim that value confidence modulates the exploration-exploitation trade-off should be interpreted carefully, because the model uses global uncertainty across both options, not option-specific value confidence.

Reviewer #1 (Public review):

This study provides evidence that the apicoplast-locaized isoform of acyl-carrier protein (ACP) has acquired important non-enzymatic functions in the malaria parasite. Previous studies have shown that the apicoplast-located FASII-dependent pathway of fatty acid synthesis is not essential in Plasmodium blood stages. In contrast, genome-wide knockout studies suggested that ACP, a key protein in this pathway, is essential in these stages, indicating that it may have additional non-canonical functions. In this study, the authors confirm that ACP is essential in Pf blood stages (using both apicoplast IPP rescue and conditional knockdown); show that this essential function requires modification with 4-phosphopantetheine and use proximity biotinylation and complementary immunoprecipitation pull-down approaches to provide compelling evidence that ACP binds to and stabilizes the apicoplast-located isoform of pyruvate kinase II. Notably, these interactions appear to differ from those associated with the binding of mitochondrial isoforms of ACP to proteins involved in Fe-S biosynthesis. Loss of ACP was shown to lead to a decrease in PKII levels and apicoplast DNA/RNA synthesis, consistent with loss of NTP synthesis in this organelle. The data are clear and very well described, and the findings represent a significant advance in our understanding of metabolic regulatory mechanisms in apicomplexan apicoplast studies.

Strengths:

The study uses a variety of complementary genetic approaches to demonstrate the essentiality of ACP and the enzyme involved in its activation with 4-PP in Pf blood stages, demonstrating that the ascribed non-enzymatic function is mediated by holo-ACP. Similarly, a number of complementary biochemical approaches, including proximity biotinylation, immunoprecipitation, and co-expression of PfACP and PK-II in a heterologous bacterial expression system, are used to confirm the physiological significance of the PfACP and PK-II interaction. The study also reports additional findings, such as the independence of P. faciparum blood stages on exogenous (media) fatty acids, indicating that intracellular stages can salvage all of their requirements from the red blood cell.

Weaknesses:

Overall, this is a very strong study. While questions remain around the function of other apicoplast ACP-interacting proteins detected in this study, I don't have any suggestions for significant improvements.

Reviewer #1 (Public review):

Summary:

In this manuscript, Duss et al. use several complementary and state-of-the-art strategies to characterize the effects of norepinephrine release from LC axons on post-synaptic cell types in the hippocampus. While a large body of research supports an important role for NE signaling in hippocampal function, the precise role by which NE promotes these effects remains poorly elucidated, in large part due to the complexity that adrenergic subtypes can be expressed in a variety of cell types and promote a variety of responses. Towards assessing this, the authors first establish an optogenetic strategy by which their delivery stimuli mimic endogenous activation of LC in 'moderate' and 'high' acute stress events, using NE sensors to titer stimulation patterns to similar levels of NE release. They then conduct a series of 2P imaging experiments in mice and compare response properties of various cell types in the hippocampus (excitatory and inhibitory neurons, and astrocytes) when the animal is 'naturally' or optogenetically aroused (via activation of the LC). The results are surprising. Whereas natural arousal causes activation of astrocytes, pyramidal cells, and interneurons, optogenetic activation of the LC does almost the opposite, with only astrocytes responding positively. Another important finding from the study is that astrocytes seem to be the most responsive cell type in the hippocampus to NE release, suggesting they could be key components for downstream functional effects of NE release in this brain region.

Strengths:

(1) The study was methodically done with respect to the characterization of how optogenetic parameters related to levels of NE release. Also, the analysis of their calcium imaging of various cell types in the hippocampus was very comprehensive.

(2) Related, their discovery that cell types in the hippocampus respond differently to NE release, while not a completely unexpected finding, is something that has not been addressed experimentally in such a direct way before (to my knowledge).

(3) Their finding that optogenetic stimulation of the LC produces opposing results to when these cells are naturally activated has wide implications for the LC field and potentially beyond.

Weaknesses:

I was surprised that no efforts were made to further assess what might be causing this discrepancy in hippocampal responses to optogenetic vs. natural activation of the LC. Some experiments that I felt were missing:

(1) The authors go to great lengths to measure NE release in a variety of arousing conditions (tail lift, foot shock, 5Hz LC opto, 20Hz LC opto), but then in their 2P imaging, they're comparing the opto results to a 'natural' arousal state defined as when the mice were in motion. Maybe I missed it, but I wasn't sure that they ever checked the level of hippocampal NE release in this running state, similar to what they did in the other arousal conditions. Thus, it wasn't clear to me how comparable this state was to the optogenetic stimulation.

(2) The authors do a nice experiment to show that increases in the hippocampal NE sensors are dependent on LC activity via optogenetic inhibition of the LC (Figure 1, Supplement 3). It seems like a missed opportunity to include a similar strategy in their 2P testing, to assess whether the differing responses of pyramidal cells, interneurons, and astrocytes are truly due to NE release. I could imagine it might be difficult to precisely time LC inhibition with periods of movement, but I imagine that mice would still run even if the LC is inhibited.

Reviewer #2 (Public review):

The study by Chen, Deng et al. aims to develop an efficient viral transneuronal tracing method that enables retrograde tracing in larval zebrafish. The authors utilize pseudotyped rabies virus that can be targeted to specific cell types using the EnvA-TvA system.

Pseudotyped rabies virus has been used extensively in rodent models and, in recent years, has begun to be developed for use in adult zebrafish. However, compared to rodents, the efficiency of spread in adult zebrafish is very low (~one upstream neuron labeled per starter cell). Additionally, there is limited evidence of retrograde tracing with pseudotyped rabies in the larval stage, which is when most functional neural imaging studies are conducted in the field. In this study, the authors systematically optimized several parameters for rabies tracing, including rabies virus strains, glycoprotein types, temperatures, expression construct designs, and the elimination of glial labeling. The optimal configurations developed by the authors are up to 5-10-fold higher than more commonly used configurations.

The results are compelling and support the conclusions.

Reviewer #1 (Public review):

Summary

The authors apply dynamic representational similarity analysis (dRSA), a method introduced in de Vries and Wurm 2023, to source-reconstructed MEG data from 40 participants who viewed ballet dancing sequences under three conditions: normal viewing, up-down inversion, and temporal piecewise scrambling. In normal viewing, they replicate their previous finding of a hierarchical pattern of leading-edge neural representations, with view-invariant body motion represented earliest in time (around 500 ms before the corresponding stimulus state), followed by view-dependent body motion (around 200 ms) and pixelwise motion (around 150 ms). Inversion selectively attenuates the leading-edge representation of view-invariant body motion while enhancing view-dependent body motion. Scrambling abolishes all leading-edge motion representations and instead increases post-stimulus representations of body posture. The authors interpret these findings as evidence that biological motion perception relies on a hierarchy of priors operating within a predictive-processing framework, with inversion specifically disrupting holistic priors and scrambling disrupting kinematics priors.

Strengths

The empirical work is careful and technically ambitious. The dRSA framework introduced in the 2023 paper is a useful methodological contribution to the study of dynamic neural representations, and the present manuscript extends it in well-motivated directions. The dataset is substantial: 40 participants, source-reconstructed MEG, three within-subject conditions. The replication of the 2023 normal-condition findings in an independent 40-subject sample is solid, which is increasingly rare and welcome in the field. The inversion and scrambling manipulations are well-motivated, and the conditions are matched on stimulus identity. Principal component regression is used appropriately to handle the genuine challenge of correlated and autocorrelated stimulus features, and the authors validate this choice through simulations. Eye position is included as a covariate and successfully regressed out, addressing a common confound in MEG decoding work. Behavioral catch trials demonstrate that participants attended to the stimuli across conditions. Both frequentist and Bayesian statistics are reported with appropriate corrections for multiple comparisons. The inversion result, in particular, is striking, and the asymmetry between view-invariant and view-dependent representations is informative.

Weaknesses

The central interpretive step in the manuscript treats a negative-lag dRSA peak as direct evidence for active hierarchical predictive inference. The data are equally consistent with at least three other accounts that the manuscript does not engage with, and the conclusion is therefore stronger than the data support.

First, the leading-edge dRSA signature is a natural consequence of nonlinear temporal integration of autocorrelated stimulus features. A long line of work from the Winawer and Grill-Spector labs (Zhou et al. 2018, Zhou et al. 2019, Stigliani et al. 2017, Kim et al. 2024) has established that the human visual cortex implements compressive temporal summation with delayed divisive normalization and that temporal integration windows progressively increase from early to higher visual areas. A nonlinear-summation response to an autocorrelated feature encodes deviations from the recent baseline. For smooth trajectories, this is essentially a local derivative, and the derivative inherits the trajectory's leading edge as a free consequence - no predictive machinery required. The integration-window hierarchy that Kim et al. (2024) recovered from voxelwise spatiotemporal pRFs maps onto the 150 / 200 / 500 ms hierarchy reported here almost one-for-one. That alignment is unlikely to be coincidental and deserves explicit treatment.

Second, the experimental design places participants firmly in the regime where Dayan's successor representation (SR) predicts that the brain holds a precompiled associative cache of trajectory structure. Each unique sequence is presented approximately 47 times across the experiment. An SR in Dayan's original formulation is a precompiled lookup table, not an online inference engine - querying it during familiar trajectories produces leading-edge representations through passive associative retrieval, mechanistically distinct from active prediction despite producing similar signatures. The senior author's own lab has demonstrated SR-like representations in V1 (Ekman, Kusch, de Lange 2023 eLife), but this paper is not cited or engaged with in the present manuscript despite its direct relevance.

Third, the canonical computational model of biological motion perception (Giese and Poggio 2003 Nat Rev Neurosci) is a fully feedforward template-matching architecture that predates the predictive-coding framing of biological motion. It accommodates the inversion effect (templates tuned to upright statistics), the hierarchy of timescales (graded leaky integrator time constants), and the scrambling effect (broken sequence-neuron activation) without invoking generative models or prediction errors. The manuscript cites Giese-tradition work for the inversion-effect literature but does not engage with the model itself, even though it is the field standard.

The inversion result, while empirically striking, has a simpler interpretation than the one offered. Inversion makes viewpoint-invariant body computation fail because the underlying machinery is tuned to upright body statistics. A weaker representation produces a weaker dRSA signature at every lag, including the leading edge - no appeal to priors in the active-inference sense is required. The view-dependent enhancement under inversion fits this reading naturally: when viewpoint abstraction fails, processing falls back to viewpoint-specific representations that remain extractable. The manuscript implicitly acknowledges this when it states that "predictions were channeled to the level at which prediction was still possible," but does not notice that this concession softens the strong predictive-coding inference.

The scrambling result is internally awkward on the predictive-coding framing. The paper acknowledges that pixelwise motion prediction should, in principle, survive 200-500 ms scrambled segments (typical latency around 150 ms) but reports that it does not. The proposed save - that segments are "too short to start up prediction" - undercuts the framework, since by the same logic, most of normal viewing would also be pre-prediction. A cleaner reading is that scrambling destroys the temporal autocorrelation of stimulus features, which is the prerequisite both for nonlinear-summation neural responses to produce leading-edge representations and for SR-style associative retrieval to operate.

A further concern is that the experimental design and analysis pipeline are structurally biased toward producing the cleanest possible predictive signature. The 14 stimuli are repeated extensively, and trials are averaged across repetitions before dRSA is computed, filtering out exactly the variability that would distinguish online prediction from amortized retrieval. The 2023 paper reports a control comparing the first and last thirds of the experiment, but this test is in the post-saturation regime for any plausible associative-learning rate and does not actually adjudicate the question. A first-exposure or first-run analysis would be diagnostic. Finally, the behavioral task changed between the 2023 paper and the present manuscript. The earlier paradigm asked participants to recognize the current motion ("arms moving up?"), while the present paradigm asks participants to judge whether an occluded video continues correctly. The latter explicitly demands prediction. This change transforms the experimental context from naturalistic viewing into one that actively incentivizes predictive engagement, potentially inflating the very signatures the paper interprets as spontaneous prediction.

The 2023 Nature Communications paper actually navigated these interpretive questions more carefully than the present manuscript does, explicitly stating that the approach "does not provide conclusive evidence for predictive processing/coding theory but leaves the door open for related theories such as adaptive resonance or Bayesian inference without predictive coding." The current manuscript would benefit from restoring that epistemic discipline. The data and methods are valuable; the interpretive frame is overstated relative to what the evidence supports.

Impact and utility

The dataset and dRSA framework are useful contributions to the study of neural representation of dynamic stimuli, and the inversion and scrambling conditions open productive lines of inquiry. The interpretive over-commitment to predictive processing risks limiting the paper's reach into adjacent literatures - temporal integration, successor representations, template-matching biological motion models, encoding-model approaches - where the findings could land productively. With a more pluralistic interpretive frame, this work would speak to a substantially broader audience and connect more naturally with existing mechanistic accounts of dynamic visual processing.

Reviewer #1 (Public review):

Summary:

Dhillon and Lewis present an optical approach to record single CRAC channel activity, overcoming the long-standing barrier imposed by the channel's extremely small unitary conductance. By fusing HaloTag to Orai1, labeling with JF646-BAPTA, and combining TIRF microscopy with whole-cell voltage clamp (Patch-TIRF), the authors achieve genuine single-channel resolution. A central contribution is the recognition that JF646-BAPTA undergoes reversible photophysical blinking that can be readily mistaken for gating events. The authors exploit the multi-dye labeling of hexameric Orai1, combined with voltage-clamped definition of open and closed fluorescence levels, to distinguish true gating transitions from blinks. The result is the first kinetic characterization of single CRAC channel openings activated by STIM1, reporting multiple open and closed states with durations from about 0.1 s to tens of seconds, predominantly high open probabilities ({greater than or equal to} 0.7), and an unexpected population of "silent" channels that co-localize with STIM1 but show no detectable activity over the observation window.

Strengths:

The work is technically rigorous, and the controls are appropriate. The integration of patch-clamp voltage control with TIRF imaging is a thoughtful methodological choice that defines the open- and closed-channel fluorescence reference levels with precision, providing a quantitative framework that the field has lacked. The use of the non-conducting Orai1-E106A mutant as a specificity control (Figure 4C) is exactly the right experiment, and the demonstration that JF646-BAPTA signals require Ca²⁺ flux through Orai1 itself anchors the entire approach. The identification and characterization of JF646-BAPTA blinking (Figures 2 and 3) is a significant contribution in its own right. The authors show clearly that the dye exhibits long-lived dark states and that transitions to zero fluorescence, rather than to a finite calcium-free baseline, are diagnostic of blinking rather than channel closure. This caveat has immediate implications for the interpretation of recent work using the same dye on other calcium-permeable channels, and will recalibrate the broader field of HaloTag-based single-channel optical recording. The kinetic analysis itself reveals something that was previously inaccessible: seconds-long open times, multi-state gating behavior, and a population of channels that co-localize with STIM1 yet remain electrically silent. These findings are physiologically meaningful and would not have been detectable by macroscopic electrophysiology. Overall, an outstanding study.

Weaknesses:

The manuscript would benefit from a small number of additional analyses of the existing data and modest refinements to the presentation. The discrete-channel interpretation of the intensity histogram in Figure 6C, the open probability distribution in Figure 8C, and the assignment of the "silent" channel population are all interesting and likely correct, but each rests on assumptions that the authors are well positioned to test directly using data already in hand. Brief additional discussion of the dynamic range of JF646-BAPTA in situ and of how the temporal resolution of the recordings shapes the inferred kinetic model would also help readers calibrate the findings.

None of these points challenges the central claims of the paper, and none requires new experiments.

Reviewer #1 (Public review):

Summary:

This manuscript deals with the ability to identify material hardness from the vibrations induced by single light taps on that surface. Psychophysical tests of human perception under varying conditions of modified fingertip compliance and/or externally imposed vibrations demonstrated that total spectral energy was the main determinant of perceived hardness and that perception of increased hardness can be induced by adding external vibration at the time of contact.

Strengths:

The experiments are well-reported and the data potentially useful, but much narrower than is implied by the (provisional) title and abstract. Their potential application to tactile perception in virtual reality seems promising, but the largely unexplored need for synchronization with physical contact and modulation with velocity and force of that contact seems likely to complicate proposed applications to prosthetics and telerobots.

Weaknesses:

(1) The authors have confused discriminability with perception. The sense of touch is derived from several different types of mechanoreceptors and processed into several dimensions of haptic perception. The fact that subjects can rank surface material hardness correctly when requested to focus on that alone does not mean that they rely on total spectral energy normally or that total spectral energy is normally perceived as surface material hardness, as opposed to other aspects of materials, such as their surface texture. They have not considered the effects of more complex features of most surfaces, such as curvature, lamination or other exploratory movement strategies besides light taps.

(2) Discussion section. Lines 262-264 are overstated. Dynamic spectral energy can be used to modify perceived hardness when exploratory movements are limited to taps that are unlikely to generate any other useful cues, such as skin deformation or proprioception. The authors have not explored what happens if there actually are conflicting cues in non-vibratory modalities. There are many different examples from sensory psychophysics of percepts that arise from taking the mean of conflicting cues (e.g. stereophonic sound localization) and others that arise from a dominant modality (e.g. self-motion perception from visual flow fields, vestibular signals and proprioception).

The authors have ignored the substantial literature on artificial tactile sensors and their ability to identify texture, hardness and other haptic properties of materials. These have emphasized the importance of the many types and parameters of exploratory movements, which were loosely specified and not quantified in these studies.

See:

Li, Q., Kroemer, O., Su, Z., Veiga, F. F., Kaboli, M., & Ritter, H. J. (2020). A Review of Tactile Information: Perception and Action Through Touch. Ieee Transactions on Robotics, 36(6), 1619-1634. doi:10.1109/tro.2020.3003230.

Fishel, J. A., & Loeb, G. E. (2012). Bayesian exploration for intelligent identification of textures. Frontiers in Neurorobotics, 6(4). doi:10.3389/fnbot.2012.00004

Fishel, J. A., & Loeb, G. E. (2012). Sensing Tactile Microvibrations with the BioTac - Comparison with Human Sensitivity. Paper presented at the IEEE/RAS-EMBS International Conference on Biomedical Robotics and Biomechatronics, Rome.

(3) Introduction (lines 23-31) and Discussion (lines 296-298). The notion that tactile receptors are "frequency tuned" is something of a straw man. Different receptor types are preferentially sensitive to different broad spectral bands, but it has long been known that they can be driven by larger stimuli outside those bands and that humans have very limited ability to discriminate actual frequency of tactile vibration (as opposed to auditory pitch), particularly for frequencies greater than the maximal one-to-one firing rate of neurons (~200-300 Hz). Conversely, fine onset timing of spikes in tactile afferents appears to be available from brief contact taps to identify features other than hardness; see:

Johansson, R. S., & Flanagan, J. R. (2009). Coding and use of tactile signals from the fingertips in object manipulation tasks. Nature Reviews Neuroscience, 10, 345-359.

Pruszynski, J. A., Flanagan, J. R., & Johansson, R. S. (2018). Fast and accurate edge orientation processing during object manipulation. eLife, 7, e31200.

(4) Methods section. The Lofelt L5 actuator used to apply vibrations to the fingernail is rather large for use on multiple fingers of a haptic display. Do the authors know of any more compact technology with the requisite power and frequency response? One of the most useful contributions of this paper is to suggest that those details matter relatively little, which opens up more compact technologies such as piezoelectric actuators.

(5) Methods section. It is good that headphones were used to block and mask audible tapping sounds, which are known to be capable of generating tactile illusions (Jousmäki, Veikko, and Riitta Hari. "Parchment-skin illusion: sound-biased touch." Current biology 8.6 (1998): R190-R191). But that suggests that hardness might be signalled by precisely timed acoustic stimuli, which would be much easier to deliver than fingertip vibration.

