Reviewer #2 (Public review):

Summary:

This is an extensive study using phylogenetic comparison across multiple plasmodium species to gain new insights in relation to their evolutionary pathways and the potential function of pir. In addition to establishing a framework to identify related orthologues across species as well as expanding paralogues families within a species, the work also focuses on understanding loss and gain of different PIRs and how this indicates a relative lack of functional constraints and essentiality for most members of the gene family.

The authors provide evidence that at least pirC has a conserved function and plays an important role in parasite growth in multiple species.

While this study represents a significant effort and does provide interesting new insights that would help our understanding of this complex gene family in the future, it has a number of limitations.

Strengths:

Extensive and thorough phylogenetic analysis that is supported by some biological validation. Provides an indication that the PIR gene family has limited biological constraints and evolved independently across different species, leading to rapid expansion and deletion of orthologous groups. Identified pirC as a functional and important member of the family that is conserved across the species.

Weaknesses:

The phylogenetic tree is based on a truncated sequence that focuses on the more conserved parts of the pir sequence. This could potentially lead to missing the key functional drivers of evolution. The biological validation of the role of pirC has some inconsistencies that need to be addressed.

Reviewer #3 (Public review):

This paper aims to classify, from an evolutionary perspective, the multigene family PIR found in malaria parasites infecting rodents and Old World monkeys, and to link this classification to functional diversification. The authors also hypothesize that PIR members conserved across species play important roles in parasite survival, and seek to clarify their functions.

To achieve these aims, the authors comprehensively analyze the evolution of PIR genes using genomic and transcriptomic information from many malaria parasite species. They focus on PIRC1, a member conserved across species, and attempt to clarify its function in rodent and simian malaria parasites by examining the phenotypes of parasites in which the corresponding genetic locus has been disrupted. They also attempt to determine its localization using PIRC1 tagged with an epitope sequence. However, although the locus-disrupted parasites appear to show an approximately 50% reduction in growth rate, this effect seems to be overestimated. Another weakness is that the cause of the reduced growth rate has not been clarified. The localization analysis also remains insufficiently conclusive.

Therefore, I consider that the first half of the paper, consisting of the bioinformatics analyses, achieves the objective of comprehensively summarizing PIR and may become a reference paper for discussing the evolution and function of the PIR gene family. On the other hand, regarding the function of PIRC1, no clear conclusion can be drawn from the results presented, and several additional experiments are necessary.

My major comments are as follows.

(1) The claim that the failure of eight disruption attempts indicates that pirC1 is essential is too strong.

Lines 319-321: The authors argue that a total of eight failed attempts to disrupt the pirC1 locus using two different construct designs suggest that pirC1 is essential in P. berghei. However, the failure of these attempts could also reflect technical issues with the construct design itself, such as the length of the homologous regions used for recombination, which are approximately 650 bp. Therefore, it is an overstatement to conclude that "pirC1 is essential for P. berghei blood-stage growth." Given that parasites with disruption of the corresponding locus could be obtained in both P. chabaudi and P. knowlesi, a more appropriate statement would be that "pirC1 is important for P. berghei blood-stage growth."

(2) The data on the mCherry-expressing P. berghei line shown in Supplementary Figure 11 are insufficient.

(a) Panel C: Southern blot analysis<br /> To conclusively identify the lower band in panel C as chromosome 1, additional probes specific to genes located on chromosomes 1 and 2 would be required. In addition, a parental parasite control should also be included. The Southern blot image of the parental parasite should show only a single band at the higher position, with no band at the lower position. Probes specific to chromosomes 1 and 2 would help demonstrate that the lower band corresponds to chromosome 1, rather than chromosome 2.

To this end, the authors could describe the result as follows:<br /> "In the parental parasite, only a single band corresponding to chromosome 7 was detected, indicating that the smaller chromosome was genetically modified. The size of the lower band detected with the dhfr probe was identical to that of the band detected with the control chromosome 1 probe, but distinct from that detected with the chromosome 2 probe, indicating that chromosome 1 was modified."

That said, this chromosome-level Southern blot analysis is not sufficient to demonstrate that the target PBANKA_0100500 locus was specifically modified. The authors should provide more direct evidence showing that the PBANKA_0100500 locus, rather than another genomic locus, was modified. For example, Southern blot analysis after restriction enzyme digestion would provide more definitive evidence. Diagnostic PCR may also provide more specific evidence.

(b) Panel D: Flow cytometry analysis

To allow a more accurate interpretation of the percentage of mCherry-positive cells, flow cytometry data for the parental parasite line should also be presented.

(3) There are unclear points in the PCR results shown in Supplementary Figure 12.

Supplementary Figure 12: In panel B, a PCR product should also be amplified from dPCHAS_0101200 using the P1-P3 primer pair. Why is this band absent? The authors should provide the uncropped electrophoresis image so that the larger band can be seen. In addition, if labels 1 and 2 indicate independent clones, this should be stated in the figure legend.

(4) The growth rates of P. chabaudi and P. knowlesi parasites with disruption of the PIRC1 gene locus should be quantitatively analyzed.

The growth rates of P. chabaudi and P. knowlesi are described only qualitatively, but they should be evaluated quantitatively. In Figure 4A, the parasitemia of wild-type P. chabaudi increases from approximately 6.1% on day 6 to approximately 15.6% on day 8, corresponding to a 3.8-fold increase. However, because parasite growth may already be affected by immune-mediated suppression at this stage, this value should be regarded as a minimum estimate. In contrast, the mutant increases from approximately 3.2% on day 8 to approximately 6.8% on day 10, corresponding to a 2.1-fold increase. Based on these values, the daily growth rate of the mutant appears to be reduced to at least approximately 56% of that of the wild type. Similarly, from the growth curve of P. knowlesi in Fig. 5A, the DMSO-treated group appears to increase approximately two-fold per day, whereas the rapamycin-treated group increases only approximately one-fold per day. Thus, P. knowlesi also appears to show an approximately 50% reduction in growth rate. Taken together, both P. chabaudi and P. knowlesi appear to reproducibly show an approximately 50% reduction in growth capacity. A reduction of this magnitude is difficult to describe as a "severe growth defect"; a more appropriate wording would be simply that the parasites "showed a growth defect." In addition, the terms "a severe growth defect" and "essential" appear to be overstated throughout the manuscript, and the wording should be toned down. Finally, I recommend presenting Figure 4A and Figure 5A on a logarithmic scale so that the trend in growth rates can be more intuitively appreciated from the graphs.

(5) The evidence that disruption of the PIRC1 gene locus in P. knowlesi does not affect erythrocyte invasion is weak.

The authors describe that "the developmental cycle of the parasites lacking PIRCl is slightly longer than that of parasites that produce PIRCl (line 383-384)," and appear to support this interpretation with data showing that "mutant parasites are significantly smaller than wild-type parasites (line 414)" and that "the DNA content in ML10-arrested parasites lacking PIRCl is lower than that of DMSO-treated parasites (line 417-418)" at 24 hours after invasion. However, a slightly longer developmental cycle alone does not seem sufficient to explain a 50% growth reduction.

I think the erythrocyte invasion capacity has not been quantitatively evaluated, and therefore, the evidence supporting the conclusion that the phenotype of P. knowlesi parasites with disruption of the PIRC1 gene locus is unrelated to erythrocyte invasion is weak. The authors should assess invasion efficiency using purified merozoites. For P. chabaudi, it should also be possible to apply an in vitro or in vivo erythrocyte invasion assay similar to that used for other rodent malaria parasites, and this should be evaluated as well.

(6) The authors should examine whether disruption of the PIRC1 gene locus results in a phenotype characterized by a reduced number of merozoites.

Alternatively, the reduced DNA content in ML10-arrested parasites lacking PIRC1 (lines 416-417) could suggest that the number of merozoites formed per schizont may be reduced. To clarify this point, the authors should assess whether the number of merozoites per schizont is altered in P. knowlesi (and P. chabaudi parasites lacking PIRC1).

(7) The authors propose the possibility that PIRC1 expressed in merozoites is released after invasion; however, the evidence that PIRC1 localizes to intracellular organelles is weak.

Line 333: "a peripheral pattern around the parasite" is indicative of parasite plasma membrane, PV, or PVM. ", indicative of a parasitophorous vacuole (PV) or parasitophorous vacuole membrane (PVM) location" should be amended to ", indicative of parasite plasma membrane, a parasitophorous vacuole (PV) or parasitophorous vacuole membrane (PVM) location". In the Figure S14 image, red signals are uniformly detected from the merozoites formed in the schizont stage parasite (not really microorganelle patterns), but not from the PVM surrounding the schizont, suggesting parasite plasma membrane localization, not PVM. I agree that the signal is detected from the compartments extending into the iRBC cytosol, which may be difficult to explain if it is located on the parasite plasma membrane, but how frequently were such images seen?

Figure 4D. In the images of liver-stage schizonts, AMA1 does not appear to localize to the micronemes in mature merozoites, suggesting this image is an immature schizont. Although PIRC1 appears to be expressed in liver-stage schizonts, it is difficult to clearly determine whether it localizes to intracellular organelles or to the parasite plasma membrane.