Reviewer #1 (Public review):

Summary:

This study develops a novel theory to account for various aspects of dopamine signals, particularly dopamine ramps. They propose that dopamine reward prediction error (RPE) signals are generated by a dual-process learning system in which values inferred by a model-based system enter the RPE asymmetrically into the update target but not the prediction (equation 6). The work offers specific, mechanistic explanations of Krausz et al. (2023) and Guru et al. (2020), Kim et al. (2020) by maintaining an RPE interpretation, and presents an alternative to the state-uncertainty account in Mikhael et al. (2022) that doesn't require the asymmetric uncertainty assumption Mikhael needs, using Campbell et al. (2025) in a thoughtful way. The asymmetric-RPE idea is clean and well presented. Overall, this study makes an important contribution to the field.

Strengths:

The theory is relatively simple and intuitive. It addresses a long-standing controversy or mystery in the field of dopamine.

Weaknesses:

(1) The biggest outstanding question is what V_TD does - letting V_MB drive everything would seem to produce much of the same outcomes in the settings discussed here. The discussion suggests that in situations where there is little contribution of the model-based system, the backpropagating bump is a feature (e.g. Amo et al.). It would be interesting to see if this is a true outcome of the model, potentially by varying the arbitration parameter k. This is an interesting alternative account from eligibility trace explanations of the lack of backpropagating bump in some experimental settings.

(2) The model-based accounts are quite simplistic, and this should probably be acknowledged - it does help delineate their contribution, but in the model, only the goal-reward value is updated; everything else is a known computation. Perhaps engage more deeply with Sagiv et al?

(3) The application of Campbell et al. (2025) to push back on Mikhael (lines 253-259) is interesting: if striatum to VTA implements TD via synaptic delays such that V(s_t) is a delayed copy of V(s_{t+1}), then state uncertainty is necessarily shared between the two terms in the RPE, defeating Mikhael's required asymmetry.

But the same circuit logic creates tension for the dual-process model. It seems they are proposing that the frontal cortex projects V_MB into VTA dopamine neurons (as proposed in 3.1 and the Discussion) and adds to the prediction error derived from the biphasic filtering of value. But the biphasic idea (and data of Campbell et al.) implies that the V(t+1) and -V(t) come from the same source and are proportional. Adding the V_MB term is akin to adding a positive bias, breaking the optimality of the TD error for predicting value and predicting over-learning of cached value. It is worth considering whether V_MB passes through a similar filter - I am not sure if it is fatal if V_MB contributes somewhat to the negative term of the update error.

(4) A few places where the predicate of the conclusion needs more care. The "normative" framing throughout 3.2 and the Discussion is normative conditional on the architecture already including a separate cached system that needs to converge to the true value function and on a system in which the model based is learnt much faster - see comments about learning rate parameter later.

(5) Kim et al. is cited heavily as a data source for Figure 4, but is never engaged with as a theoretical alternative, even though Kim et al. explicitly argued that an appropriate state representation makes standard TD compatible with ramps and the teleport responses. That is, Kim et al. is already a TD account of these phenomena, and doesn't require a second learning system. The introduction and Mikhael discussion treat the field as if the choice were between "dopamine = value" (Hamid, Howe, Mohebi) and dopamine = RPE-with-special-conditions (Mikhael, Kato-Morita), but Kim et al.'s framework is also dopamine = RPE. Two specific places this matters: (i) Figure 4 currently demonstrates that the dual-process model reproduces the Kim teleport results, but Kim et al.'s framework also reproduces them - the figure doesn't distinguish the two, and I am not sure the figure gives this message cleanly. (ii) Kim et al. report that ramps develop with training over days; the manuscript should address whether the dual-process model has an alternative explanation for this, especially given the contrast with the Guru result (ramps diminishing with training over a longer timescale).

(6) The arbitration parameter k is fixed at 0.5 throughout, and the paper acknowledges this is for simplicity, but a supplementary panel sweeping k ∈ {0, 0.2, 0.5, 0.8, 1.0} on the key figures (Figure 1B convergence, Figure 2D ramp dynamics, Figure 3D Krausz updating) would be informative. At k = 0, the model reduces to standard TD; at k = 1, it's effectively V_MB-driven. I think these would be easy to add and help clarify the work this assumption is doing.

(7) Learning-rate asymmetry needs justification. The story relies on α_MB >> α_TD throughout (α_MB = 0.50, α_TD = 0.01 - a 50× ratio). With α_MB = 0.5, a single rewarded trial moves R[goal] halfway to the new value, which would predict strong dependence of dopamine ramp amplitude on the previous trial's outcome. This is testable in existing data (Krausz et al. should have enough trials to fit the exponential decay constant for trial-history dependence; Guru's swap-session data likewise), and the paper would be strengthened by explicitly deriving and checking that prediction.

(8) α_MB is dropped to 0.10 specifically for the Krausz simulation without justification in the text - Why? Either the value should be the same as elsewhere, or the paper should explain why Krausz's task requires slower MB learning. It would be good to check the robustness of the Krausz simulation - the test phase is a single set of three trials (t-2 = omission, t-1 = reward, then t = 50% rewarded) after training on a single set of 500 simulated trials (believe only one random seed is used - given the high alpha, varying this set of simulated trials seems important). Also, do they get the other result in Krausz (t-2 = reward, t-1 = omission, t = 50% rewarded)?

(9) It might be possible to fit the alpha to the Guru and Krausz simulations - this might be informative to show the range over which it varies.

(10) The Kato and Morita account is cited in the introduction but never really discussed again - it would be good to engage with this a bit more in the discussion. The rejection of the value-based accounts seems to rely primarily on Kim et al., where the value and TDRPE accounts differ, but this could be directly acknowledged, rather than absorbing credit for this into their model.

Reviewer #1 (Public review):

Summary:

The authors develop alignment methods for layer-specific widefield calcium imaging in the mouse cortex. Under the assumption that the majority of the widefield signal originates at the level of the cell bodies, different cortical layers will appear at different locations in a top-down view as a function of the curvature of the mouse cortex. The authors develop software tools to correct for this, as well as depth-dependent source blurring. Finally, they apply these tools to investigate functional connectivity differences of different neuron types and find only subtle differences.

Strengths:

The work is technically strong, the experiments well executed, and the presentation clear.

Weaknesses:

One concern I have is that the central assumption underlying the rationale for the depth correction, namely that the source of the majority of the widefield signal is the cell body, may be incorrect. Layer 5 neurons have a dense axo-dendritic plexus very close to the surface of the cortex. Given the attenuation length of visible light in tissue, as well as our own measurements (https://elifesciences.org/articles/71476#fig6s1), I suspect that the majority of the widefield calcium signal originates in the superficial axo-dendritic plexus. The authors acknowledge this possibility, but there are a few simple measurements they could make to address this more directly. If indeed, as I suspect, the majority of the calcium signal originates in the first 50 um of tissue (even when imaging layer 5 neurons), the curvature correction is counterproductive, of course. The authors could test the effect of adding brain slices of varying thicknesses on top of e.g., a layer 2/3 widefield recording. If the authors are correct, and most of the signal is from cell bodies, this should, at most, attenuate the layer 2/3 recording to the level of a layer 5 recording. Anecdotally, while doing the measurements for the figure referenced above, we have done this experiment with a 100 um thick slice, and no quantifiable calcium responses remained.

Reviewer #1 (Public review):

Summary:

The current manuscript characterizes in detail the macrophages in the thymus. The authors identify two distinct populations of thymic macrophages and describe their surface marker expression and transcriptional signatures. They also explore their ontology and kinetics of settling and persistence in the thymus and find that the TIMD4+ macrophages are derived from embryonic progenitors and self-maintain in the thymus, while the TIMD4- macrophages are derived from monocytes. Most importantly, the authors test the functional importance of thymic macrophages for T cell development using an in vitro depletion system, from which they conclude that macrophages are important for one of the earliest selection steps in T cell development - the beta selection.

Strengths:

The authors use state-of-the-art techniques, such as multiple genetically modified mice, multi-color flow cytometry, single-cell RNA sequencing, genetic fate mapping, and fetal thymic organ culture (FTOC) combined with depletion. Their work is in good agreement with prior published studies on the subject, such as Tacke et al. (PMID: 26091486) and Zhou et al. (PMID: 36449334). In addition to reproducing prior knowledge, the authors uncover novel and unexpected facets of thymic macrophage biology, such as their SpiC independence and the fact that TIMD4- thymic macrophages depend on CCR2 (Tacke et al. have shown that the overall thymic macrophage compartment is normal in CCR2-/- mice). Most surprisingly, the authors claim that thymic macrophages control an early checkpoint in T cell development, the beta selection. This has not been reported before, as beta selection is usually considered a cell-autonomous process in thymocytes that does not require input from other cells.

Weaknesses:

The thymic macrophage depletion experiments are not well controlled, and the authors' interpretation of the results is a stretch. First, the treatment depletes other cell types, most notably dendritic cells (DCs), which have well-known roles in thymic selection (though not specifically in beta selection). The authors' reasoning that macrophages are abundant in the cortex, where beta selection occurs, while DCs are enriched in the medulla, seems questionable, as the embryonic thymus typically lacks (or has very small) medulla. A second salient point is that the authors haven't ruled out direct toxicity of the dimerizer drug AP20187 on thymocytes (specifically DN cells) in MAFIA mice.

Altogether, this is a solid manuscript that largely confirms the previously established ontogeny and heterogeneity of thymic macrophages. However, the participation of thymic macrophages in beta selection needs stronger evidence.

Reviewer #1 (Public review):

Summary:

The authors use Dyngo-4a, a known Dynamin inhibitor to test its influence on caveolar assembly and surface mobility. They investigate whether it incorporates into membranes with Quartz-Crystal Microbalance, they investigate how it is organized in membranes using simulations. Finally, they use lipid-packing sensitive dyes to investigate lipid packing in the presence of Dyngo-4a, membrane stiffness using AFM and membrane undulation using fluorescence microscopy. They also use a measure they call "caveola duration time" to claim that something happens to caveolae after Dyngo-4a addition and using this parameter, they do indeed see an increase in it in response to Dyngo-4a, which is reduced back to the baseline after addition of cholesterol.

Overall, the authors claim: 1) Dyngo-4a inserts into the membrane and this 2) results in "a dramatic dynamin-independent inhibition of caveola scission". 3) Dyngo-4a was inserted and positioned at the level of cholesterol in the bilayer and 4) Dyngo-4a-treatment resulted in decreased lipid packing in the outer leaflet of the plasma membrane 5) but Dyngo-4a did not affect caveola morphology, caveolae-associated proteins, or the overall membrane stiffness 6) acute addition of cholesterol counteracts the block in caveola scission caused by Dyngo-4a.

Overall, in this reviewers opinion, after the additional experiments in the review process, all claims are now well-supported by the presented data from electron and live cell microscopy, QCM-D and AFM.

Significance:

A number of small molecule inhibitors for the GTPase dynamics exist, that are commonly used tools in the investigation of endocytosis. This goes as far that the use of some of these inhibitors alone is considered in some publications as sufficient to declare a process to be dynamin-dependent. However, this is not always correct, as there are considerable off-target effects, including the inhibition of caveolar internalization by a dynamin-independent mechanism. This is important, as for example the influence of dynamin small molecule inhibitors on chemotherapy resistance is currently investigated (see for example Tremblay et al., Nature Communications, 2020).

The investigation of the true effect of small molecules discovered as and used as specific inhibitors and their offside effects is extremely important and this reviewer applauds the effort. It is important that inhibitors are not used alone, but other means of targeting a mechanism are exploited as well in functional studies. The audience here thus is besides membrane biophysicists interested in the immediate effect of the small molecule Dyngo-4a also cell biologists and everyone using dynamic inhibitors to investigate cellular function.

Comments on revised version.

Overall, in this reviewer's opinion, after the additional experiments in the review process, all claims are now well-supported by the presented data from electron and live cell microscopy, QCM-D and AFM.

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 manuscript offers a careful and technically impressive dissection of how subpopulations within the subthalamic nucleus (STN) support reward-biased perceptual decision-making. The authors recorded STN neurons in monkeys performing an asymmetric-reward visual motion discrimination task, then combined single-unit analyses, regression modeling, and drift-diffusion model (DDM) fitting to identify functionally distinct neuronal clusters. Each subpopulation shows unique relationships to computational decision variables - evidence accumulation rate, decision bound, and non-decision time - as well as to post-decision evaluative signals including choice accuracy and reward expectation. The revised manuscript substantially strengthens the original submission by improving both the objectivity of neuron selection and the robustness of the clustering solution.

Strengths:

The asymmetric-reward paradigm cleanly separates perceptual and motivational contributions to STN activity, allowing the authors to characterize how neurons blend these distinct sources of information. The dataset is extensive and well-controlled, and the behavioral and neural analyses are tightly integrated. Relating cluster-specific activity to DDM parameters provides an interpretable computational link between population signals and behavior. The clustering solution is now validated across two algorithms, two monkeys, and subsets of trials - establishing that the three-cluster structure is robust. The new Figure 9 offers a conceptually useful, if necessarily speculative, synthesis connecting the identified subpopulations to distinct basal-ganglia pathways (hyperdirect versus indirect). The new Figure 8 documenting the anatomical intermingling of subpopulations is also important, as it directly informs the interpretation of prior and future STN stimulation studies.

Weaknesses:

The inferred relationships between neural clusters and DDM parameters remain correlational - the authors now appropriately flag this throughout, and the causal inference gap is acknowledged in the Discussion with concrete proposals for future targeted perturbation strategies. While a generative multi-cluster model would further strengthen mechanistic interpretation, the conceptual framework in Figure 9 provides a reasonable intermediate step given the scope of the study and the absence of simultaneous population recordings, which preclude direct inter-cluster covariation analyses. These remaining limitations are inherent to the experimental design rather than analytical oversights.

Comments on the previous version:

The authors have responded thoroughly and constructively to all of my concerns. The revised clustering pipeline - incorporating finer temporal resolution, objective neuron selection, outlier removal, a second clustering algorithm, cross-monkey validation (Rand indices of 0.94 and 1.0 for the two monkeys), and trial-subset stability analysis - substantially increases confidence in the three-cluster solution. The correlational nature of the DDM-activity relationships is now clearly stated, and the Discussion appropriately contextualizes the causal inference gap while suggesting feasible future directions. The new Figure 9 provides the conceptual synthesis I had hoped for, within the realistic scope of the present study. I am satisfied with the authors' responses and have no further requests.

Reviewer #1 (Public review):

Summary:

In the paper, the authors propose a new RNA velocity method, TSvelo, which predicts the transcription rate linearly based on the expression of RNA levels of transcription factors. This framework is an extension of its recent work TFvelo by including unspliced reads and designing a coherent neuralODE framework. Improved performance was demonstrated in six diverse datasets.

Strengths:

Overall, this method introduces innovative solutions to link cell differentiation and gene regulation, with a balance between model complexity (neuralODE) and interpretability (raw gene space).

Comments on revised version:

The authors have added comprehensive analyses in this revision, and all of my concerns have been very well addressed. Here, I just want to re-emphasize the original points 1 and 3.

(1) The analysis and clarification are very helpful - thanks! I found that Fig. R1 and R2 are very insightful, as DoRothEA-only returns much worse performance. Please consider adding these two figures to the supp figure and possibly highlighting your setting for edge pruning (down-weights); therefore, the model is more likely to be affected by false negatives than false positives in the TF-target prior.

(3) Please consider adding some discussion on the challenges in capturing cell cycle transitions.

Reviewer #1 (Public review):

The authors have conducted substantial additional analyses to address the reviewers' comments. However, several key points still require attention. I was unable to see the correspondence between the model predictions and the data in the added quantitative analysis. In the rebuttal letter, the delta peak speed time displays values in the range of [20, 30] ms, whereas the data were negative for the 45{degree sign} direction. Should the reader directly compare panel B of Figure 6 with Figure 1E? The correspondence between the model and the data should be made more apparent in Figure 6. Furthermore, the rebuttal states that a quantitative prediction was not expected, yet it subsequently argues that there was a quantitative match. Overall, this response remains unclear.

A follow-up question concerns the argument about strategic slowing. The authors argue that this explanation can be rejected because the timing of peak speed should be delayed, contrary to the data. However, there appears to be a sign difference between the model and the data for the 45{degree sign} direction, which means that it was delayed in this case. Did I understand correctly? In that regard, I believe that the hypothesis of strategic slowing cannot yet be firmly rejected and the discussion should more clearly indicate that this argument is based on some, but not all, directions. I agree with the authors on the importance of the mass underestimation hypothesis, and I am not particularly committed to the strategic slowing explanation, but I do not see a strong argument against it. If the conclusion relies on the sign of the delta peak speed, then the authors' claims are not valid across all directions, and greater caution in the interpretation and discussion is warranted. Regarding the peak acceleration time, I would be hesitant to draw firm conclusions based on differences smaller than 10 ms (Figures R3 and 6D).

The authors state in the rebuttal that the two hypotheses are competing. This is not accurate, as they are not mutually exclusive and could even vary as a function of movement direction. The abstract also claims that the data "refutes" strategic slowing, which I believe is too strong. The main issue is that, based on the authors' revised manuscript, the lack of quantitative agreement between the model and the data for the mass underestimation hypothesis is considered acceptable because a precise quantitative match is not expected, and the predictions overall agree for some (though not all) directions and phases (excluding post-in). That is reasonable, but by the same logic, the small differences between the model prediction and the strategic slowing hypothesis should not be taken as firm evidence against it, as the authors seem to suggest. In practice, I recommend a more transparent and cautious interpretation to avoid giving readers the false impression that the evidence is decisive. The mass underestimation hypothesis is clearly supported, but the remaining aspects are less clear, and several features of the data remain unexplained.

Comments on revised version.

The authors have reworked the sections of the text where the narrative was too strong or binary wrt alternative interpretations. The result is well balanced. No further recommendation.

Reviewer #1 (Public review):

Summary:

The objective of this study was to infer the population dynamics (rates of differentiation, division and loss) and lineage relationships of NK cell subsets during an acute immune response and under homeostatic conditions.

Strengths:

A rich dataset and a detailed analysis of a particular class of stochastic models.

Weaknesses: (relating to initial submission)

The stochastic models used are quite simple; each population is considered homogeneous with first-order rates of division, death, and differentiation. In Markov process models such as these there is no dependence of cellular behavior on its history of divisions. In recent years models of clonal expansion and diversification, in the settings of T and B cells, have progressed beyond this picture. So I was a little surprised that there was no mention of the literature exploring the role of replicative history in differentiation (e.g. Bresser Nat Imm 2022), nor of the notion of family 'division destinies' (either in division number, or the time spent proliferating, as described by the Cyton and Cyton2 models developed by Hodgkin and collaborators; e.g. Heinzel Nat Imm 2017). The emerging view is that variability in clone (family) size arises may arise predominantly from the signals delivered at activation, which dictate each precursor's subsequent degree of expansion, rather than from the fluctuations deriving from division and death modeled as Poisson processes.

As you pointed out, the Gerlach and Buchholz Science papers showed evidence for highly skewed distributions of family sizes, and correlations between family size and phenotypic composition. Is it possible that your observed correlations could arise if the propensity for immature CD27+ cells to differentiate into mature CD27- cells increases with division number? The relative frequency of the two populations would then also be impacted by differences in the division rates of each subset - one would need to explore this. But depending on the dependence of the differentiation rate on division number, there may be parameter regimes (and timepoints) at which the more differentiated cells can predominate within large clones even if they divide more slowly than their immature precursors. One might not then be able to rule out the two-state model. I would like to see a discussion or rebuttal of these issues.

Comments on revised version.

I am happy with the latest revisions that the authors have made.

Reviewer #1 (Public review):

Summary:

Kashiwagi et al. undertook a population analysis of dendritic spine nanostructure applied to the objective grouping of 8 mouse models of neuropsychiatric disorders. They report that spine morphology in cultured hippocampal neurons shows a higher similarity among schizophrenia mouse models (compared with autism spectrum disorder (ASD) mouse models) and identify an effect of Ecrg4 (encoding small secretory peptides) on spine dynamics and shape in these models.

Strengths:

The study developed a method for objectively comparing spine properties in primary hippocampal neuron cultures from 8 mouse models of psychiatric disorders at the population level using high-resolution structured illumination microscopy (SIM) imaging. This novel technique identified two distinct groups of mouse models according to the population-level spine properties: those with ASD-related gene mutations and those with schizophrenia-related gene mutations. Functional studies, including gene knockdown and overexpression experiments, identified an effect of Ecrg4 on the spine phenotype of the schizophrenia model mice.

Weaknesses:

The main weakness is that the study is wholly in vitro, using cultured hippocampal neurons. The authors present this as an advantage, however, arguing that spine morphology as measured in a reduced culture system can demonstrate direct effects of gene mutations on neuronal phenotypes in the absence of indirect influences from nonneuronal cells or specific environments.

Reviewer #1 (Public review):

Summary:

Roseby and colleagues report on a body region-specific sensory control of the fly larval righting response, a body contortion performed by fly larvae to correct their posture from an inverted (dorsal side down) position. This is an important topic because of the general need for animals to locomote in the correct orientation and the clever and broadly useful methodologies used in this paper to uncover the sensory triggers for the behavior, including a body region-specific optogenetic approach along different axial positions of the larva, region-specific manipulation of surface contacts with the substrate, and a 'water unlocking' technique to initiate righting behaviors, all strengths of the manuscript. The authors found that multidendritic neurons, particularly the daIV neurons, are necessary for righting behavior. The contribution of daIV neurons had been shown by the authors in a prior paper (Klann et al, 2021), but that study had used constitutive neuronal silencing. Here the authors used acute inactivation to confirm this finding. Additionally, the authors describe an important role for anterior sensory neurons. They move on to test the genetic basis for righting behavior and, consistent with the regional specificity they observe, implicate sensory neuron expression of Hox genes Antennapedia and Abdominal-b in self-righting.

Strengths:

Strengths of this paper include the important question addressed and the elegant and innovative combination of methods, which led to clear insights into the sensory biology of self-righting and links between body plan and nervous system function that will be useful for others in the field. The manuscript is very clearly written and couched in interesting biology.

Limitations:

There are several important questions for future study that, left unresolved, do not diminish the significance of this manuscript. These include the cellular and developmental basis for Hox gene action, the contributions of dorsal and ventral regions of the animal in righting, and the regional contributions of other sensory cell types in the righting response.

Comments on revised version.

The authors have addressed my major concerns.

Reviewer #2 (Public review):

Summary:

The authors sought to characterize the somatic mutation landscape and gene expression profiles of Kenyan breast cancer patients. By comparing Whole Exome Sequencing (WES) and RNA-seq data from 23 paired tumor-normal samples against The Cancer Genome Atlas (TCGA) cohorts, the study specifically aimed to highlight the role of the ZNF gene family.

Strengths:

The study addresses a critical gap in genomic research by focusing on an underrepresented African population, which is essential for achieving global health equity in oncology.

Weaknesses:

The cohort is relatively small for definitive landscape characterization. The study fails to explore the mechanistic link between identified somatic mutations and observed aberrant gene expression.

Impact and Utility:

The impact of this work is currently limited. While the data adds to the growing repository of African genomic samples, the lack of novelty and mechanistic insight reduces its utility for the broader scientific community. To be clinically valuable, the study would need to offer more robust, unbiased profiling that could eventually inform population-specific diagnostics or therapies.

Additional Context:

Breast cancer in African populations often presents with different clinical trajectories compared to Western cohorts. While any data from these regions is vital, "landscape" studies require high statistical power and unbiased analysis to differentiate true population-specific drivers from noise or small-sample variance. Without a clear regulatory mechanism linking mutations to phenotypes, the findings remain preliminary observations.

Reviewer #1 (Public review):

Summary:

This important study performs a theoretical analysis of the evolutionary dynamics of strains under a classical resource competition model to understand how clonal interference and diversification of resource preferences interact to structure microbial population genetic structure. They find that in large asexual populations evolving in relevant parameter regimes, where evolutionary and ecological time scales overlap, populations are characterized by a small number of ecotypes, which are groups of strains that share a given resource preference, whose dynamics in the long run are dominated by priority effects.

Strengths:

The manuscript constitutes a novel and sound contribution to theory in ecology and evolution, under relevant parameter regimes which have been previously overlooked due to the complexities they bring, i.e. when the weak mutation regime breaks down. Here, the authors make a considerable step forward by taking advantage of analytical advances in the population genetics theory of clonal interference in recent years (travel fitness wave moving at a constant average speed v), which they apply to resource competition models typically studied in ecology.

The main insights in the derivations shown in the supplementary text are clearly summarized in Figure 2 of the main manuscript, where the different phases of the somewhat counterintuitive dynamics of the strategic mutations in the model are quantified.

Weaknesses:

Despite its many merits, I believe the manuscript can profit from a few clarifications as I point out below:

(1) I think the authors should make explicit in the abstract of the paper that they study a stair to heaven fitness landscape and that the rate of beneficial mutations does not slow down.

(2) Evolution is elegantly incorporated in the resource consumption model by assuming two classes of mutations: strategic mutations and constitutively beneficial mutations. I believe that the biological meaning of these different types should be better explained. Specifically, on pages 3 and 4, the authors state that strategy mutations "alter resource uptake strategy and potentially its overall magnitude as well", whereas the other type is "only tangentially related to resource consumption (e.g. eliminating a pathway that is not necessary in the current environment)." I find this a bit strange since this is a model of resource competition, and I would assume that the latter type of mutations would be neutral. Maybe I am not reading this well, and the meaning of the mutations, as well as their assumed rates, could be clarified with some examples as the authors state that these mutations are routinely observed in microbial evolution experiments.

(3) The authors discuss the theoretical results obtained in the light of the famous Lenski experiment, where ecotype formation is observed in some populations. However, in the mentioned example, cross-feeding was the mechanism involved. Since in their model, unlike in other models, cross-feeding is not considered, I found this example to be misplaced. In addition, in the Lenski experiment, a single (and essential) resource is present in the environment, so the assumptions of the model do not appear to apply. On the other hand, in Herron and Doebeli's experiments, two resources (substitutable) were present, so a comparison with their experimental results would be more appropriate.

(4) The paper should also discuss deleterious mutations, which I did not see mentioned anywhere.

Reviewer #1 (Public review):

Summary:

In this manuscript, Balasubramaniam and colleagues continue this group's efforts to understand mitochondrial-derived compartments (MDCs) that bud off from yeast mitochondria in response to metabolic stress. In a previous genetic screen, they identified Ups lipid transfer proteins and the AAA-protease Yme1 as components that modulate MDC formation. In this study, the authors link these observations by showing that Yme1 modulates levels of Ups1, Ups2, as well as MICOS complex members in the mitochondrial proteome. Using genetic approaches, they then show that Yme1's role on MDCs is dependent on its catalytic activity (via an inactive mutant) and that YME1 shows genetic interactions with UPS1/2 and MIC10/MIC60. The overall model is that Yme1 activity responds to metabolic cues and acts via proteolysis of these two distinct mitochondrial machineries to regulate MDC biogenesis.

Strengths:

The strengths of the study are its integration of mitochondrial proteomics with strong genetic approaches, as well as synergy with the authors' previous studies on the role of lipids in MD genesis. The work is overall well carried-out and experiments are thoughtfully discussed.

Weaknesses:

The major weaknesses are a lack of mechanistic resolution surrounding the model, e.g., proposed or tested mechanisms by which Yme1 activity is regulated by metabolic cues, or how Ups1/2 activity and the MICOS contribute to MDC generation. The authors acknowledge these as open questions, but addressing them would still enhance the significance of the study.

Reviewer #1 (Public review):

Summary:

Combining in vitro refolding, SEC-based assembly assays, peptide-library screening, MALDI-TOF, LC-MS/MS, structural analysis and immunopeptidomics, this manuscript investigates the peptide-binding principles of the promiscuous chicken MHC-I molecule BF2*21:01.

Strengths:

Although the peptide motif of BF2*21:01 is highly complex, this manuscript identified several principles, including a preference for 10-mer peptides, co-variation between P2 and Pc-2, effects of P3 and Pc-3, and a strong cellular preference for Leu at Pc. The results are important for avian MHC biology and poultry vaccine epitope prediction.

Weaknesses:

The manuscript is sometimes difficult to follow because the authors present a large amount of peptide-library, structural and immunopeptidomics data. without always clearly explaining how these datasets support the proposed simplifying principles.

Major Issues - Points Requiring Clarification or Additional Support:

(1)（Line 282-301, 537-545）<br /> The immunopeptidomics conclusions are mainly based on one B21 cell line with one biological replicate and at least two technical replicates. Given the complexity of the BF2*21:01 peptide repertoire, this is a major limitation. The authors should either provide additional biological replicates or clearly state this limitation in the Abstract, Results and Discussion.

(2) (Lines 290-313）<br /> The B21 cell preparations contain both BF2 and the lowly expressed BF1 molecule. Some peptides, especially 8-mers or peptides with atypical motifs, may derive from BF1*21:01. The authors should clarify how BF2*21:01-bound peptides were distinguished from possible BF1-derived peptides, or interpret the immunopeptidomics motif more cautiously. The authors should also provide or cite evidence confirming the B21 haplotype identity of the cell line and chicken materials used for immunopeptidomics.

(3) (Lines 217-221, 243-253)<br /> The authors acknowledge that MALDI-TOF cannot reliably distinguish peptide combinations with identical or similar masses, nor determine residue positions in some cases. Therefore, MALDI-TOF results should not be overinterpreted as precise evidence for residue preference. The authors should clearly indicate which conclusions are supported by LC-MS/MS.

(4) (Lines 297-301, 316-330)<br /> The authors suggest that longer peptides may bulge in the middle or extend out of the groove at the C-terminal end. The rationale for the C-terminal extension is not clearly explained. Why is the C-terminal extension considered rather than the N-terminal extension? If the binding register is uncertain, long peptides should be analyzed separately from canonical-length peptides.

(5) (Lines 406-439)<br /> In vitro assembly assays show that several hydrophobic residues can be tolerated at Pc, whereas immunopeptidomics shows a strong Leu preference at this position. The authors should clarify whether this Leu preference reflects intrinsic BF2*21:01 binding specificity, TAP-mediated peptide transport, antigen processing, peptide loading, or a cell-line-specific effect. Additional experimental support, such as TAP transport analysis, would strengthen this conclusion.

(6) (Lines 172-178, 243-279, 442-457)<br /> The structural analysis explains some residue combinations, such as Arg at P2 with Glu at Pc-2 or Trp at Pc. However, the structural interpretation is not fully integrated with the large-scale peptide library and immunopeptidomics results. Representative high- and low-frequency combinations should be discussed structurally.

(7) The inference of co-variation between P2 and Pc-2, as well as the modulatory effects of P3 and Pc-3, should be better explained. At present, some conclusions appear to be based mainly on residue-frequency patterns, and the logical connection between these observations and the proposed binding principles is not always clear. Statistical analyses, such as mutual information, chi-square tests or permutation tests, and representative structural explanations would strengthen this conclusion.

Reviewer #1 (Public review):

Summary:

The "multiple-demand" (MD) system is a well-known finding of human brain imaging and is thought to play a central role in cognitive control. To directly compare the MD system in humans and monkeys, Mione et al. used functional magnetic resonance imaging to measure whole-brain activation in a multi-step saccadic maze task. In humans, the authors found a distributed pattern of brain activity close match to the canonical MD network and extends to adjacent regions of dorsal attention and other networks. While there was good correspondence between monkey and human data, differences were also notable in the lateral frontal cortex, the dorsal parietal cortex, and the sensorimotor cortex.

Strengths:

Though previous data hint at a corresponding network in the macaque, there has been no direct comparison to human data. This study provides a direct cross-species comparison with whole-brain data from fMRI, and the findings suggest an extended and strongly interconnected brain network recruited by increased cognitive challenge.

Weaknesses:

In previous human imaging, the MD system is defined by overlapping activation for many kinds of cognitive demands. In the present work, however, the authors used just a single task. Although there is some overlap between the putative monkey MD network and the canonical MD network identified in human imaging, there should be caution in linking current findings to the MD system based on limited task events.

Reviewer #1 (Public review):

Summary:

The manuscript entitled "Essential function reflected in the phylodynamics of a multigene family - the pir genes of malaria parasites" by Jackson and colleagues investigates the global phylogeny of pir genes across 14 Plasmodium species and one Hepatocystis species. The authors also focus on the functional characterization of the conserved ortholog pirC1 and claim that pirC1 is not the founder of the family and that it plays an essential role in blood-stage growth.

Strengths:

Overall, the manuscript is well written and interesting, as it combines comparative genomics and evolutionary analysis with functional experiments. The phylogenetic analysis is rigorous and represents a major strength of the manuscript.

Weaknesses:

The general conclusions regarding the potential function of this gene family are not fully supported by the data presented. The manuscript moves too quickly from growth phenotype and localization studies to a specific mechanistic model. The discussion argues that PIRC1 may be involved in nutrient acquisition, host sensing, or metabolic support, but the data provided do not directly support these functions, and the manuscript in its present form remains speculative. Although the manuscript includes some experimental results, it lacks direct mechanistic validation of the specific functions of the pir genes, including pirC1. In its current form, the study does not yet establish a definitive role for pirC1 in metabolic processes.

Reviewer #1 (Public review):

This is an interesting and valuable paper by Gil-Lievana, Arroyo et al. that presents an open-source method (the "Crunchometer") for quantifying biting and chewing behavior in mice using audio detection. The work addresses an important and unmet need in the field: quantitative measures of feeding behavior with solid foods, since most prior approaches have been limited to liquids. The authors make a clear and compelling case for why this problem is important, and I fully agree with their motivation.

The system is carefully validated against human-scored video data and is shown to be at least as accurate, and in some cases more accurate, than human observers. This is a major strength of the study. I also particularly appreciate the demonstration of the technology in the context of LHA circuitry, which nicely illustrates its utility and importance for mechanistic studies of feeding. I also appreciate the ability to readily time lock neural data to individual crunches. Overall, the manuscript is well executed and represents a useful contribution to the field.

Comments on revised version.

The revised manuscript has addressed my minor initial concerns. I appreciate that the sample size was increased for the recording experiments.

Reviewer #2 (Public review):

[Editors' note: this version has been assessed by the Reviewing Editor without further input from the original reviewers.]

Summary:

The premise of the manuscript by Matteucci et al. is interesting and elaborates a mechanism via which TNFa regulates monocyte activation and metabolism to promote murine survival during Plasmodium infection. The authors show that TNF signaling (via an unknown mechanism) induces nitrite synthesis, which (via yet an unknown mechanism), and stabilizes the transcription factor HIF1a. Furthermore, that HIF1a (via an unknown mechanism) increases GLUT1 expression and increases glycolysis in monocytes. The authors demonstrate that this metabolic rewiring towards increased glycolysis in a subset of monocytes is necessary for monocyte activation including cytokine secretion, and parasite control.

Strengths:

The authors provide elegant in vivo experiments to characterize metabolic consequences of Plasmodium infection, and isolate cell populations whose metabolic state is regulated downstream of TNFa. Furthermore, the authors tie together several interesting observations to propose an interesting model.

Weaknesses:

The authors show that TNFa induces GLUT1 in monocytes, but do not show a direct role for GLUT1 or glucose uptake in monocytes in host resistance to infection.

Reviewer #1 (Public review):

The authors have presented a revised version of their investigation into the Membrane Associated Periodic Skeleton (MPS) in iPSC derived human motor neurons. As mentioned in the earlier report, the main observations reported in this article-occurrence of patch and gap arrangement of MPS-is very interesting. The real puzzle is whether, and if so how, this structure coarsens over time to produce continuous MPS.

Following suggestions from reviewers, the authors attempted live cell imaging, but the results were not consistent enough and the authors point out difficulties in obtaining sufficient numbers and possible artefacts of over-expression. This investigation would have been much stronger with live cell imaging data on the dynamics of patch and gap structures.

Reviewer #1 (Public review):

The manuscript by Butler et al. explores a novel physiological role for connexin 32 (Cx32) hemichannels in Schwann cells of peripheral nerves. Building on the authors' prior work on CO₂-sensitive gating of connexin hemichannels, this study proposes that axonal activity-dependent mitochondrial CO₂ production promotes the opening of Cx32 hemichannels in adjacent Schwann cells, a process regulated by carbonic anhydrase (CA) activity and AQP1. This work reveals a new form of intercellular communication that may contribute to the regulation of conduction velocity.

The authors aimed to determine whether CO₂ acts as an activity-dependent signal in peripheral nerves through activation of Cx32 hemichannels in myelinating Schwann cells. The study is strengthened by the use of complementary techniques, including in silico approaches, pharmacological manipulation, dye uptake assays, calcium imaging, adenoviral delivery of dominant-negative Cx32 constructs targeted to Schwann cells, and extracellular recordings in isolated sciatic nerves. Together, these methods allow the authors to connect molecular mechanisms with tissue-level function.

The study has a few technical limitations, and some aspects of the interpretation require caution. Limitations in antibody specificity complicate interpretation of the precise distribution of the signaling pathway components studied here. Dye uptake into the outer myelin layer is consistent with hemichannel opening, but it does not by itself prove that Cx32 directly mediates the observed permeability changes. Similarly, Ca²⁺ signals associated with Cx32 activation could reflect direct Ca²⁺ permeability through Cx32 or secondary activation of other Ca²⁺ entry or release pathways. Finally, hemichannel opening is assessed primarily using FITC uptake, which may not fully capture the complexity of Cx32 gating or distinguish between different conductive states.

Overall, the authors provide substantial evidence that activity-dependent CO₂ production can influence Schwann cells through a pathway involving CA, AQP1, and Cx32. The results support the broad conclusions of the study, although some direct mechanistic links require further validation. The work is likely to have an important impact because it proposes a novel role for CO₂ as a local signaling molecule in peripheral nerves and may provide new insight into how Schwann cells detect axonal activity and regulate peripheral nerve physiology.

Comments on revised version.

The authors have addressed all of my concerns. The manuscript is now much improved and reads very well. Congrats to all the research team.

Reviewer #1 (Public review):

In the manuscript entitled "Flexible and high-throughput simultaneous profiling of gene expression and chromatin accessibility in single cells," Soltys and colleagues present easySHARE-seq, a method described as an improvement upon SHARE-seq for the simultaneous measurement of RNA transcripts and chromatin accessibility.

The authors demonstrate the utility of easySHARE-seq by profiling approximately 20,000 nuclei from the murine liver, successfully annotating cell types and linking cis-regulatory elements to target genes. The authors claim that easySHARE-seq supports longer read lengths potentially enabling better variant discovery or allele-specific signal assessment, though they do not provide direct evidence to support these specific claims.

A key strength of the protocol is enhanced sequencing efficiency, achieved by shortening the Index 1 read from 99 to 17 nucleotides. This reduction does not come at a significant cost to barcode diversity, retaining approximately 3.5 million combinations. Additionally, the approach allows for the sequencing of a sub-library to assess quality prior to final barcoding and sequencing which seems quite clever.

While the increase in RNA transcript recovery is substantial, it appears to come at a cost: there is a notable decrease in ATAC fragments per cell compared to the original SHARE-seq (and other platforms). Likely as a result, the dimensionality reduction (UMAP) shows good resolution for RNA profiles but relatively poor resolution for accessibility profiles. Furthermore, the presented data suggests potential ambient RNA contamination; specifically, the detection of Albumin in HSCs and B cells is likely an artifact of the protocol rather than a biological signal.

Overall, the study is well-presented and represents a promising advance. However, there are significant shortcomings that should be addressed, particularly regarding "leaky" transcript recovery and reduced ATAC performance.

Reviewer #1 (Public review):

Summary:

The manuscript by Yang et al. investigates the relationship between multi-unit activity in the locus coeruleus, putatively noradrenergic locus coeruleus, hippocampus (HP) sharp-wave ripples (SWR) and spindles using multi-site electrophysiology in freely behaving male rats. The study focuses on SWR during quiet wake and non-REM sleep, and their relation to cortical states (identified using EEG recordings in frontal areas) and LC units.