To clarify the above points, the authors should examine whether PIRC1 is detected in intracellular organelles or around the merozoites by analyzing its localization in purified merozoites.

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):

Summary:

The authors set out to develop and validate the Crunchometer, a low-cost, open-source acoustic system designed to overcome the limitations of existing methods for studying feeding behavior in rodents. Their goal was to provide a tool that could precisely capture the microstructure of solid food intake, something often overlooked in favor of liquid-based assays, while being affordable, scalable, and compatible with neural recording techniques. By doing so, they aimed to enable detailed analysis of how physiological states, drugs, and specific neural circuits shape naturalistic feeding behaviors.

Strengths:

(1) Introduces a low-cost, open-source acoustic tool for measuring solid food intake, filling a critical gap left by expensive and proprietary systems.

(2) Makes the method easily adoptable across labs with detailed setup instructions and shared benchmark datasets.

(3) Provides high temporal precision for detecting bite events compared to human observers.

(4) Successfully distinguishes feeding microstructure (bites, bouts, IBIs, gnawing vs. consumption) with greater objectivity than manual annotation.

(5) Demonstrates compatibility with electrophysiology and calcium imaging, enabling fine-scale alignment of neural activity with feeding behavior.

(6) Effectively discriminates between fed vs. fasted states, validating physiological sensitivity.

(7) Captures pharmacological effects of semaglutide, although this is really just reduced feeding and associated readouts (bouts, latency, etc.)

(8) Has potential to distinguish consummatory vs. non-consummatory behaviors (e.g., food spillage, gnawing), however the current SVM model struggles to separate biting from gnawing due to similar acoustic profiles and manual validation is still required.

(9) Provides potential for closed-loop experiments

Weaknesses:

(1) Some neuroscience findings (calcium imaging of GABAergic vs. glutamatergic neurons) are based on small pilot samples (n=2 mice per condition), limiting generalizability.

(2) Chemogenetic and pharmacological experiments used small cohorts, raising statistical power concerns.

(3) Correlation with actual food intake is modest and sometimes less accurate than human observers

(4) Sensitive to hoarding behavior, which can reduce detection accuracy and requires manual correction for misclassifications (e.g., tail movements, non-food noises). However, these limitations are discussed and not ignored.

Comments on revised version.

The authors have addressed all my comments and have put forth a creative, accurate approach to assessing food intake in rodents.

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 #2 (Public review):

Summary:

In this manuscript, Gazal et al., describe the presence of unique gaps and patches of BetaII-spectrin in medial sections of long human motor neuron axons. BII-spectrin, along with Alpha-spectrin forms horizontal linkers between 180nm spaced F-actin rings in axons. These F-actin rings along with the spectrin linkers form membrane periodic structures (MPS) which are critical for maintenance of the integrity, size and function of axons. The primary goal of the authors was to address if long motor axons, particularly those carrying familial mutations associated with the neurodegenerative disorder ALS, show defects in gaps and patches of BetaII-spectrin ultimately leading to degradation of these neurons.

Strengths:

The experiments are well designed and the authors have used the right methods and cutting-edge techniques to address the questions in this manuscript. The use of human motor neurons and the use of motor neurons with different familial ALS mutations is a strength. The use of isogenic controls is a positive. The induction of gaps and patches by the kinase inhibitor staurosporine and their rescue by Latrunculin A is novel and well executed. The use of biochemical assays to explore the role of calpains is appropriate and well designed. The use of STED imaging to define the periodicity of MPS in the gaps and patches of spectrin is a strength.

Weaknesses:

Primary weakness is the lack of rigorous evaluation to validate the proposed model of spectrin capture from the gaps into adjacent patches by the use of photobleaching and live-imaging. Another point is the lack of investigation into how gaps and patches change in axons carrying the familial ALS mutations as they age, since 2 weeks is not a timepoint when neurodegeneration is expected to start.

Comment on revised version.

The authors have given a point-by-point response to all the reviewer's concerns. They have also addressed concerns which I raised adequately. I have no further concerns.

Reviewer #3 (Public review):

Summary:

Gazal et al present convincing evidence supporting a new model of MPS formation where a gap-and-patch MPS pattern coalesces laterally to give rise to a lattice covering the entire axon shaft.

Strengths:

(1) This is a very interesting study that supports a change in paradigm in the model of MPS lattice formation.

(2) Knowledge on MPS organization is mainly derived from studies using rat hippocampal neurons. In the current manuscript, Gazal et al use human IPS-derived motor neurons, a highly relevant neuron type to further the current knowledge on MPS biology.