The manuscript highlights differential modulation of LC units as a function of HP-cortical communication during wake and sleep. They establish that ripples and LC units are inversely correlated to levels of arousal: wake, i.e. higher arousal correlates with higher LC unit activity and lower ripple rates. The authors show that LC neuron activity is strongly inhibited just before SWR detected during wake. During non-REM sleep, they distinguish "isolated" ripples from SWR coupled to spindles and show that inhibition of LC neuron activity is absent before spindle-coupled ripples but not before isolated ripples, suggesting a mechanism where noradrenaline (NA) tone is modulated by HP-cortical coupling. This result has interesting implications for the roles of noradrenaline in the modulation of sleep-dependent memory consolidation, as ripple-spindle coupling is a mechanism favoring consolidation. The authors further show that NA neuronal activity is downregulated before spindles.

Strengths:

In continuity with previous work from the laboratory, this work expands our understanding of the activity of neuromodulatory systems in relation to vigilance states and brain oscillations, an area of research that is timely and impactful. The manuscript presents strong results suggesting that NA tone varies differentially depending on coupling of HP SWR with cortical spindles. The authors place their findings back in the context of identified roles of HP ripples and coupling to cortical oscillations for memory formation in a very interesting discussion. The distinction of LC neuron activity between awake, ripple-spindle coupled events and isolated ripples is an exciting result and its relation to arousal and memory opens fascinating lines of research.

Weaknesses:

I regretted that the paper fell short of trying to push this line of idea a bit further, for example by contrasting in the same rats the LC unit-HP ripple coupling during exploration of a highly familiar context (as seemingly was the case in their study) versus a novel context, which would increase arousal and trigger memory-related mechanisms. Any kind of manipulation of arousal levels and investigation of the impact on awake vs nonREM sleep LC-HP ripple coordination would considerably strengthen the scope of the study.

Comments on revised version.

The authors have added methodological details to the results section after the first round of reviews, improving the manuscript readability. Some points might still be improved, for example, the authors use a delta/gamma ratio to track cortical states for example, but there is no methods section corresponding to this metric. Authors write that higher SI corresponds to a lower arousal state that is associated with "more synchronized cortical population activity, higher ripple rate and reduced LC neurons firing" but there are no references or analysis to support this statement, only examples showing changes in SI over a few minutes.

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.]

This paper aims to improve the accuracy of predictions of the impact of ITN strategies by developing a method to estimate duration of ITN access and use over time on a subnational scale from cross-sectional survey data and the numbers ITNs received annually. The subnational estimates are then input into a mathematical model to predict clinical cases under different ITN distribution strategies.

Strengths:

The approach is novel and addresses a useful and timely topic. It makes use of available routine data, and has considered all of the relevant components of ITN distributions.

The authors have made revisions, particularly to the methods, appendices and title - leaving the paper easier to follow, and with a clear, consistent aim. The assumptions are clearly stated.

Reviewer #1 (Public review):

This work addresses a question of practical importance that had never been systematically analysed in the cryo-ET field: when collecting tilt-series data, what is the optimal angular step size between successive tilt images? Due to the upper limit in electron exposure (100 - 150 e⁻/Ų), this question is important, since finer angular sampling improves attainable reconstruction resolution (Crowther criterion) but reduces the signal-to-noise ratio of each individual image, potentially compromising both image quality and the ability to computationally align successive frames. To address this, the authors designed a thorough benchmarking study comparing five tilt increments (1{degree sign}, 2{degree sign}, 3{degree sign}, 5{degree sign}, and 10{degree sign}) while keeping the total dose and tilt range constant. They evaluated the consequences at every stage of the cryo-ET workflow - from raw image quality and tilt-series alignment, through template matching for ribosome detection, to high-resolution subtomogram averaging - with the goal of providing the community with an evidence-based recommendation for data acquisition.

The manuscript is well written, and the experimental design is carefully thought out. The work provides valuable practical insights into cryo-ET data acquisition by demonstrating that balancing two competing demands - sufficient dose per individual tilt image and fine angular sampling - is essential to achieve high-quality tomographic reconstructions. The identification of a practical optimum at 3{degree sign} tilt increment is the key contribution of the work. It will be interesting to see in the future whether this optimum shifts for smaller molecular targets, and how emerging tilt interpolation strategies such as cryoTIGER may interact with the choice of experimental angular increment.

The conclusions of this paper are mostly well supported by data, but some aspects of data analysis need to be clarified and/or extended, including:

(1) Line 109: The authors state that the tilt range was kept at {plus minus}60{degree sign} relative to the lamella plane. Assuming a typical lamella pre-tilt of ~10{degree sign}, the absolute stage tilt would approach its mechanical limit. Two clarifications would be appreciated: (a) What was the average pre-tilt across all lamellae? (b) How many dark tilt images, if any, were excluded during tomogram reconstruction?

(2) Line 148: "When analysing tomographic volumes, we found that tomograms from data with a smaller increment displayed higher SNR values (see Fig. 2B)." It would be helpful to specify which comparisons are statistically meaningful (e.g. Mann-Whitney U test?). While the difference between 1{degree sign} and 2{degree sign} appears pronounced, the differences between 2{degree sign}, 3{degree sign}, and 5{degree sign} seem minimal. From my point of view, reporting the mean SNR values +/- standard deviations for each condition would already indicate some significance. Furthermore, since SNR is expected to depend on lamella thickness, it should be clarified whether the average lamella thickness is comparable across the five datasets.

(3) Line 167: "Indeed, the variation in maximum resolution correlates with lamella thickness across all datasets (see Fig. 2F)." The reported R² values of 0.30 (1{degree sign}), 0.38 (2{degree sign}), 0.66 (3{degree sign}), 0.61 (5{degree sign}), and 0.60 (10{degree sign}) reveal a notably weak linear relationship for the finer tilt increments. It is also difficult to assess whether the lamella thickness distributions are comparable across conditions from the current figures - visually, the 1{degree sign} dataset appears to be based on thinner lamellae, while the 10{degree sign} dataset appears to include thicker samples. A histogram of lamella thickness distributions for each condition, provided as supplementary material, would greatly aid interpretation. Given this thickness dependency, reporting mean +/- standard deviation of lamella thickness per condition is highly appreciated.

(4) Figure 4: It should be specified which tomogram subsets were used for the Rosenthal-Henderson analysis, whether lamella thickness was taken into account in the subset selection, and whether ribosomes too close to the lamella edges were excluded. Finally, linear fits should be displayed across the full x-axis range for all tilt increments to facilitate direct visual comparison.

(5) General: Were ribosomes located at the lamella edges excluded from the analysis? As demonstrated in the authors' own prior work (Tuijtel et al., Science Advances, 2024), Ga-FIB milling induces structural damage at the lamella surfaces. To exclude the influence on the STA results, particles near the lamella edges should be removed prior to analysis, and the criteria for this exclusion should be stated explicitly.

The aim of the authors was to provide the cryo-ET community with an evidence-based recommendation for the choice of tilt increment, and they largely succeeded in this goal. The identification of 3{degree sign} as a practical optimum - balancing sufficient dose per tilt image for effective per-particle refinement with fine enough angular sampling for accurate tilt-series alignment - is well supported by the data and consistent across the multiple quality metrics employed. The conclusion that coarser increments (5{degree sign} and 10{degree sign}) compromise tomogram quality, template matching accuracy, and STA resolution is robust and clearly demonstrated. However, the conclusion rests entirely on a single biological system using ribosomes as the sole molecular target, which are exceptionally favourable due to their abundance, size, and electron contrast. Whether the identified optimum holds for smaller, lower-abundance, or lower-contrast targets remains an open question.

In future, it would be particularly interesting to test whether emerging tilt interpolation strategies, such as cryoTIGER, which is particularly intriguing, can effectively compensate for coarser experimental angular sampling in post-processing. Here, the optimal experimental increment may shift, and the interaction between these two approaches represents a promising direction for future work. More broadly, as cryo-ET datasets grow larger and public repositories expand, the practical tradeoffs between acquisition time, data storage, and structural quality identified here will become increasingly relevant to the field.

Reviewer #1 (Public review):

This study addresses an important clinical challenge by proposing muscle network analysis as a tool to evaluate rehabilitation outcomes. The research direction is relevant and the findings suggest further research.

The revised manuscript included additional methodological details and a supplementary comparison with conventional NMF.

Comments on latest version:

No additional comments.

Reviewer #1 (Public review):

Summary

In the presented paper, Lu and colleagues focus on how items held in working memory bias someone's attention. In a series of three experiments, they utilized a similar paradigm in which subjects were asked to maintain two colored squares in memory for a short and variable time. After this delay, they either tested one of the memory items or asked subjects to perform a search task.

In the search task, items could share colors with the memory items, and the authors were interested in how these would capture attention, using reaction time as a proxy. The behavioral data suggest that attention oscillates between the two items. At different maintenance intervals, the authors observed that items in memory captured different amounts of attention (attentional capture effect).

This attentional bias fluctuates over time at approximately the theta frequency range of the EEG spectrum. This part of the study is a replication of Peters and colleagues (2020).

Next, the authors used EEG recordings to better understand the neural mechanisms underlying this process. They present results suggesting that this attentional capture effect is positively correlated with the mean amplitude of alpha power. Furthermore, they show that the weighted phase lag index (wPLI) between the alpha and theta bands across different electrodes also fluctuates at the theta frequency.

Strengths

The authors focus on an interesting and timely topic: how items in working memory can bias our attention. This line of research could improve our understanding of the neural mechanisms underlying working memory, specifically how we maintain multiple items and how these interact with attentional processes. This approach is intriguing because it can shed light on neuronal mechanisms not only through behavioral measures but also by incorporating brain recordings, which is definitely a strength.

Subjects performed several blocks of experiments, ranging from 4 to 30, over a few days depending on the experiment. This makes the results - especially those from behavioral experiments 2 and 3, which included the most repetitions - particularly robust.

Comments on revision:

The authors have adequately addressed my concerns. No further comments.

Reviewer #1 (Public review):

Summary:

Laaker et al. investigates the immunological role of the cribriform plate during neuroinflammation using the EAE model. The authors combine immunohistochemistry, flow cytometry and single-cell RNA sequencing to characterize CD11b+CD11c+ myeloid cells that accumulate at podoplanin (PDPN)-rich meningeal-lymphatic niches surrounding olfactory nerve bundles. They identified distinct populations of migratory dendritic cells (DCs) and macrophages retained at the cribriform plate that exhibit transcriptional signatures consistent with immune tolerance, reduced interferon signaling, and programmed cell death, including Pdcd1 (PD-1) expression. In parallel, CCR2+ monocytes and alternatively activated (M2-like) Arg1+/CHI3L3+ macrophages integrate into this niche, suggesting the establishment of a locally immunosuppressive myeloid network.

Strengths:

(1) Overall, the study postulates a novel model in which the cribriform plate functions as a specialized perineural immune interface that reshapes myeloid phenotypes during neuroinflammation.

(2) Suggests broader relevance for shaping peripheral immunity and therapeutic targeting. If DCs are being "tuned" at this exit site, it could influence what reaches cervical lymph nodes and how peripheral responses are set during CNS autoimmunity; the authors explicitly position this as relevant to CNS autoimmunity and possibly other CNS diseases (while acknowledging the need for human validation).

(3) Technical sound and highly original work. Convergent multi-method support: the central narrative is backed by immunohistochemistry + flow cytometry + scRNA-seq, rather than a single assay. The headline conclusion (tolerogenic/suppressive skew at the cribriform plate during EAE) is explicitly built from these combined modalities.

Comments on revised version.

All my points were adequately addressed by the authors.

Reviewer #1 (Public review):

Summary:

Kaku and Flenniken investigate the mechanistic pathways through which specific viral infections alter the flight capabilities of honey bees. Building on their previous discovery that DWV impairs flight while SBV unexpectedly enhances it, the authors hypothesized that these behavioral shifts are driven by interactions with the insect's octopamine (OA) signaling pathway, which is responsible for the "fight-or-flight" neurohormonal stress response and energy mobilization. To test this, the authors experimentally infected adult honey bees with DWV or SBV and pharmacologically manipulated the OA pathway using either octopamine supplementation or epinastine (EP), an OA-receptor antagonist. They then evaluated the bees' flight performance (distance, duration, and speed) on custom flight mills and profiled their gene expression using qPCR and RNA sequencing.

Strengths:

A major strength of this study is the high prevalence of preexisting background DWV and SBV infections in the honey bee cohorts, which meant there were no completely "virus-free" control groups. However, the authors successfully mitigated this limitation by rigorously quantifying viral RNA copies for every individual bee via qPCR and utilizing these viral abundances as continuous variables in powerful linear mixed-effect models.

Weaknesses:

The primary weakness lies in the methodology used for targeted pharmacological manipulations, as well as the lack of OA quantification across different treatments. Thus, their claims are not sufficiently supported by the current data.

(1) The authors utilize Epinastine to block octopamine signaling, describing it as a highly specific OA receptor antagonist. However, pharmacological inhibitors often lack absolute specificity. Epinastine might bind to other octopamine receptor subtypes present in honey bee neural and flight muscle tissues, or it could potentially cross-react with tyramine and dopamine receptors. Without further genetic validation (e.g., RNA interference targeting specific receptors), it is difficult to definitively conclude that the altered flight performance is solely due to the blockade of the specific Oβ−2R pathway.

(2) As a natural neurotransmitter, insects have evolved highly efficient "cleanup" mechanisms. OA is rapidly cleared from the synaptic cleft via reuptake transporters and quickly inactivated by enzymes such as N-acetyltransferase (NAT) or Monoamine Oxidase (MAO). Consequently, an injection of OA produces only a transient "pulse" of activity. It is often a poor "tool" for inducing prolonged physiological effects compared to synthetic formamidines like Amitraz.

(3) The study relies heavily on transcriptomics and quantitative PCR to measure the mRNA expression of key synthesizing enzymes, namely tyrosine decarboxylase (tdc) and tyramine β-hydroxylase (tβh), to infer the activation or suppression of the octopamine pathway. However, changes in enzyme synthesis at the RNA level are often insufficient to accurately reflect the true physiological levels of biogenic amines. To robustly prove the authors' hypothesis of a "feedback loop that regulates intracellular OA concentrations", direct quantification of actual octopamine and tyramine titers in the bees (e.g., using high-performance liquid chromatography or mass spectrometry) is necessary.

Reviewer #1 (Public review):

Summary:

The authors aim to characterize Huntingtin (HTT) aggregates in various cells and tissues and propose that mutant polyQ HTT (mHTT) assembles at the Golgi apparatus, thereby impairing Golgi organization and function. They further suggest that such Golgi defects might contribute to disease pathology, including neurodegeneration.

Strengths:

The study spans a wide range of disciplines, including genetics, cell biology, neuroscience, and systems biology, and employs diverse methodologies such as iPSC, 3D SIM microscopy, omics approaches, organoid culture, electrophysiology, and antisense depletion.

Weaknesses:

While the breadth of techniques is impressive, the central premise of the work-the structural and functional relationship between polyQ assemblies and the Golgi apparatus-is not supported by sufficiently rigorous cell biological evidence.

A major concern is that much of the cell biology data remains descriptive and lacks mechanistic depth. The findings are fragmented and not integrated into a coherent molecular or cellular model. Instead of building a logical progression of experiments, the study presents a collection of observations that appear disconnected and, at times, driven more by technical capability than by hypothesis-driven design.

Critically, the key claim that polyQ HTT functionally disrupts the Golgi (Golgipathy) is not convincingly demonstrated. Many observations could be more simply explained by the polyQ HTT localization to the Golgi and known Golgi sensitivities to perturbations (e.g., starvation or Brefeldin A treatment), rather than by a specific mechanistic role of polyQ HTT.

The manuscript also suffers from issues in organization and clarity, including imprecise descriptions and figures that are difficult to interpret.

Major Concerns:

(1) Golgi localization

The localization of polyQ HTT relies entirely on the antibody 3B5H10, which is foundational to the study. However, previous reports using the same antibody have described predominantly cytosolic localization. This discrepancy must be addressed rigorously by independent validation using alternative antibodies or tagged, exogenously expressed polyQ HTT constructs that should be shown to colocalize with 3B5H10 signals.

Furthermore, the Golgi is identified solely using GM130, a cis-Golgi and ER exit site marker. This raises ambiguity: does polyQ HTT associate with the entire Golgi or only recruit GM130? Could the observed signal correspond to a sub-Golgi compartment?

If polyQ HTT is indeed Golgi-associated, several key observations become expected rather than novel. For example, in Figure 4I-M, sensitivity to Brefeldin A is unsurprising, as Golgi structure collapses upon such treatment; in Figure 4N-O, co-fragmentation with the Golgi is expected under Golgi-disrupting conditions.

(2) 3D rendering

The extensive use of 3D rendering appears unnecessary and, in some cases, misleading. The rendered images do not provide additional insight beyond conventional 2D fluorescence images. Serial 2D fluorescence sections should be more objective in representing the 3D organization. In Figure 2A and Figure 5A, red line features in 3D beige polyQ HTT structures resemble unrelated biological structures, such as vasculature, which is inappropriate.

There is also an inconsistency in rendering. For example, fine mesh-like structures are shown in some figures (e.g., Figure 2A, Figure 4A), whereas others appear as amorphous aggregates (e.g., Figure 5A, Figure S2B), without explanation.

(3) Quantification of area and volume

The manuscript extensively quantifies the area and volume of polyQ assemblies (e.g., Figure 2B, C and Figure 3B, C, E, G, H). These measurements are not reliable. First, the structures appear filamentous and likely below the diffraction limit. Second, fluorescence signals are broadened by the point spread function (PSF), artificially inflating measured dimensions. Last, even with 3D SIM (~100 nm resolution), fine structural details remain unresolved. Thus, these quantitative measurements lack physical meaning and might not be used to support conclusions.

(4) Interpretation of structural features (Figure 2A)

Descriptions such as "parallel spindles" and "ring-like assemblies" are not clearly supported by the data. The terminology is ambiguous, and the claimed structures are not discernible. The use of the term "interaction" with the nuclear membrane is also inappropriate. At best, the data suggest colocalization, which itself is not convincingly demonstrated.

(5) Mitotic fragmentation (Figure 2E)

The conclusion that polyQ assemblies fragment during mitosis lacks proper controls. It is unclear whether these cells exhibited intact "fabric-like" assemblies during interphase, or the observed structures were already fragmented prior to mitosis.

(6) Fixation-induced fragmentation (Figure 2F)

The claim that fixation-induced fragmentation reflects a unique dynamic property of polyQ assemblies is likely an overinterpretation. This phenomenon may simply represent a fixation artifact. Therefore, it cannot be used as evidence for in-cellulo structural dynamics.

(7) Nuclear localization claims (Figure 5A)

The assertion that polyQ assemblies "almost completely occupy the nucleus" is not supported. The images are more consistent with perinuclear localization, typical of the Golgi region. There is no clear evidence for nucleoplasmic distribution.

(8) Drug treatment and data interpretation (Figure 3D-E)

The x-axis in Figure 3E is non-linear, which is inappropriate unless explicitly justified. Furthermore, the rationale for using Onjisaponin F is unclear. What is its known mechanism? Does it affect Golgi organization? Without this context, observed effects may reflect Golgi perturbation rather than specific effects on polyQ assemblies.

Reviewer #1 (Public review):

Summary:

This paper describes an application of the high-resolution cryo-EM 2D template matching technique to sub-50kDa complexes. The paper describes how density for ligands can be reconstructed without having to process cryo-EM data through the conventional single particle analysis pipelines.

Strengths:

Improved insights in which particles contribute to the density of ligands that is absent from the templates are valuable.

Weaknesses:

Although the convenient visualisation of small molecules bound to protein targets of a known structure would be relevant for the pharmaceutical industry, the evidence described for the claim that this technique "significantly" improves alignment of reconstruction of small complexes is incomplete. In a revised paper, the authors are encouraged to better evaluate the effects of model bias on the reconstructed densities.

In the revised version, the refinement of atomic occupancies in the 2DTM-generated maps has been insightful: densities only come back at values ranging from 0.55-0.80, whereas residues included in the template remain at 1, suggesting that the 2DTM-reconstruction does suffer from model bias. Their newly added Omega calculations, which are helpful, also suggest that model bias is present in the 2DTM-based reconstructions. These observations therefore contradict the first subsection heading of the Results, which claims "unbiased reconstruction of omitted residues".

Both the Omega analysis and the refined atomic occupancies provide insights into the "real-space aspect" of the model bias. The question to what extent the model bias affects the map in Fourier space remains unanswered. The authors base some of their claim in the paper on FSC curves in Figures 1b and 3b, but these will suffer from the same model bias. To assess this, I had requested the authors to reconstruct an OMIT map and to assess its resolution using FSCs. The authors have indeed performed a careful reconstruction of an OMIT map, which is currently shown in Figure 5. I liked how they implemented this, as described in detail in the Methods section. However, the measurement of how much model bias is present in this OMIT map by FSC calculations is still pending. This could be done in two ways, and I would encourage the authors to present the results of both in (hopefully a last) revised version of their manuscript. My original suggestion was to calculate a map-to-model FSC for the OMIT map and the full reference. This should be compared with a similar map-to-model FSC on the map where only the ligand was omitted. Alternatively, they can use the cisTEM FSC_uncorr procedure on the OMIT half-reconstructions and compare the resulting curve with the one presented in Figure 1b.

The reason that I am keen to see these FSCs is because high-resolution model bias is a fundamental danger of the 2DTM approach. It will therefore also be in the interest of the authors to quantify the extent to which it happens. For now, I have kept the above public review and short assessment the same as they were, but I will consider raising the assessment after the suggested experiments (which I hope will be relatively easy to do!) are incorporated.

Reviewer #1 (Public review):

Summary:

The manuscript by Singh et al. presents an application of MOA-seq to better define transcriptional control underlying the hypoxia response in human endothelial cells. This group's previously described MOA-seq technique allows for precise, identity-agnostic mapping of occupied sites of DNA-binding proteins across the epigenome and over time. Here, they applied MOA-seq to HUVECs under normal oxygen conditions or variable lengths of hypoxia treatment, comparing changes in occupancy over time and associating these changes with corresponding transcriptome alterations. This approach revealed thousands of dynamically occupied sites comprising 10 major kinetic clusters that appear to define distinct subsets and phases of the hypoxia response. Analysis of DNA motifs in these dynamically occupied regions captured the known major roles of HIF1A in the hypoxia response and also implicated new HIF1A-associated regulators. Importantly, they also identified many potential HIF1A-independent candidate TFs that act at HREs, which has been an outstanding question in the field. Additionally, this study identified ~7K additional sites not previously defined as regulatory elements by ENCODE.

Strengths:

Overall, this study is well executed and described, providing new biological insights as well as a rich data resource for the field. As MOA-seq was previously developed for use in plants, this work demonstrates the application of this method in mammalian cells and highlights its utility in identifying new potential regulatory sites not captured by DNase-seq or ATAC-seq. The conclusions made by the authors are well supported by the results, with the caveat that extensive use of DNA motif identification and ontology analyses invariably leads to some uncertainty regarding factor identity and gene network properties.

Weaknesses:

There are several areas where the clarity of presentation could be improved:

(1) Given the importance of the methodology, the methods section needs more detail on how the extent of MNase digestion is chosen to achieve optimal results with MOA-seq. This is described to some extent in the description of control library preparation, but not for the experimental samples.

(2) The abstract describes this approach as "native cistrome profiling" but this is misleading since formaldehyde fixation is used.

(3) Species- and field-specific jargon and abbreviations need to be clarified on first usage. For example, on page 9: "Downsampling analysis was carried out for two sets of published reference peaks; the CTCF cCRE peak midpoints and for the ERG motif under the ERG ReMap ChIP-seq peaks." The different categories of cCREs were not clearly defined, nor will it be clear what the term ReMap refers to for those outside the field. The sentence after this refers to IDR, which also should be defined.

(4) Figure 4C: Are these motifs examined under MOA sites specifically or anywhere in the genes in question?

(5) Figure 5B shows that up-DEGs with diff-MOA footprints tend to show more losses of footprints. Do the authors interpret this as a loss of repressor binding?

Reviewer #1 (Public review):

Summary:

White et al. explore the role of synaptotagmin isoforms in mediating neurotransmitter release from EPN terminals in the LHb. The authors show a relatively high expression of Syt2 and Syt3 in the EPN relative to other Syt isoforms. The authors then perform a series of experiments to show that Syt2 preferentially regulates glutamatergic transmission while Syt3 regulates GABAergic transmission.

Strengths:

Interesting, timely topic.

Weaknesses:

While interesting, the study is rather preliminary. There are a number of issues the authors need to address.

Reviewer #1 (Public review):

Public Review

This paper presents an fNIRS neuroimaging study with a relatively large sample of preschool children (aged 3-5) that measures both positive and negative empathy within a single task. Children watch emotional events and are asked questions about both their own emotions and the emotions of others, allowing the authors to distinguish between affective and cognitive empathy. The authors propose "foundational" models of affective and cognitive empathy and argue that their findings support the idea that cognitive empathy emerges before affective empathy in early childhood.

Strengths:

The paper addresses a valuable question by measuring both positive and negative empathy within a single cognitive task. The use of fNIRS with a relatively large preschool sample is commendable, and the pre-registered design strengthens the contribution. The task itself is innovative, well-suited to this age group, and achieves high compliance, which is essential and notably difficult with young children. Overall, the methods are appropriate, and the empirical work is valuable.

Weaknesses:

The main concerns relate to the framing of the paper rather than the empirical work itself.

The introduction contains several claims that are overstated or inaccurate. The statement that "we know very little about the development of this fundamental social skill during the first years of life" does not reflect the state of the field; empathy in early development has been quite extensively studied (e.g., Davidov et al., Malti et al., Uzefovsky et al., Decety et al., Feldman et al., among others). The view that emotional contagion directly develops into affective empathy is based on early theoretical accounts that have since been challenged by empirical evidence (see Davidov et al., 2025). The claim that cognitive empathy does not require theory of mind is also overstated - it is hard to see how theory of mind, the understanding that others have thoughts, beliefs, and emotions that may differ from our own, would not be required for cognitive empathy. Furthermore, the introduction neglects recent and directly relevant work (e.g., Zach et al., 2025; Uzefovsky et al., 2020; Davidov et al., 2021).

Most critically, the claim that "no neuroimaging studies have yet investigated brain regions supporting empathy in preschoolers" is inaccurate. Multiple studies have examined brain regions supporting empathy in children within this age range, including work using fNIRS and studies of positive empathy (e.g., Decety et al., 2018; Light et al., 2009; Levy et al., 2019; Bray et al., 2022; Brink et al., 2011). This is also not the first study to measure brain activation in response to positive and negative emotional events in children (e.g., Cheng et al., 2014; Light et al., 2009). These novelty claims need to be corrected.

The use of "explicit" to describe cognitive empathy and "implicit" or "spontaneous" to describe affective empathy is problematic. Affective empathy can be expressed quite explicitly, through facial expressions, verbal statements, and gestures, and framing it as spontaneous overlooks the motivational dimensions of empathy (e.g., Zaki and colleagues). The authors' use of "foundational affective empathy model" and "foundational cognitive empathy model" as though these are established concepts is not well supported by the current evidence base.

The conclusions in the discussion go beyond what the data can support. The question of whether cognitive or affective empathy emerges first cannot be adequately addressed with a cross-sectional sample aged 3-5, an age at which affective empathy is likely already well established and cognitive empathy is expected to be developing around the lower end of this range. The cross-sectional design further limits what can be inferred about developmental trajectories during a period of substantial individual variability. Together, these issues make the developmental-precedence conclusions difficult to sustain. The claim that the results demonstrate "the first time that this brain specialisation for stimuli of different emotional valence may be rooted in childhood" is also inaccurate, as there is prior evidence for brain specialisation of emotional valence in early childhood (e.g., Grossmann et al., 2007).

Appraisal:

The empirical contribution, the task design, the fNIRS data, and the analyses are sound and have value for the field. However, in its current form, the paper does not achieve what it sets out to do. The novelty claims are undermined by the omission of a substantial body of relevant prior work, and the developmental conclusions are not adequately supported by the cross-sectional design and age range studied. The abstract similarly overstates the support this study provides for the early emergence of cognitive over affective empathy.

Impact:

With appropriate revision, this work could make a meaningful contribution. The task is well-designed for studying empathy in young children and could be useful to other researchers in the field. The fNIRS data from a large preschool sample are a valuable resource. However, the contribution needs to be framed accurately, both in terms of what is genuinely novel relative to the existing literature and in terms of what conclusions the data can and cannot support.

Reviewer #1 (Public review):

The study by He and colleagues aims to investigate the molecular mechanisms driving key cell potency transitions, particularly the naïve-to-primed pluripotency transition. The authors explore the relationship between cell polarity and stemness using stem cell models combined with a comprehensive panel of experiments, including pharmacological inhibition and co-culture/conditioned medium rescue approaches. Overall, the study provides interesting observations and contributes to the understanding of the molecular mechanisms dynamically regulating stem cell differentiation.

However, several conceptual and interpretational aspects could be strengthened:

First, the Introduction would benefit from being more focused on what is currently known regarding cell polarity during early embryogenesis and pluripotent stem cell transitions, rather than emphasizing later neurogenesis events. Such reorientation would better match the main topic of the manuscript and improve the conceptual coherence of the study.

Similarly, Figure 6, where the authors attempt to provide clinical relevance through neural organoid formation experiments, feels somewhat disconnected from the central theme of the naïve-to-primed transition. Although this section is interesting on its own, there is already extensive literature describing polarization and morphogenetic events occurring much earlier during pluripotent state transitions. Therefore, the developmental relevance of the neural differentiation phenotypes could be better contextualized in relation to earlier morphogenetic events associated with pluripotency progression.

The manuscript contains a substantial amount of experimental work; however, several results would benefit from deeper discussion. For example, in Figure 1, what is the rationale behind ZO1 downregulation being observed specifically in primed PAR knockout cells but not under naïve culture conditions? In addition, in Figure 3, the authors perform co-culture and conditioned medium experiments between wild-type and knockout cells. While the authors focus on the secreted protein fraction that rescues the phenotype, they also mention that other fractions display rescuing activity. Could the authors briefly discuss what additional components may contribute to this rescue effect? For example, could other molecules within these fractions also converge on AKT signaling regulation?

Importantly, transitions in cell potency are frequently associated with coordinated morphogenetic changes. For example, during mouse embryogenesis, naïve pluripotent inner cell mass cells progressively polarize into a rosette-like structure with apical domain specification before lumen formation and epithelialization during progression toward the primed epiblast state. This developmental context could help strengthen the biological interpretation of the study.

There are also several claims throughout the manuscript that appear to be overinterpreted or insufficiently quantified. For example, in Figure 1, the authors state that CDH1 expression is uniform; however, this is difficult to appreciate from the images shown, and quantitative analysis would be necessary to support this conclusion.

Another example appears in Figure 2, where the authors claim that "heatmap analysis revealed that transcriptomic profiles of PAR knockout cells progressively diverged from wild type from day 3 onwards". This conclusion is not fully supported by the presented data for two reasons: (1) transcriptomic divergence is more appropriately assessed through principal component analysis, clustering, or distance-based methods rather than by visual inspection of a heatmap alone; and (2) although some genes displayed in panel E begin to show genotype-associated differences from day 3, the overall transcriptomic structure shown in the PCA and heatmap remains primarily dominated by temporal progression rather than genotype.

In this context, it remains unclear whether PAR knockout cells truly retain a more naïve pluripotent transcriptomic identity. To support this claim, the authors should compare the knockout transcriptome directly against a naïve pluripotent population. The phenotype observed in the knockout cells may instead represent an incomplete or aberrant primed transition rather than maintenance of naïve pluripotency itself. Intermediate morphogenetic states, such as rosette-like epithelial stages, could also explain the observed phenotype.

Strengthening this aspect of the study would substantially improve its developmental and in vivo relevance, which currently appears somewhat limited. In particular, it would be interesting to determine whether this mechanism operates during embryogenesis itself. The authors could consider relatively simple but informative experiments, such as perturbing PAR signaling or Furin activity during embryo culture.

Along the same lines, some statements in the manuscript appear overly speculative. For example, the statement that "these findings may reveal a developmental compensation mechanism during embryogenesis, whereby normal cells rescue defective cells or increase their own proportion" extends well beyond the experimental evidence presented. Such claims invoke concepts related to cell competition, abnormal cell recognition, or developmental quality control mechanisms in vivo, none of which are directly demonstrated in this study. The authors are encouraged either to substantially tone down these statements or move them to the Discussion as speculative possibilities.

Another important conceptual point concerns the relationship between PAR complex regulation and Lefty signaling. If this mechanism indeed reflects a physiological or homeostatic process operating during embryogenesis, what would be the developmental rationale for the PAR complex regulation of Lefty? Lefty is well known for its role during gastrulation and anterior epiblast patterning. It would therefore be interesting if the authors could further discuss potential links between these developmental contexts.

Minor points:

(1) The authors state that PAR knockout cells do not exhibit major differences in self-renewal capacity; however, they simultaneously claim that these cells remain in a more naïve-like state. This interpretation requires clarification, as naïve pluripotent cells are typically associated with increased clonogenicity, enhanced self-renewal, and expression of markers such as alkaline phosphatase and SSEA1 compared to primed cells. The relationship between the observed phenotype and the proposed "naïve-like" state should therefore be discussed more carefully.

(2) The authors generated several independent knockout clones, but appear to use only one clone for downstream analyses after observing similar morphogenetic phenotypes. Is this sufficient to account for potential clonal heterogeneity? Would the use of pooled clones provide a more robust experimental system?

(3) The rescue experiments using pathway inhibitors are interesting; however, the interpretation again relies primarily on colony morphology. Readers may question whether these experiments truly represent rescue of the naïve-to-primed transition itself without additional transcriptomic or molecular characterization.

(4) In Figure 4, the manuscript could be strengthened by integrating transcriptomic analyses from pharmacological treatments with the secreted-factor and co-culture datasets.

(5) The authors could better clarify the context of Furin downregulation in the knockout cells. Is this a direct consequence of altered transcriptional regulation by the PAR complex, or could it instead represent a secondary consequence of impaired progression through the primed pluripotent transition?

Reviewer #1 (Public review):

The wide-ranging serotonergic projections emerging from the Dorsal Raphe nucleus (DRN) is suggestive of a central role in regulating brain-wide activity and behavioural states. DRN activity has been associated to 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.

Comments on revised version.

The authors successfully addressed my points.

Reviewer #1 (Public review):

Summary:

In this article by Xiao et al. the authors aimed to identify the precise targets by which magnesium isoglycyrrhizinate (MgIG) functions to improve liver injury in response to ethanol treatment. The authors found through a series of in-vivo and molecular approaches that MgIG treatment attenuates alcohol-induced liver injury through a potential SREBP2-IdI1 axis. The revised manuscript adds to a previous set of literature showing MgIG improves liver function across a variety of etiologies, and also provides mechanistic insight into its mechanism of action. All major weaknesses were addressed in the revised submission.

Strengths:

(1) The authors use a combination of approaches from both in-vivo mouse models to in-vitro approaches with AML12 hepatocytes to support the notion that MgIG does improve liver function in response to ethanol treatment.

(2) The authors use both knockdown and overexpression approaches, in-vivo and in-vitro, to support most of the claims provided.

(3) Identification of HSD11B1 as the protein target of MgIG, as well as confirmation of direct protein-protein interactions between HSD11B1/SREBP2/IDI1 is novel.

Comments on revision:

The authors addressed all my concerns. No additional comments.

Reviewer #1 (Public review):

Summary:

The authors combine PSMC and habitat modeling to try to connect habitat change during the Last Glacial Period to changes in Ne.

Strengths:

Observing how tropical single-island endemic bird species responded to habitat change in the past may help inform conservation interventions for these particularly vulnerable species. The combination of genomics and habitat modeling is a good idea-this sort of interdisciplinary thinking is what is needed to tackle these complex questions. Additionally, the use of PSMC makes it possible to perform this analysis on poorly-studied species with only a single genome available.

Room for Improvement:

A paper was cited to support the idea, but why coalescent Ne is a better predictor of extinction risk than current genomic diversity or current Ne isn't explicitly explained in this paper.

Differing PSMC parameters may also impact results: the differences between passerines and non-passerines was one of their main results. They explain why they chose different mutation rates for the two groups, but they do not provide any analysis to show this difference was not driven by the different mutation rates used for the two groups.

For five of the species tested, PSMC parameter differences led to different results, but the species shown in table S4 are different from what is listed in the manuscript.

Ecosystems are highly complex; there may also be other variables influencing past demographic change other than those explored here. Results should be interpreted with caution.

Reviewer #1 (Public review):

Summary of goals:

The authors' stated goal (line 226) was to compare gene expression levels for gut hormones between males and females. As female flies contain more fat than males, they also sought to identify hormones that control this sex difference. Finally, they attempted to place their findings in the broader context of what is already known about established underlying mechanisms.

Strengths:

(1) The core research question of this work is interesting. The authors provide a reasonable hypothesis (neuro/entero-peptides may be involved) and well-designed experiments to address it.

(2) Some of the data are compelling, especially positive results that clearly implicate enteropeptides in sex-biased fat contents.

Comments on revised version:

There are small but useful improvements in the revised manuscript. Textual revisions have helped clarify some points, and I particularly appreciate the model (Figure 5). It gives a broader overview of fat storage regulation, even if new insights are limited to a generic statement that this phenomenon is complex (e.g. line 261).

One crucial sticking point is again the handling of statistics. As the authors now explain, peptide knockdown effects are significant only if the experimental group differs from both parental controls (lines 191-194). By this definition (which is indeed the field standard and I also agree with), Tk knockdown had no significant effect (Figure 3B). The authors partially acknowledge this, initially calling the result a trend (line 198), but in many other places in their manuscript (e.g. lines 258-259, line 333) including in the Abstract (line 30) they (misre)present it as if it were significant. I have a huge problem with this, and it is the reason why I evaluate the strength of the evidence as Incomplete.

Overall, I do not think it is meaningful for authors to undergo a new (second) revision if they do not carry out experiments to address key points.

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:

The manuscript by Bohra et al. describes the indirect effects of ligand-dependent gene activation on neighboring non-target genes. The authors utilized single-molecule RNA-FISH (targeting both mature and intronic regions), 4C-seq, and enhancer deletions to demonstrate that the non-enhancer-targeted gene TFF3, located in the same TAD as the target gene TFF1, alters its expression when TFF1 expression declines at the end of the estrogen signaling peak. Since the enhancer does not loop with TFF3, the authors conclude that mechanisms other than estrogen receptor or enhancer-driven induction are responsible for TFF3 expression. Moreover, ERα intensity correlations show that both high and low levels of ERα are unfavorable for TFF1 expression. The ERa level correlations are further supported by overexpression of GFP-ERa. The authors conclude that transcriptional machinery used by TFF1 for its acute activation can negatively impact the TFF3 at peak of signaling but once, the condensate dissolves, TFF3 benefits from it for its low expression.

Strengths:

The findings are indeed intriguing. The authors have maintained appropriate experimental controls, and their conclusions are well-supported by the data.

Reviewer #2 (Public review):

Summary:

Zhang and colleagues investigate the molecular mechanisms by which the small brown planthopper (SBPH, Laodelphax striatellus) manipulates host rice carbohydrate metabolism to enhance its own fitness. Using a combination of molecular, pharmacological, and biochemical approaches, they demonstrate that SBPH infestation induces systemic glucose reallocation in rice, as evidenced by the upregulation of glucose levels in aerial tissues and simultaneous reduction in root glucose levels. Notably, host-derived glucose acts as a central signaling molecule, driving two key adaptive traits: enhanced fecundity via the glucose-TOR-JH-Vg signaling cascade, and increased imidacloprid tolerance through synergistic metabolic (GCL-GSH) and regulatory (TOR-JH-GST) pathways targeting GST activity. These findings uncover a sophisticated resource-manipulation strategy in SBPH and identify nutrient-sensing and detoxification pathways as potential targets for pest control.

Strengths:

(1) The study addresses a gap in plant-insect coevolution research by identifying glucose as a dual-function signaling molecule that coordinates SBPH reproduction and insecticide tolerance, providing valuable insights into how herbivores exploit host nutritional signals.