(3) The quality of the images provided, specifically of those involving super-resolution is of high standards, supporting adequately the conclusions of the authors.

Weaknesses:

(1) The main concern raised by the manuscript is the assumption that staudosporine-induced gap and patch formation recapitulates the physiological assembly of gaps and patches of betaII-spectrin.

(2) One technical challenge that limits a more compelling support of the new model of MPS formation, is that fixed neurons are imaged, which precludes the observation of patch coalescence.

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 #2 (Public review):

Aims:

The authors sought to optimize SHARE-seq, a multimodal single-cell method, to improve the simultaneous profiling of gene expression and chromatin accessibility. Their goal was to enhance barcode design for better sequencing efficiency and cost savings, while improving overall data quality. They then applied their optimized method, easySHARE-seq, to study liver sinusoidal endothelial cells (LSECs) to demonstrate its utility in examining gene regulation and spatial zonation.

Strengths:

The improved barcode design is an advance, increasing the proportion of sequencing reads dedicated to biological information rather than barcode identification. This modification offers practical benefits in terms of sequencing costs and read length, potentially reducing alignment errors. The method also demonstrates improved RNA detection compared to the original SHARE-seq protocol. The biological applications showcase how simultaneous measurement of both modalities enables analyses that would be practically impossible with single-modality approaches, particularly in examining how chromatin states change along developmental or spatial trajectories.

Weaknesses:

There is a notable reduction in chromatin accessibility detection compared to the original SHARE-seq method, likely limiting the use of the method in certain situations.

Overall:

The authors achieve their aim of creating an optimized protocol with improved barcode design and enhanced RNA detection. The method represents a useful advance for specific experimental contexts where the trade-offs are appropriate.

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 #2 (Public review):

Summary:

In this study, authors studied the synchrony between ripple events in Hippocampus, cortical spindles and Locus Coeruleus spiking. The results in this study together with the established literature on the relationship of hippocampal ripples with widespread thalamic and cortical waves, guided authors to propose a role for Locus Coeruleus spiking patterns in memory consolidation. The findings provided here, i.e. correlations between LC spiking activity and Hippocampal ripples, could provide basis for future studies probing the directional flow or the necessity of these correlations in the memory consolidation process. Hence, the paper provides enough scientific advance to highlight the elusive yet important role of Norepinephrine circuitry in the memory processes.

Strengths:

Authors were able to demonstrate correlations of Locus Coeruleus spikes with hippocampal ripples as well as with cortical spindles. Specific strength of the paper is in the demonstration that the spindles that activate with the ripples are comparatively different in their correlations with Locus Coeruleus than those which do not.

Weaknesses:

The claims regarding the roles of these specific interactions were mostly derived from the literature that these processes individually contribute to the memory process, without any evidence of these specific interactions being necessary for memory processes. There are also issues with the description of methods, validation of shuffling procedures and unclear presentation and the interpretation of the findings, which are described in points that follow. I believe addressing these weaknesses might improve and add to the strength of the findings.

Comments on revised version.

The authors addressed all of my major concerns during the revision. As a result, the study now provides convincing evidence as well as improved presentation of results, that makes this manuscript important to the broader field of neuroscience, beyond the specific sub-field.

Reviewer #3 (Public review):

This manuscript examines how locus coeruleus (LC) activity relates to hippocampal ripple events across behavioral states in freely moving rats. Using multi-site electrophysiological recordings, the authors report that LC activity is suppressed prior to ripple events, with the magnitude of suppression depending on ripple subtype. Suppression is stronger during wakefulness than during NREM sleep and least pronounced for ripples coupled to spindles.

The study is technically sound and addresses a timely and important question regarding how LC activity interacts with hippocampal and thalamocortical network events across vigilance states. While the findings are interesting, they remain observational in nature. Following revision, the manuscript has substantially improved in both presentation and interpretation of the results, and most concerns have been addressed satisfactorily. I therefore only have a few minor considerations that the authors may wish to explore further in the current study or in future work, as these directions could provide additional mechanistic insight and would likely be of considerable interest to the field.

The authors demonstrate clearly that tonic LC firing rates preceding ripples differ significantly between wake-associated ripples (highest LC firing), isolated ripples during NREM sleep (lower LC firing), and spindle-coupled ripples (lowest LC firing). They also appropriately note that baseline firing differences will naturally influence the magnitude of LC suppression, which they also observe (highest LC reduction for wake ripples, then isolated ripples and last spindle-coupled ripples). However, this aspect could be explored further, as it may provide additional insight into the regulation of spindle-associated ripple events. Since LC activity appears to decline gradually prior to ripple occurrence (Suppl. Figure 2), it would be interesting to test whether this gradual reduction helps organize the emergence of isolated versus spindle-coupled ripples. For example, isolated ripples may occur during the initial phase of LC decline, whereas spindle-coupled ripples may preferentially emerge when LC activity reaches its lowest levels. Such a relationship could also be consistent with the stronger synchronization observed for spindle-ripple coupling.