(2) The experimental design is well structured and multifaceted, integrating RNAi, RT-qPCR, Western blotting, pharmacological inhibition, and biochemical assays. The use of appropriate controls (e.g., osmotic controls with mannitol and hydrolase-inhibitor rescue experiments) strengthens the causal interpretation of the results.

(3) The mechanistic framework is clear and well-supported. The authors delineate two interconnected molecular cascades (glucose-TOR-JH-Vg for fecundity and GCL-GSH/TOR-JH-GST for tolerance) with hierarchical validation (e.g., rescue experiments with JHA), ensuring the reliability of conclusions.

Weaknesses:

(1) The study focuses exclusively on SBPH without validating whether the observed phenomena and mechanisms are conserved in closely related planthopper species (e.g., brown planthopper Nilaparvata lugens). This limitation restricts the generalizability of the findings to other economically important rice pests.

(2) The specific upstream signals that trigger glucose reallocation in rice (e.g., SBPH salivary effectors or oviposition-associated factors) are not identified. Although this represents a complex and independent research direction, the absence of such information limits the depth and completeness of the mechanistic framework and leaves open questions regarding the initiation of host metabolic manipulation.

(3) Insecticide tolerance assays are limited to imidacloprid. Extending these analyses to one or two additional commonly used insecticides (e.g., thiamethoxam) would help determine whether the glucose-mediated detoxification pathway is specific to imidacloprid or reflects a broader resistance mechanism, thereby strengthening conclusions regarding the generality of the GST activation cascade.

(4) Given the study's potential implications for pest management, the manuscript would benefit from a brief discussion of possible practical applications, such as manipulating rice glucose metabolism through breeding strategies or developing small-molecule inhibitors targeting the TOR-JH axis. Including such perspectives would enhance the translational relevance of the work by linking mechanistic insights to real-world pest control strategies.

Comments on revised version.

The authors have comprehensively and satisfactorily addressed all my comments. The revised manuscript shows significant improvement in quality. I have no further questions or suggestions.

Reviewer #1 (Public review):

Summary:

In this study, the authors propose that HSV-1 infection degrades the class I histone deacetylases HDAC1 and HDAC2. The MDM2 E3 ubiquitin ligase from the DNA damage response pathway is responsible for ubiquitinating these HDACs that are subsequently degraded via proteasomes. The authors hypothesize that HDAC degradation will cause hyperacetylation of viral chromatin and enable viral gene transcription.

Strengths:

The ubiquitination of HDAC1 & HDAC2 by Mdm2 and the mapping studies are clear.

Comments on revised version:

The authors enhanced their manuscript by more supportive data and providing clarification and the necessary corrections. However, a few more issues pertain:

(1) In Figure 4j at 2 h post-infection we typically see the input virus and not progeny virus production. The input seems to have about 1-log difference that is expected to impact the results.

(2) Figs 1A, 1E, 2H it seems unclear why ICP4 becomes detectable at 12 h post-infection in HeLa cells? How about other a-genes? How about other cells? ICP4 is typically detectable within 2-3 h post-infection.

(3) In responses 2-2, Fig 5K: An infection without transfection has not been included. This is important to understand kinetics of infection in transfected cells.

(4) Why HDAC1 with deleted NES does not accumulate or looks like it is degraded? Why then ICP4 does not accumulate?

Reviewer #2 (Public review):

Summary:

This paper presents results interpreted to indicate that sequences upstream of stop codons capable of base-pairing with the 3' end of 18S rRNA prolong the dwell time of 80S ribosomes at stop codons in a manner impeded by Rps26 in the 40S subunit exit channel, which leads to the proper completion of termination and ribosome recycling and prevents spurious translation of 3'UTR sequences by one or more unconventional mechanisms.

Strengths:

The standard 80S and selective eRF1 80S ribosome profiling data obtained using EZRA-Seq are of high quality, allowing the authors to detect an enrichment for purine-rich sequences upstream of stop codons at sites where termination is relatively slow and ribosomal complexes are paused with eRF1 still engaged in the A site.

Weaknesses:

There are many weaknesses in the experimental design and interpretation of results that undermine several of the final conclusions of the study described in the abstract, as described in detail below.

(1) It's not indicated how far upstream of the stop codon the sequences were searched to find the enriched motifs in Figs. 1C and 2D. If it's further upstream of -15 then the sequence would generally not be found in the exit channel of a terminating ribosome positioned with the stop codon in the A site in the manner expected from their final model of mRNA:18S rRNA pairing. (This would be analogous to the occurrence of the Shine-Dalgarno within 15 nt of the initiation codon for most mRNAs in E. coli.) They could have depicted nucleotide percentages at each nucleotide from -1 to -15 for the high and low pause stop codons to better facilitate consideration of their proposed mechanism of termination pausing involving the 3' end of 18S rRNA.

(2) lines 234-242: Their reporter data in Fig. 4B suggest that only the presence of GGG triplets at any location in the 9 nt substantially prevents downstream translation. If their interpretation about these G-rich sequences promoting termination by forming G-quadruplexes is correct, then this would have little to do with the purine-rich motifs identified by the profiling experiments (and their proposed function in base-pairing with rRNA), as the purine-rich motifs do not feature GG bases (as shown in Fig. 2D in particular). The authors point out that the MPRA can sample sequence space not represented in living cells. While true, this doesn't change the fact that it failed identify sequences conforming to the purine rich motifs found by the profiling experiments and identified instead sequences capable of forming G-quadruplexes that may well function by a different mechanism than that employed in cells. The authors cannot persist in claiming that the MPRA results confirm the findings of the profiling experiments regarding the purine-rich motif. Also, the claim of enrichment for C-rich sequences in the MPRA results is not compelling as only 3 of the 11 triplets showing the smallest M/P ratios contain more than 1 C and three of them contain no Cs. Also, there was no evidence for depletion of C's upstream of the stop codons with low pause scores from the ribosome profiling data in Fig. 1, so it's inaccurate to claim "mirroring" of results from the ribosome profiling and MPRA data on this point as well.

(3) lines 256-260: I still contend that the different results shown in Fig. 4E for the C-rich and GA-rich sequences are not compelling as results for only a single sequence of each type are shown, which might not be typical of the entire class. In fact, the GA-rich sequence has two GG's and could form a G-quadruplex, whereas the GA-rich motifs identified by ribosome profiling and eRF1-seq do not exhibit consecutive GGs, such that the single G-rich sequence chosen for analysis might function by G-quadruplex mediated stalling rather than base-pairing with the 3' end of 18S rRNA, as they actually suggested in their rebuttal. Even the second GA-rich sequence analyzed in Fig. S3G has two GGs. Thus, while the results in Fig. 4 provide support for the notion that C-rich sequences preceding the stop codon promote stop codon read-through, it's important to note that no evidence was obtained by ribosome-profiling in Fig. 1 that the increased 3'UTR translation seen for low-pause stop codons is associated with C-rich sequences. It's unclear why they would be unable to observe this in the manner they document for the eRF1-Seq data in Fig. 2D for the three C-rich triplets enriched at stop codons lacking eRF1 peaks.<br /> - lines 278-282: These differences are quite small and could arise from the different sequences of the GFP-HiBit fusion proteins, as observed in Fig. 4C (top two control constructs), precluding mechanistic interpretations.

(4) Notwithstanding their claim in the rebuttal, I still find no definition of the GA-rich and C-rich mRNAs described in Fig. 5C in the Methods or legends, nor whether the compilation is restricted to -15 from the stop codons. In addition, if expression of the mutant 18S rRNA is sufficient to alter the height of the termination peaks as shown in Fig. 5C and to alter reporter expression in Fig. 5D, I see no reason why they cannot carry out the pause score/motif enrichment of Fig. 1C to determine if they see the expected diminished enrichment for the GA-motif shown there on expressing the mutant 18S vs. the WT 18S control strain. If not, this would undermine their interpretation of the results in Figs. 5C-D as favoring base-pairing between the 3' end of 18S rRNA and sequences upstream of the stop codon.

(5) I still find a significant shortcoming in their failure to analyze the 18S rRNA 3' end biochemically to show that the expected ~15% with the mutant sequence. Stating simply that they followed a previous protocol is not sufficient to document their success in this notoriously challenging experimental approach.

(6) lines 382-384: The level of the control protein RACK1 is diminished in testis polysomes, and it's unclear that the ratio of Rps26:RACK1 is actually lower in testis polysomes in the manner claimed.

(7) lines 414-427: I still contend that the authors should have quantified the ratio of the stop codon peak to the adjacent coding sequences in Figures 7E to establish that Rps26 OE decreased the stop codon peaks selectively on the GA-rich cohort of mRNAs. In addition, they still have not explained why the C-rich reporter behaves like the GA-rich reporter in Fig. 7F in showing reduced HiBiT expression on Rps26 OE when it should be unaffected. As such, the reporter data do not support the conclusion reached from the data in Fig. 7E.

(8) Notwithstanding their rebuttal I still contend that the failure to measure Rps26 association with 80S ribsoomes or polysomes and show that it is depleted by the shRNA knockdown and increased by Rps26 OE is a significant shortcoming, especially since their interpretation of the OE data depends on the occurrence of 40S subunits lacking Rps26 in unstressed WT cells, which seems improbable based on the prior work on yeast.

(9) Overall, examining the claims in the revised Abstract, I feel that I am in agreement with the claim "We identify a sequence motif upstream of the stop codon that promotes termination pausing,.." but disagree that the function of this motif was "validated by massively paralleled reporter assays", for the reasons stated above in point 2. Regarding the statement "Unexpectedly, reduced termination pausing increases the likelihood of stop codon slippage, giving rise to proteins with heterogenous C-terminal extensions." , I believe it would be more cautious to say that "reduced pausing is associated with stop codon read-through accompanied by frameshifting" since the MRPA did not provide compelling evidence for causality for the reasons described in point 3 above. Regarding the statement "Mechanistically, we show that sequence-dependent termination pausing arises from post-decoding mRNA scanning by the 3' end of 18S rRNA", I find this statement too strong in view of the shortcomings described above in points 4-5 and think it would be more correct to say that their findings are consistent with (rather than showing) this point, and also think they should add qualifying statements to the manuscript acknowledging the limitations of these experiments. I further contend that there are shortcomings in the experiments leading to the conclusion that the stoichiometry of Rps26... modulates mRNA:rRNA interactions, described above in points 6-9. Finally, in the last sentence, the claims that termination pausing is shaped by ribosome heterogeneity, and cell type-specific translational control is too strong.

Reviewer #1 (Public review):

Summary:

Plasmodesmata are channels that allow cell-cell communication in plants; based on the functional similarities between facilitated transport within plasmodesmata and into the nucleus, the authors speculate that nuclear pore complex proteins might be involved in plasmodesmata function. In this manuscript, they localize nuclear pore complex proteins to plasmodesmata using proteomics and heterologous overexpression. They also document a possible plasmodesmata transport defect in a mutant affecting one nuclear pore complex protein.

Strengths:

The main strength of this manuscript is the interesting and novel hypothesis. This work could open exciting new directions in our understanding of plasmodesmata function and cell-cell communication in plants. They also localized many NUPs (12/35 Arabidopsis NUPs).

Weaknesses:

The main weakness of this manuscript is that the data are solid, but could benefit from further controls. The authors appropriately and frequently acknowledge caveats to their data, which include: 1) that the proteomics preparations cannot completely purify plasmodesmata; 2) heterologous expression does not allow them to assess the function of the fluorescently-tagged NUPs; 3) some NUPs may be overexpressed, especially in the heterologous system, which can lead to localization artefacts; 4) ER-localized proteins can appear partially localized to plasmodesmata.

Comments on revised version.

In the revised version of the manuscript, the authors have addressed my main concerns from the previous review and they acknowledge the caveats and alternative interpretations to their results in the text. However, although some important controls have been added, the rationale for why different NUPs were used in different control experiments is often unclear, and it is also unclear why specific NUPs (corresponding to different locations in the nuclear pore complex) were selected for each experiment. This includes:

a) Expression level analysis via proteomics: NUP62 (core FG NUP)<br /> b) Colocalization with known PD protein: HOS1 (outer ring)<br /> c) Colocalization with ER marker: NUP43 (outer ring)<br /> d) Complementation assays: CPR5 (membrane anchor) - only the rationale for this choice is articulated clearly (lines 224-228).

However, they have not systematically conducted all controls for one NUP, nor explained why they selected specific different NUPs, corresponding to different localizations within the complex, for the control experiments.

Generally, the manuscript needs careful proofreading. There are a number of typos, misused punctuation, sentence fragments, etc.

- As one example, see the legend for Figure 5: there are two different definitions of white arrowheads, yet green are not defined; there is a sentence fragment on line 1320 ("And aniline blue."); there is double punctuation on line 1321 "localization.,"; and red arrows are defined as "mCherry-HDEL specific localization., without overly with other markers" yet in several cases, they point to either 1) regions of only mCherry-HDEL in cells not expressing NUP43-mVenus (both red arrows in the second row of images, which are biologically meaningless and potentially misleading) or 2) red arrows pointing to sites where mCherry-HDEL and NUP43-mVenus are colocalized (top two red arrows in the first row of images, which are biologically meaningful yet incorrectly interpreted by the authors). These are just a small example set of the proofreading required.

Reviewer #1 (Public review):

Summary:

Some of the authors proposed in a PNAS paper in 2016 the occurrence of the Entner-Doudoroff (ED) pathway in cyanobacteria and plants, on the basis of several lines of biochemical and genetic evidence. However, more recent results indicated that one of the two specific enzymes of the ED pathway (EDD) is missing in Synechocystis PCC 6803. The authors carried out additional experiments, which demonstrated that EDD is missing, and one of the enzymes (ED aldolase) is a promiscuous enzyme which seems to be involved in proline metabolism and is not actually participating in the ED pathway as initially believed. The results described in this paper are strong evidence that this new interpretation is appropriate, and therefore, it corrects the previous proposal, providing an honest description of the reasons why the authors had reached the wrong conclusion about the existence of the ED pathway in cyanobacteria and plants.

Strengths:

Thorough reanalysis of the experimental results obtained in previous studies, which led to the publication of the PNAS paper in 2016.

New experimental evidence to confirm that enzymes previously considered as participating in the ED actually are not catalyzing the ED biochemical reactions, but are involved in other metabolic pathways. Also, the authors completely discarded the occurrence of the GDH/GK shunt in Synechocystis PCC 6803. Generally speaking, the manuscript is very clearly written, with a precise description of the previous findings, the mistakes which took place in the 2016 paper, and the strategies they have used to address those issues, in order to reach a thoroughly revised vision of the glucose metabolic pathways in Synechocystis PCC 6803. In this regard, the drawings shown in Figures 1 and 7 are very helpful for the reader to follow the story and understand the possible metabolic transformations depending on the working hypothesis.

Also, I commend the authors for openly describing previous mistakes. In this paper, they reassess past observations in light of more recent findings and to integrate the information in this manuscript. The scientific conclusions are solid and very interesting, and besides, they use the opportunity to offer valuable advice to researchers. This is especially focused on the importance of careful biochemical characterization of enzymes, which should always be carried out when studying proteins which have been identified as a specific enzyme on the basis of sequence homology. In a similar way, they found that an insertional mutant was the cause of the absence of specific metabolites, which had been attributed to particularities of a metabolic pathway in that mutant, when it was actually due to a nucleotide insertion; this could have been easily prevented by confirming the correct generation of the mutant by DNA sequencing.

Weaknesses:

The authors propose that EDA might be involved in the PEP-pyruvate-OAA node, or in the proline metabolism, but this requires further experimental work for clarification; what their results indicate clearly is that this enzyme is not actually catalyzing the transformation of KDPG to GAP, which is the second specific enzyme of the ED pathway. But the real physiological function in this cyanobacterium is still unconfirmed.

Another aspect which could be improved is that the recombinant expression of some genes was carried out in E. coli; even if this is a useful and valid research strategy, in studies like this (where there is a strong focus on the physiological function of enzymes in the original organism, Synechocystis PCC 6803), I think it would have been more appropriate to express the 6803 genes in another cyanobacterium easily amenable for genetic transformation and gene expression, which would produce the protein in a physiological environment more similar to another cyanobacterium (compared to E. coli, which is an heterotrophic bacterium). I am not sure this would change any of the obtained results, but it certainly would confer additional robustness to the enzymatic results.

Bibliography:

I think the list of papers used in this manuscript is complete and up to date. However, I do miss recent papers which addressed one aspect that was proposed in the original 2016 PNAS paper: the authors wrote, "We therefore suggest that Prochlorococcus might oxidize glucose via the ED pathway under mixotrophic conditions, as shown for Synechocystis." Recent studies checked this hypothesis and have shown that the ED pathway seems to be also missing in Prochlorococcus and marine Synechococcus, and I think this manuscript is a good place to cite them, since these results are consistent with the findings of this paper.

Reviewer #1 (Public review):

Summary:

The authors attempt to use a combination of behavioural and EEG analyses in order to investigate whether expectation of task difficulty influences spatial focus narrowing in the context of a spatially cued task, alongside an expected attention-related amplitude effect. This distinguishes the experiment from previous tasks which looked at this potential spatial narrowing in the context of more non-cued diffuse attention tasks. The authors present 2 major findings.<br /> (1) Behaviourally, they analysed the effects of cue validity and difficulty expectation on response accuracy and found that participants displayed an effect of difficulty expectation in validly cued trials, showing relatively enhanced behaviour to Hard Expectation trials, but no effect of expectation in invalidly cued trials.<br /> (2) Inverted encoding modelling on broadband EEG showed greater pre-target attentional processing in the Hard Expectation blocks. They go on to show that this enhancement comes in the form of greater amplitude of the Channel Tuning Functions (CTFs) approximately 300 to 400ms post-cue, in the absence of any spatial tuning specificity enhancement (as would be evident in a difference in CTF fit width). Together these results provide valuable findings for those investigating the separable effects of expectation and attention on target detection in visual search.

Strengths:

(1) This is a very solidly performed experiment and analysis, with different streams of evidence convincingly pointing in the same direction, i.e. a gain effect of Expectation in the absence of a spatial tuning effect.

(2) EEG is competently analysed and interpreted, and the paper is well written, and simple in its motivation.

(3) The authors report appropriately on the results in the Discussion, without overreaching.

Comments on revised version:

The authors have addressed all of my comments. Very interesting work, thank you!

Reviewer #1 (Public review):

Summary:

This useful study provides incomplete evidence of an association between atovaquone-proguanil use (as well as toxoplasmosis seropositivity) and reduced Alzheimer's dementia risk. The study reinforces findings that VZ vaccine lowers AD risk and suggests that this vaccine may be an effect modifier of A-P's protective effect. Strengths of the study include two extremely large cohorts, including a massive validation cohort in the US. Statistical analyses are sound, and the effect sizes are significant and meaningful. The CI curves are certainly impressive.

Weaknesses include the inability to control for potentially important confounding variables. In my view, the findings are intriguing but remain correlative / hypothesis generating rather than causative. Significant mechanistic work needs to be done to link interventions which limit the impact of Toxoplasmosis and VZV reactivation on AD.

Weaknesses:

Major:

(1) Most of the individuals in the study received A-P for malaria prophylaxis as it is not first line for Toxo treatment. Many (probably most) of these individuals were likely to be Toxo negative (~15% seropositive in the US), thereby eliminating a potential benefit of the drug in most people in the cohort. Finally, A-P is not a first line treatment for Toxo because of lower efficacy.

(2) A-P exposure may be a marker of subtle demographic features not captured in the dataset such as wealth allowing for global travel and/or genetic predisposition to AD. This raises my suspicion of correlative rather than casual relationships between A-P exposure and AD reduction. The size of the cohort does not eliminate this issue, but rather narrows confidence intervals around potentially misleading odds ratios which have not been adjusted for the multitude of other variables driving incident AD.

(3) The relationship between herpes virus reactivation and Toxo reactivation seems speculative.

(4) A direct effect on A-P on AD lesions independent on infection is not considered as a hypothesis. Given the limitations above and effects on metabolic pathways, it probably should be. The Toxo hypothesis would be more convincing if the authors could demonstrate an enhanced effect of the drug in Toxo positive individuals without no effect in Toxo negative individuals.

Minor:

(5) "Clinically meaningful" should be eliminated from the discussion given that this is correlative evidence.

Reviewer #1 (Public review):

Summary:

In this manuscript, Torro et al. presented CellDetective, an open-source software designed for a user-friendly execution of single cell segmentation, tracking and analysis of time-lapse microscopy data. The authors demonstrated the applications of the software by measuring NK cell spreading events acquired with reflection interference contrast microscopy (RICM), as well as detecting target cell death events and their interaction with neighboring NK cells in a multichannel widefield microscopy datasets.

Strengths:

The segmentation (StarDist, Cellpose) and tracking (bTrack) modules implemented were based on existing and published software packages, while the event detection, classification and analysis modules were added by the authors to enable an end-to-end time-lapse microscopy data processing and analysis pipeline, complete with graphical user interface (GUI) to minimize coding experience required from the user. The latest iteration of CellDetective also incorporates new features that enable multiple cell subsets to be examined and visualized. The documentation that accompanies CellDetective is also well written.

Weaknesses:

The current iteration of CellDetective is still limited to 2D 'widefield' analysis, although the authors have provided convincing justification for the current implementation for 2D + time analysis and clarified such limitations of the software in the manuscript. This reviewer maintains that support for 3D + time analysis in future iterations of CellDetective will substantially improve its applicability across broad disciplines, especially with emerging focus on 3D organoid studies.

Additionally, this reviewer has also encountered a key technical issue with the latest version of CellDetective (v1.5.2, installed on Windows 11 25H2) where the main CellDetective window is displayed in a fixed size that prevented the user from accessing the user interface/buttons that are essential for operating the software. As an example, in the very first demo (https://celldetective.readthedocs.io/en/latest/first-experiment.html), the fixed window size prevented this reviewer from accessing the "Submit" button in Step 2: Segment Cells (which is not visible as the fixed window size only displayed a certain portion of the GUI) of the workflow. This limitation made it near impossible to evaluate the useability and stability of the software. Fixing this issue by making the window size adjustable such that these buttons of the interface can be accessed by the user will be important to ensure the useability of the software.

This reviewer understands the difficulties and time involved in bug fixing, and hope that the experience could have been much smoother and the software behaves much more stably in order to maximize its useability.

Reviewer #1 (Public review):

Summary:

This paper investigates the physical basis of epithelial invagination in the morphogenesis of the ascidian siphon tube. The authors observe changes in actin and myosin distribution during siphon tube morphogenesis using fixed specimens and immunohistochemistry. They discover that there is a biphasic change in the actomyosin localization that correlates with changes in cell shapes. Initially, there is the well-known relocation of actomyosin from the lateral sides to the apical surface of cells that will invaginate, accompanied by a concomitant lengthening of the central cells within the invagination, but not a lot of invagination. Coincident with a second, more rapid, phase of invagination, the authors see a relocalization of actomyosin back to the lateral sides of the cells. This 2nd "bidirectional" relocation of actin appears to be important because optogenetic inhibition of myosin in the lateral domain after the initial invaginations phase resulted in a block of further invagination. Although not noted in the paper, that the second phase of siphon invagination is dependent on actomyosin is interesting and important because it has been shown that during Drosophila mesoderm invagination that a second "folding" phase of invagination is independent of actomyosin contraction (Guo et al. eLife 2022), so there appear to be important differences between the Drosophila mesoderm system and the ascidian siphon tube systems.

Using the experimental data, the authors create a vertex model of the invagination, and simulations reveal a coupled mechanism of apicobasal tension imbalance and lateral contraction that creates the invagination. The resultant model appears to recapitulate many aspects of the observed cell behaviors, although there are some caveats to consider (described below).

Strengths:

The studies and presented results are well done and provide important insights into the physical forces of epithelial invagination, which is important because invaginations are how a large fraction of organs in multicellular organisms are formed.

Weaknesses:

(1) This reviewer has concerns about two aspects of the computational model. First, the model in Fig. 5D shows a simulation of a flat epithelial sheet creating an invagination. However, the actual invagination is occurring in a small embryo that has significant curvature, such that nine or so cells occupy a 90-degree arc of the 360-degree circle that defines the embryo's cross-section (e.g., see Fig. 1A). This curvature could have important effects on cell behavior.

(2) The second concern about the model is that Figure 5 D shows the vertex model developing significant "puckering" (bulging) surrounding the invagination. Such "puckering" is not seen in the in vivo invagination (Fig. 1A, 2A). This issue is not discussed in the text, so it is unclear how big an issue this is for the developed model, but the model does not recapitulate all aspects of the siphon invagination system.

(3) In Fig. 2A Top View and the schematic in Fig. 2C, the developing invagination is surrounded by a ring of aligned cell edges characteristic of a "purse string" type actomyosin cable that would create pressure on the invaginating cells that has been documented in multiple systems. Notably, the schematic in Fig 2C shows myosin II localizing to aligned "purse string" edges, suggesting the purse string is actively compressing the more central cells. If the purse string consistently appears during siphon invagination, a complete understanding of siphon invagination will require understanding the contributions of the purse string to the invagination process.

(4) The introduction and discussion put the work in context of work on physical forces in invagination, but there is not much discussion of how the modeling fits into the literature.

Comment on revised version.

This is an extensively revised version of a previously submitted manuscript that, as detailed in their 20-page response to the first reviews, satisfactorily addresses the reviewers' comments. In particular, the revised manuscript makes it much clearer how this work fits into and advances the field. The added experiments strengthen the rigor of the manuscript as well. Overall, this paper is ready to go.

Reviewer #4 (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:

The authors demonstrate a computational rational design approach for developing RNA aptamers with improved binding to the Receptor Binding Domain (RBD) of the SARS-CoV-2 spike protein. They demonstrate the ability of their approach to improve binding affinity using a previously identified RNA aptamer, RBD-PB6-Ta, which binds to the RBD. They also computationally estimate the binding energies of various RNA aptamers with the RBD and compare against RBD binding energies for a few neutralizing antibodies from the literature. Finally, experimental binding affinities are estimated by electrophoretic mobility shift assays (EMSA) for various RNA aptamers and a single commercially available neutralizing antibody to support the conclusions from computational studies on binding. The authors conclude that their computational framework, CAAMO, can provide reliable structure predictions and effectively support rational design of improved affinity for RNA aptamers towards target proteins. Additionally, they claim that their approach achieved design of high affinity RNA aptamer variants that bind to the RBD as well or better than a commercially available neutralizing antibody.

Strengths:

The thorough computational approaches employed in the study provide solid evidence of the value of their approach for computational design of high affinity RNA aptamers. The theoretical analysis using Free Energy Perturbation (FEP) to estimate relative binding energies supports the claimed improvement of affinity for RNA aptamers and provides valuable insight into the binding model for the tested RNA aptamers in comparison to previously studied neutralizing antibodies. The multimodal structure prediction in the early stages of the presented CAAMO framework, combined with the demonstrated outcome of improved affinity using the structural predictions as a starting point for rational design, provide moderate confidence in the structure predictions.

Reviewer #1 (Public review):

Summary:

Authors have investigated the role of FMRP in the formation and function of RNA granules in mouse brain/cultured hippocampal neurons. Most of their results indicate that FMRP does not have a role in the formation or function of RNA granules with specific mRNAs but may have some role in distal RNA granules in neurons and their response to synaptic stimulation. This is an important work (though the results are mostly negative) in understanding the composition and function of neuronal RNA granules. the last part of the work in cultured neurons is disjointed from the rest of the manuscript and the results are neither convincing nor provide any mechanistic insight.

Strengths:

(1) The study is quite thorough, the methods and analysis used are robust and the conclusion and interpretation are diligent.

(2) The comparative study of Rat and Mouse RNA granules is very helpful for future studies

(3) The conclusion that the absence of FMRP does not affect the RNA granule composition and many of its properties in the system the authors have chosen to study is well supported by the results

(4) The difference in the response to DHPG stimulation concerning RNA granules described here is very interesting and could provide a basis for further studies though it has some serious technical issues (see below)

Weaknesses:

(1) The system used for the study (P5 mouse brain or DIV 8-10 cultured neuron) is surprising as the majority of defects in the absence of FMRP are reported in later stages (P30+ brain and DIV 14+ neurons). It is important to test if the conclusions drawn here hold good at different developmental stages.

(2) The term 'distal granules' is very vague. Since there is no structural or biochemical characterization of these granules it is difficult to understand how they are different from the proximal granules and why FMRP has an effect only on these granules.

(3) Since the manuscript does not find any effect of FMRP on neuronal RNA granules, it does not provide any new molecular insight with respect to the function of FMRP

Comments on revised version.

The authors have answered several questions raised by the reviewers. But for me, the critical issue of using only the brain from P5 animals and relatively early DIV neurons is still not convincingly addressed. FMRP may still play a role in determining the stalled ribosomes on its target mRNAs at a later stage of development, when there is more scope for activity-mediated protein synthesis.

I agree with the authors that this work helps the molecular understanding of FMRP functions by disproving one of the long-standing hypotheses.

Reviewer #1 (Public review):

Summary:

The article by Zdraljevic et al. reports the discovery of a third toxin-antidote (TA) element in C. elegans, composed of the genes mll-1 (toxin) and smll-1 (antidote). Unlike previously characterized TA systems in C. elegans, this element induces larval arrest rather than embryonic lethality. The study identifies three distinct haplotypes at the TA locus, including a hyper-divergent version in the standard laboratory strain N2, which retains a functional toxin but lacks a functional antidote. The authors propose that small RNA-mediated silencing mechanisms, dependent on MUT-16 and PRG-1, suppress the toxicity of the divergent toxin allele. This work provides insights into the evolutionary dynamics of TA elements and their regulation through RNA interference (RNAi).

Overall, there are many things to like about this paper and only a few small quibbles, which will not require more than a little rewriting or relatively minor analyses.

Strengths of the Paper:

(1) The discovery of a maternally deposited TA element with delayed toxicity due to delayed mRNA translation of the maternally deposited toxin mRNA is a significant addition to the literature on selfish genetic elements in metazoans.

(2) Identifying three haplotypes at the TA locus provides a snapshot of potential evolutionary trajectories for these elements, which are often inferred but rarely demonstrated in naturally occurring strains. The genomic analysis of 550 wild isolates contextualizes the findings within natural populations, revealing geographic clustering and evolutionary pressures acting on the TA locus.

(3) The study employs various techniques, including CRISPR/Cas9 knockouts, FISH, long-read RNA sequencing, and population genomics. The use of inducible systems to confirm toxicity and antidote functionality is particularly robust. This multifaceted approach strengthens the validity of the findings.

(4) The authors provide compelling evidence that small RNA pathways suppress toxin activity in strains lacking a functional antidote. This highlights an alternative mechanism for neutralizing selfish genetic elements.

Comments on revised version.

The authors have addressed all my (relatively minor) comments from the first round of reviews. However, the most substantial comments came from Reviewer 2, mostly focused on the conclusions that "Multiple lines of evidence suggest that the N2 tmrl-1 allele is recognized by piRNAs, leading to MUT-16-dependent 22G siRNA production and post-transcriptional silencing of the transcript." This is beyond my expertise to fully evaluate what is state-of-the-art in terms of acceptable evidence, so I will defer to Reviewer #2 for this.

Reviewer #3 (Public review):

Summary:

This study uses large-scale all-atom molecular dynamics simulations to examine the conformational plasticity of the HIV-1 envelope glycoprotein (Env) in a membrane context, with particular emphasis on how the transmembrane domain (TMD), cytoplasmic tail (CT), protomer cleavage, and membrane environment influence ectodomain orientation and antibody epitope exposure. By comparing Env constructs with and without the CT, explicitly modeling glycosylation, and embedding Env in an asymmetric lipid bilayer, the authors aim to provide an integrated view of how membrane-proximal regions and lipid interactions shape Env antigenicity, including epitopes targeted by MPER-directed antibodies.

Strengths:

The authors have made a heroic effort to address the concerns raised in the first two rounds of review, and the revised manuscript is substantively improved. The addition of dynamical cross-correlation maps, expanded citation of prior computational work, clarification of the membrane composition rationale, data deposition to Zenodo, and new contextualization has improved the flow and interpretation of the manuscript throughout. Several scientifically interesting aspects of the work merit highlighting with a brief discussion on how future studies can leverage this data to build upon its impact.

A key strength of this work remains the scope, scale, and realism of the simulation systems. The authors construct a very large, nearly complete-Env-scale model that includes a glycosylated Env trimer embedded in an asymmetric bilayer, enabling analysis of membrane-protein interactions that are difficult to capture experimentally. The inclusion of specific glycans at reported sites, and the focus on constructs with and without the CT or cleavage, are well motivated by existing biological and structural data.

The observation that R696 orientation and its interacting partners give rise to asymmetric protomer conformations and distinct TMD tilts is a notable finding. The statement that interactions between R696 and lipid headgroups or CT residues can be strong enough to introduce a kink into the TMD is well-supported by representative snapshots and consistent with prior isolated-TMD simulations. The use of two initialization depths ("high" and "low") to probe R696 leaflet preference is methodologically interesting and the authors' interpretation - that there is a slight bias toward cytoplasmic leaflet interactions, but that these contacts could be highly dynamic over the course of viral entry - is appropriately cautious. It would be valuable to explicitly frame this as a hypothesis with testable predictions that future experimental or enhanced-sampling work could address. Similarly, the equilibration-driven kinking of the TMD core, consistent with prior isolated-TMD studies, represents a useful validation that extends those earlier observations to the intact trimeric context.

The simulations reveal substantial tilting motions of the ectodomain relative to the membrane, with angles spanning roughly 0-30{degree sign} (and up to ~40{degree sign} in some analyses), while the ectodomain itself remains relatively rigid. This framing, that much of Env's conformational variability arises from rigid-body tilting rather than large internal rearrangements, is an important conceptual contribution. The authors also provide interesting observations regarding asymmetric bilayer deformations, including localized thinning and altered lipid headgroup interactions near the TMD and CT, which suggest a reciprocal coupling between Env and the surrounding membrane.

The analysis of antibody-relevant epitopes across the prefusion state, including the V1/V2 and V3 loops, the CD4 binding site, and the MPER, is another strength. The study makes effective use of existing experimental knowledge in this context, for example by focusing on specific glycans known to occlude antibody binding, to motivate and interpret the simulations.

Finally, the revised text provides clear context that situates the study's findings and discrepancies within the broader literature, strengthening the manuscript's clarity and interpretability.

Future work in the field:

As the authors appropriately acknowledge within in the text, these microsecond simulations capture only the closed ground state and with limited sampling due to the already computationally intensive nature of these simulations. Their simulation setup provides interesting foundational knowledge of this state and a framework for these additional important questions.

Additionally, the authors appropriately acknowledge that CT-TMD and CT-ectodomain correlations are difficult to interpret given limited structural confidence in these regions. Future experimental and computational work in the field can extend and build upon the author's framework, particularly as the authors have made their trajectories available for the public. Re-analysis of the authors' deposited MD trajectories-such as probing for exposure of cryptic epitopes and potential allosteric coupling-could serve as valuable extensions of this work, particularly as advancements in computational analysis has reached an inflection point.

Comments on revised version.

Bravo! The improved clarity was a delight to read and will increase the impact this study has on the field.

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:

Mitotic kinesins carry out crucial roles in intracellular motility and mitotic spindle organization. Although many mitotic kinesins have been extensively studied, a few conserved mitotic motors remain poorly explored, including chromosome-associated kinesins. Here, Furusaki et al reconstitute recombinant chromosome-associated kinesin or chromokinesin (Kid) and reveal processive plus-end motility along microtubules. The authors purify multiple versions of Kid, revealing dimeric organization and their processive microtubule plus-ended motility which depends on their conserved motor domains, neck linkers, and coiled-coil regions. The study reveals for the first time that KID can recruit and transport duplex DNA along microtubules using its conserved C-terminal DNA binding domain. The work provides crucial revised thinking about the mechanisms of Chromokinesins mitosis as physical processive motors that mobilize chromosomes towards the microtubule plus ends in early metaphase.

Strengths:

The authors reconstitute multiple chromosome-associated kinesin (KID) orthologs from Xenopus and humans with microtubules and determine their oligomerization. The study shows how coiled-coil and neck linker regions of KID are essential for its function as its deletion leads to non-processive motility. Chimeras placing the KID coiled-coil and neck linker on the KIF1A motor domain led to the production of a processive recombinant motor supporting the compatibility of their motility mechanisms. The KID c-terminal tail binds and transports only double-stranded DNA and its deletion or single-stranded DNA leads to defects in this activity.

Reviewer #1 (Public review):

This is a well-written and fully documented methods paper.

The authors have established a clear rationale for their new packages, especially for real-time use, and demonstrate significant speed improvements that will likely appeal to many users of tools like DLC, SLEAP, and LightningPose. The inclusion of a graphical user interface will help make the package more accessible to neuroscientists with limited computational expertise. While it may be challenging to get users to switch from their established workflows for video analysis, the speed gains offered by this package make it worth considering. The hardware aspects of the project are well-documented, and the GitHub repository for this part of the setup is also thorough. Overall, this paper provides a clear summary of the tools, their uses, setup, and benefits.

I have a few minor questions about the collective set of tools.

First, the GitHub repository for SqueakPoseStudio appears to be missing a testing routine and associated badge, and the package has not been formally released. This means users would need to download the repository to install it, correct? I suggest the authors consider publishing a formal release of the package, making it installable via pip, and including a basic testing routine to clearly display the package's status on the repository page. Adding a DOI from Zenodo would also be helpful. A testing routine is especially useful when updates are made, as many users avoid repositories with failing tests.

Second, the installation instructions simply state "Create a virtualenv and install:". This may not be sufficient for many researchers, as most neuroscientists are not experienced Python programmers and require clear guidance on the environment specific to this package. The installation instructions should be expanded to provide more detailed guidance and encourage more users. It would also be helpful to verify that the setups work across Windows, Mac, and Linux.

Third, the package defaults to UMAP for non-linear dimensionality reduction, which has some known issues. Can the package be modified to allow for alternative mapping methods, such as PaCMAP, PyDiffMap, or the more comprehensive topometry package?

Finally, what specific GPUs have been tested with the package, and are there any limitations based on the age of the video card or the available libraries for the deep learning component of the package?

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 this manuscript, the role of the insulin receptor and the insulin growth factor receptor was investigated in podocytes. Mice, where both receptors were deleted, developed glomerular dysfunction and developed proteinuria and glomerulrosclerosis over several months. Because of concerns about incomplete KO, the authors generated and studied podocyte cell lines where both receptors were deleted. Loss of both receptors was highly deleterious with greater than 50% cell death. To elucidate the mechanism of cell death, the authors performed global proteomics and found that spliceosome proteins were downregulated. They confirmed this directly by using long-read sequencing. These results suggest a novel role for insulin and IGF1R signaling in RNA splicing in podocytes.

This is primarily a descriptive study and no technical concerns are raised. The mechanism of how insulin and IGF1 signaling regulates splicing is not directly addressed but implicates potentially the phosphorylation downstream of these receptors. In the revised manuscript, it is shown that the mouse KO is incomplete potentially explaining the slow onset of renal insufficiency. Direct measurement of GFR and serial serum creatinines might also enhance our understanding of progression of disease, proteinuria is a strong sign of renal injury. An attempt to rescue the phenotype by overexpression of SF3B4 would also be useful but may be masked by defects in other spliceosome genes. As insulin and IGF are regulators of metabolism, some assessment of metabolic parameters would be an optional add-on.

Significance:

With the GLP1 agonists providing renal protection, there is great interest in understanding the role of insulin and other incretins in kidney cell biology. It is already known that Insulin and IGFR signaling play important roles in other cells of the kidney. So, there is great interest in understanding these pathways in podocytes. The major advance is that these two pathways appear to have a role in RNA metabolism.

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:

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):

[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:

The authors address whether theta/beta ratio /TBR) can be used as a clinical biomarker for ADHD.

Strengths:

The data were acquired independently from 2 separate datasets, and there are sufficient subjects for adequate statistical power. The authors applied up-to-date EEG data preprocessing, state-of-the-art feature extraction, and statistical analyses, using a multiverse approach. By testing and comparing all meaningful approaches, defined a priori in the previous meta-analysis, the author convincingly demonstrates that TBR cannot be used as a clinical biomarker, and previous positive results can be explained by interactions between different factors (alpha peak frequency, aperiodic component, age).

Weaknesses:

There are no apparent issues with data, separate datasets, large sample sizes, and state-of-the-art data analysis.

Reviewer #1 (Public review):

Summary:

GPR52 is an orphan receptor implicated in neuropsychiatric disorders; however, the absence of tools capable of monitoring GPR52 activity in real time has stalled both mechanistic research and ligand discovery. This study addresses this gap by reporting the development of GPR52-1.0, a genetically encoded fluorescent sensor designed to detect activation of GPR52. The sensor was systematically engineered using the established GRAB platform, yielding a construct with micromolar sensitivity and high selectivity in cell culture. The authors largely achieve their stated aims, however the biological relevance of their aims is unclear, as GPR52 is reported to be a constitutively active receptor (PMID: 32076264, PMID: 26384023). GPR52-1.0 is a validated, specific, and sensitive sensor that functions in vitro and ex vivo. The claim that electrically stimulated endogenous GPR52 ligand release occurs in the striatum is supported by the specificity of the GPR52 antagonist block using ex vivo brain slices, however, once again this aim is clouded by evidence that GPR52 is constitutively active. The sensor is presented as a tool for future deorphanization; however, this assumes that the physiological ligand is an agonist, which is unclear based on the evidence that GPR52 is constitutively active. If the authors can explain or adapt their experiments and manuscript in the context of GPR52 constitutive activity, this will be useful work to the community. The impact of this work is likely to be moderate to high within the specialized communities studying orphan GPCRs, neuronal signaling, and neuropsychiatric disease. The GRAB sensor strategy has already generated widely adopted tools for other receptors, and a validated GPR52 sensor would fill a genuine gap. The GRAB technology makes GPR52-1.0 directly applicable to in vivo studies. It is likely that GPR52-1.0 could be replicated for other orphan receptors to facilitate their deorphanization.

Strengths:

(1) Systematic and rigorous sensor optimization and characterization by screening ~800 variants with iterative linker and cpEGFP mutation step. The resulting EC50 values are characterized in HEK293T and cultured neurons.

(2) Testing GPR52-1.0 against a broad panel of neurotransmitters with no detectable off-target activation strengthens confidence in sensor specificity.

(3) The use of a selective antagonist to confirm specificity, both in cell lines and in brain slices, strengthens the conclusions significantly.

(4) Electrically stimulated GPR52-1.0 fluorescence changes in ex vivo striatal slices are blocked by a GPR52 antagonist. This is the most biologically significant result in the manuscript, as GPR52-related diseases can involve the striatum.

Weaknesses:

(1) The work, both experimentally and in its presentation, is not put into the context of what is known about GPR52 pharmacology and signaling. It is reported by multiple groups that GPR52 has high constitutive activity and does not require a ligand for high levels of signaling (PMID: 32076264, PMID: 26384023). The authors should clarify whether GPR52-1.0 senses constitutive activation and whether baseline fluorescence is stable over the timescale of their experiments. The cell and mouse work needs to be reframed and conducted in the context of the high basal activity of the receptor, or the authors need to explain the differences between their study and other studies.

(2) The electrical stimulation used in brain slice experiments is non-specific. This could be activating many cell types and neurotransmitter systems simultaneously. The pharmacological block by the GPR52 antagonist is reassuring, but the identity of the molecules driving the signal remains unknown. It could be that GPR52 is constitutively active, and that the electrical stimulation drives higher expression of GPR52 and thus constitutive signaling. This constitutive signaling can then be inhibited by the GPR52 antagonist. In this scenario, there would be no endogenous GPR52 agonist invoked by electrical stimulation.

(3) The ex vivo brain slice data rely on n=9 slices without reporting the number of animals that the slices come from. Given the importance of this result, more biological replicates and clear reporting of animal numbers would strengthen confidence.

(4) The manuscript does not benchmark GPR52-1.0 against existing approaches (e.g., HTRF, BRET, or calcium mobilization assays) to contextualize its advantages in a drug-discovery or screening workflow.

(5) The paper's title references deorphanization, but the authors have made no attempts toward this deorphanization. No candidate ligand molecules are identified or tested.

Reviewer #1 (Public review):

The manuscript titled," Sleep-Wake Transitions Are Impaired in the AppNL-G-F Mouse Model of Early Onset Alzheimer's Disease", is about a study of sleep/wake phenomena in a knockin mouse strain carrying, "three mutations in the human App gene associated with elevated risk for early onset AD". Traditional, in-depth, characterization of sleep/wake states, EEG parameters and response to sleep loss are employed to provide evidence, "supporting the use of this strain as a model to investigate interventions that mitigate AD burden during early disease stages". The sleep/wake findings of earlier studies (especially, Maezono, et al., 2020, as noted by the authors) were extended by several important, genotype-related observations, including age-related hyperactivity onset that is typically associated with increased arousal, a normal response to loss of sleep and to multiple sleep latency testing, and a stronger AD-like phenotype in females.

The authors conclude that the AppNL-G-F mice demonstrate many of the human AD prodromal symptoms and suggest that this strain may serve as a model for prodromal AD in humans, confirming the earlier results and conclusions of Maezono, et al. Finally, based on state bout frequency and duration analyses, it is suggested that the AppNL-G-F mice may develop disruptions in mechanism(s) involved in state transition.

The study appears to have been, technically, rigorously conducted with high quality, in depth traditional assessment of both state and EEG characteristics with the concordant addition of activity and temperature.

The major strengths of this study derive from observations that the AppNL-G-F mice: 1) are more hyperactive in association with decreased transitions between states; 2) maintain a normal response to sleep deprivation and have normal MSLT results; and 3) display a sex specific, "stronger" insomnia-like effect of the knockin in females.

The weaknesses stem from the study's impact being limited due to its being largely confirmatory of the Maezono et al. study with advances of import to a potentially, more focused field. Further, the authors conclude that AppNL-G-F mice have disrupted mechanism(s) responsible for state transition, however these were not directly examined. The rationale for this conclusion is stated by the authors as based on the observations that bouts of both W and NREM tend to be longer in duration and decreased in frequency in AppNL-G-F mice. Although altered mechanism(s) of state transition (it is not clear what mechanisms are referenced here) cannot be ruled out, other explanations require careful consideration. It is acknowledged in the discussion that increased arousal in association with hyperactivity would be expected to result in increased duration of W bouts during the active phase. This would also predictably result in greater sleep pressure that is typically associated with more consolidated NREM bouts, consistent with the observations of bout duration and frequency. The results from the MSLT tests and lack of increased EEG slow wave activity are problematic to interpret in the context of increased arousal (evidenced by the hyperactivity) since these phenomena, known to be enhanced in association with increased sleep pressure, may be masked by arousal (or by some other effect of the altered genotype). Perhaps, the effect on consolidation is less sensitive. Thus, understanding the underlying mechanism(s) involved is needed for conclusion(s) about sleep pressure.

Overall, this study's findings are valuable but with respect to the claims, incomplete.

Reviewer #1 (Public review):

Freas and Wystrach present a computational and experimental study of ant navigation. The main innovation of the computational model is the insertion of an oscillatory element between the steering signal and the motor control that results in a trajectory whose heading oscillates around a goal direction. Additionally, the model imposes periodic cessations of forward movement and inversely couples rotational speed to forward velocity. As a result the model periodically makes larger reorientations reminiscent of those seen in behaving ants.

The behavioral data consists of two experimental sets: experienced Melophorus bagoti foragers, recorded in 2010 and inexperienced M. bagoti foragers, recorded in 2023-2024 at the same site. The behavioral data is qualitatively compared to the model in Figures 3 through 6. In figures 3-5, all ant sets are grouped together while in Figure 6 they are separated. In Figure 6, the authors should do a careful job of making sure the reader is aware that comparisons are being made between behavioral data sets captured more than a decade apart and of justifying the validity of a quantitative comparison between these sets.

The manuscript also describes Myrmecia ants and makes comparisons between modeled Myrmecia ants and supplemental videos of these ants (Videos 3,4). These videos are not described in the methods. While the captions describe these as ants "homing in an unfamiliar environment," the videos show tethered ants walking on a ball. Without more information and absent any analysis, it is difficult for me to understand how these videos support granular points in the text about coupling between rotation and forward velocities.

Strengths:

The manuscript's main thesis, that an oscillatory element interspersed between the control signal and the motor unit can reproduce aspects of ant navigation, appears supportable.

Weaknesses:

Qualitative agreement between aspects of a model and aspects of a behavioral measurement do not prove the correctness of a model. In the section (802), "An ancestral design? Striking parallels with crawling Drosophila larvae," the authors argue that behavioral data in larvae support their model, despite the larva's lack of a (known) central complex. C. elegans navigation can also be segmented into longer runs and shorter exploratory behaviors (Chen 2025), comparable to the runs and scans described here. C elegans definitively does not have a central complex. In general, multiple internal mechanisms are capable of producing the same macroscopic behavioral outcome. This fact limits the ability of behavioral data to confirm the details of a particular model; it does not imply that observation of similar behaviors in multiple species shows that a particular model is correct or generalizable.

Here the ability of the behavioral data to confirm or constrain the model is further limited by the qualitative nature of the comparisons. Some of the comparisons are trivial (e.g. Figure 5E-F: any first order process will produce a Poisson distribution, and in the model a Poisson process was explicitly coded in with parameters chosen (1070) to match the behavioral data). Finally, the number of adjustable parameters (13) is comparable to the number of comparisons made; it is unclear that the model could not be adjusted to fit any set of behavioral measurements.

While the introduction is improved, there is still room to eliminate confusion as to what aspects of the model reflect hypothesized rather than measured neural circuits. For instance, if there is data showing LAL oscillations in insects, the authors should cite it and call it out clearly. Alternately they should say that the oscillator is hypothesized based on measured bistability. They should also clarify whether they are discussing neural oscillations or motor oscillations and whether these oscillations are measured, modeled, or hypothesized.

As one example: Lines 283-284 "This oscillator [referring to the model's intrinsic oscillator described in the previous paragraph], which is widespread in insects (Cheng, 2024; Kanzaki, 2005; Kanzaki and Mishima, 1996), resides in the lateral accessory lobes (LAL)" reads as though it is known that a neural oscillator occupies the LAL. Cheng 2024 is a brief review of behavioral oscillation. Kanzaki et al. 2005 describes numerical modeling and simulation with a physical robot. Kanzaki and Mishima, 1996 demonstrates bistability (flip-flopping) in moth descending neurons. None of these show neural oscillations and none of them describe the LAL. The authors should review the paper and be scrupulously careful that the claims made in the text are supported in the cited references. These difficulties were pointed out in a previous round of review; hopefully they can be fully corrected this time.

Kevin S. Chen, Jonathan W. Pillow*, Andrew M. Leifer*, "State-switching navigation strategies in C. elegans are beneficial for chemotaxis," arXiv:2508.00191 31 July 2025.

Reviewer #1 (Public review):

Overview:

This study examines cellular computations in the dendrites of neurons in the medial superior olive (MSO) required for computing sound location based on interaural time differences (ITD). This field had, for many decades, depended on the so-called Jeffress model, which stated that an array of binaural coincidence detector neurons fire only when a given sound lateralization is balanced by a given difference in presynaptic axonal conduction time. The apparent absence of such calibrated axonal delay lines has left the field with little mechanistic handle for the strong ITD computations in MSO. This study suggests that dendritic delay along the dendrites of the bipolar MSO neurons makes a significant contribution to a calibrated delay line.

Strengths:

The authors used a combination of in vitro patch-clamp recordings, morphological analysis of a large dataset, and computational modelling to gain experimental access to dendritic computations. A technical tour-de-force set of distal dendritic patch-clamp recordings allowed an evaluation of this otherwise inaccessible parameter, and detailed modeling based on large datasets revealed the functional consequences. The use of this broad methodological toolbox enabled a detailed study of dendritic integration in MSO neurons and revealed a prominent role for graded variation in dendrite structure in shaping the coincidence detection in MSO neurons. In addition, the modeled effects of synaptic inhibition were quite striking and shaped our understanding of ITD coding in the MSO.

Weaknesses:

The paper's organization does not set up the reader very well for the major point to be made about exactly how dendritic asymmetry could bias ITD curves. This point only arises later in the paper after discussion of uncorrelated physiological measures that merely hint that what is important is "larger morphological and electrotonic structure". The paper could also benefit from a more complete description of the methodology. As an example, bridge balance goes unmentioned, and series resistance is hardly mentioned, even though both could distort the measurements of simulated EPSP amplitudes made through tiny electrodes used for dendrite recording.

Reviewer #1 (Public review):

[Editors' note: this version has been assessed by the Reviewing Editor without further input from the original reviewers. The previous concerns have been addressed.]

The central pair apparatus of motile cilia consists of two singlet microtubules, termed C1 and C2, each of which is associated with a set of projections, referred to as the C1 and C2 projections. Each projection comprises multiple distinct structural domains, designated a, b, c, and so on. Biochemical studies combined with genetic analyses in Chlamydomonas identified three proteins as the major components of the C2a projection, and subsequent cryo-EM studies confirmed these findings.

In this paper, the authors aim to study the homologues of these three proteins-CCDC108/CFAP65, CFAP70, and MYCBPAP/CFAP147-using knockout mouse models. Biochemical and cell biological analyses demonstrate that, as in Chlamydomonas, these proteins are components of the C2 projection and form a complex that depends on the presence of each other. In addition, the authors use affinity purification to identify two previously uncharacterized proteins and show that they are central pair apparatus proteins that associate with the aforementioned complex. Knockout mice lacking any of the three core proteins exhibit phenotypes consistent with primary ciliary dyskinesia (PCD).

Overall, the manuscript is clearly written, and the data are convincing and support the authors' conclusions. However, given the previous findings in Chlamydomonas, this work provides limited conceptual advances to the field. Nonetheless, it represents a useful and well-documented resource for understanding the conserved organization of the central pair apparatus in motile cilia. It will be of interest to cell and developmental biologists, biochemists, and clinicians studying and treating human ciliopathies.

Reviewer #1 (Public review):

In this work, Gaurav et al. present an extensive study of phase-separated condensates formed by the foci-forming region (FFR) of the MUT-16 protein. The authors first report in vitro experiments showing that these condensates exhibit upper critical solution temperature (UCST) behavior. They then provide a detailed analysis based on atomistic simulations of MUT-16 FFR condensates, identifying key interactions responsible for LLPS, including salt bridges, cation-π interactions, and the role of Na⁺ ions.

Overall, the manuscript is well written. However, there are several concerns that should be addressed.

Major Concerns:

(1) I have several questions regarding the system preparation that require clarification. The authors state that "65 copies of the coarse-grained MUT-16 FFR were embedded in a slab-shaped simulation," but it is not clear how this initial configuration was generated. Were the molecules randomly distributed in the simulation box, or were they initially arranged in a preformed condensate? Alternatively, were they randomly inserted and allowed to self-assemble into a condensate during NpT simulations?

In Figure 1, the atomistic snapshot appears to show a well-defined condensate at the center of the simulation box. It would be important to clarify how this configuration was obtained: Was it generated from coarse-grained simulations starting from random initial conditions? Or was a preassembled condensate used as input?

Related to this, how do the authors ensure that the simulations are equilibrated? While 20 μs appears to be a reasonably long simulation time for coarse-grained simulations, it would be useful to demonstrate equilibration explicitly. For example, the authors could plot the center-of-mass positions (in the long axis of the simulation box) of individual proteins over time to show that all molecules reach a steady state and remain within the condensate without systematic drift.

(2) The authors experimentally observe UCST behavior for these condensates. Do the coarse-grained or atomistic simulations reproduce this behavior?

While atomistic simulations may be too computationally demanding to systematically explore temperature dependence, coarse-grained simulations could be used to test whether condensates are stable at lower temperatures and dissolve at higher temperatures. Such an analysis would provide valuable support for the experimental observations.

(3) Regarding the analysis of ions, several points could be clarified and extended:

a) It would be helpful to report the total number of ions and quantify how many are located inside vs. outside the condensate. While qualitative trends can be inferred from density profiles, quantitative analysis would strengthen the conclusions.

b) It would also be interesting to analyze the number of contact ion pairs (e.g., Na⁺-Cl⁻ pairs), as described in J. Chem. Phys. 156, 044505 (2022). It is known that some ion models tend to overestimate ion pairing and underestimate solubility (e.g., J. Chem. Phys. 153, 010903 (2020)).

c) In this context, the use of scaled-charge models has been shown to improve the description of ionic solutions and biomolecular systems (e.g., J. Phys. Chem. Lett. 2019, 10, 23, 7531-7536). I would suggest that, at least for one trajectory, the authors perform a test simulation using scaled charges (e.g., scaling by ~0.8) to evaluate whether ion distributions and protein-ion interactions are significantly affected.

d) Finally, while the selected water model is known to be accurate, it would be useful to assess its performance for concentrated salt solutions. For example, the authors could estimate the density of a 6 m salt solution and compare it with experimental data or validated models (e.g., J. Chem. Phys. 151, 134504 (2019)). This would help clarify to what extent the conclusions depend on the chosen force field.

Minor Concerns

(1) In the Introduction, it would be helpful to elaborate further on the possible driving forces of LLPS in this region. Are there prior hypotheses or evidence pointing to specific interactions (e.g., cation-π, π-π, electrostatic interactions)? While this work addresses these questions, a brief discussion of previous experimental or theoretical insights would provide useful context.

(2) On page 18, the authors state:<br /> "MUT-16 FFR satisfies the length (172 residues), aromatic content (20.35%), and Arg enrichment (85.71%) criteria. Its charge content (10.47%) and charge balance (38.89% positive charge fraction) are slightly below the nominal thresholds."<br /> It would be very helpful to include a schematic representation of the protein sequence highlighting these features (aromatic residues, charge distribution, etc.) in the corresponding figure, to provide a more intuitive understanding.

(3) A question regarding ion hydration: What is the coordination environment of the ions that bridge proteins? Are they still hydrated by water molecules, or does the reduced water content inside the condensate significantly affect their solvation?<br /> Typically, Na⁺ and Cl⁻ ions have coordination numbers around 5-6 in aqueous solution. Do protein interactions and reduced solvent conditions within the condensate alter this coordination? A brief analysis or discussion would be valuable.

Reviewer #1 (Public review):

Summary:

The authors investigated the relationship between physical activity (PA) and both structural (MRI) and cognitive brain health in the LIFE-Adult Study, with total baseline recruitment of 2576. Hippocampal volume, an MRI-derived BrainAGE marker, and scores from the Trail Making Test were used as outcomes, with the majority of participants measured at baseline and subsets also measured in a follow up session. The key findings were a lack of direct association between PA and outcomes, but longitudinal evidence for a higher BrainAge at baseline leading to lower physical capacity at follow-up. This supports a reverse-causation hypothesis in contrast to prevailing understanding of the positive effects of physical activity on brain health.

Strengths:

The Life-Adult study is a rich and carefully acquired dataset, with multiple follow-up time points. The statistical analyses were conducted carefully with appropriate control for confounds and multiple testing. The study design enables the important assessment for reverse causality. The authors are scrupulous in their consideration of a number of factors that could potentially bias their results, performing an age-stratified analysis, and emphasising discrepancies in PA measurements (specifically and age-reporting bias) across the dataset and other limitations.

Weaknesses:

This is an observational study with inconsistent measures of physical activity. Previous studies have used physical activity interventions, and might be more strongly weighted when considering evidence for these effects (specific confounders involved in interventions notwithstanding) .

The model identifying potential reverse causality is relatively limited - it seems possible/likely that brainAge could reflect more general health status, which would expand the potential range of factors underlying this observation. The authors comment on these possibilities.

The important quantitative actigraphy subset is small (n=227) as are the longitudinal subsets. Along with the discrepancy of physical activity/capacity at baseline and follow-up, and other complexities of the dataset, it is difficult to make firm conclusions. The authors point out that the actigraphy subset was quite inactive, and discuss this as a limitation.