Related to this point, it would also be informative to examine whether isolated spindles occur more randomly in time, whereas spindle-associated ripple events appear more temporally clustered. If a single isolated spindle occurs, the associated LC suppression might be more pronounced. In contrast, when multiple spindle-associated ripple events occur in succession, LC activity may already be reduced following the first event, resulting in smaller additional suppression preceding subsequent events. Exploring this possibility could help clarify how LC dynamics shape the temporal emergence of ripple-subtypes

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 #2 (Public review):

Summary:

The authors design a custom Bayesian model to estimate the probabilities of access, use and use given access of insecticide-treated nets in six African countries, providing sub-national estimates and inferring the average duration of ITN use and access. An individual-based model was employed to simulate malaria epidemics and estimate the effectiveness of different ITN distribution strategies. The study finds that the mean probability of use or access did not reach 80% (a universal coverage formerly targeted by WHO) for any of the regions even for biennial campaigns, demonstrates that switching from triennial to biennial distribution campaigns increases population use by 7.9%, and evaluates the impact of employing more efficient ITNs on P. falciparum prevalence.

Strengths:

The authors developed a data-driven model that accounts for data collection imperfections and sources of uncertainty while differentiating between ITN use and access. They developed a methodology to infer the timing of mass campaign from publicly available data instead of assuming fixed dates. The probability of use given access allows determining the regions where ITN distribution is least effective. This work can help better inform future interventions by identifying regions where increasing mass campaign frequency or employing better ITNs are most effective. Finally, in addition to insights on ITN access and use for the six countries analyzed, the paper contributes with a methodological framework that can likely be extended to other countries.

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 #2 (Public review):

The determination of macromolecular structures directly within their native cellular environment is becoming increasingly routine, making standardized data collection strategies essential. In this manuscript, Tuijtel et al. provide a timely and valuable contribution by benchmarking key acquisition parameters and establishing practical guidelines for in situ cryo-electron tomography (cryo-ET). Critically, the authors present a systematic framework for optimizing data collection to achieve the highest attainable resolution.

Using Dictyostelium cells as a model system, the authors generate multiple datasets at a constant total dose while varying the tilt increment. They demonstrate that tilt-series acquired with finer increments (1-3 degrees) yield superior alignment accuracy and improved template-matching performance, resulting in higher-quality reconstructions than those collected with coarser increments (5 degrees or above). Furthermore, the authors show that for subtomogram averaging, a 3-degree tilt increment outperforms all other conditions tested, particularly after per-particle refinement as implemented in M.

Overall, the manuscript is clearly written, and the conclusions are well supported by the data presented. I have no major concerns. There are some minor points that the authors should address, including:

(1) The phrase "electron optical density distribution" (line 31, Introduction) should be revised to "electrostatic potential" or "Coulomb potential distribution," which more accurately reflects what is measured in cryo-EM/ET.

(2) The authors state that the maximum tolerable electron dose is approximately 100-150 e⁻/Ų (line 34, Introduction). This is an oversimplification, as bacterial specimens, for example, have been shown to tolerate doses of 200 e⁻/Ų or higher (see Breigel et al., PNAS, 2009; https://www.pnas.org/doi/10.1073/pnas.0905181106#T1). The statement should be revised to reflect this variability.

(3) Lines 56-57: The authors do not cite their own prior work benchmarking tilt-series acquisition strategies on in vitro samples. This earlier study provides important context and should be referenced and briefly discussed.

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 #2 (Public review):

This study presents an important analysis of how interactions between muscles can serve as biomarkers to quantify therapeutic responses in post-stroke patients. To do so, the authors employ an information-theoretical metric (co-information) to define muscle networks and perform cluster analysis.

Comments on revised version.

Thank the authors for the carefully revised article. I have no further 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 #2 (Public review):

Summary:

In this article, Laaker et al described diverse populations of macrophages and dendritic cells found in and around the cribriform plate in a context of a neuroinflammation caused by an autoimmune disease (EAE). The authors utilize elegant histochemical staining and a nifty approach to sort doublets to interrogate cells that are in contact with one another, presumably in vivo. Notably, they uncover a population of CD11c+CD11b+ cells interacting with M2 macrophages and PDPN+ fibroblasts and lymphatics. These cells are heterogenous but some of these DCs express PD-1 and transcriptional profiling suggests they may have immunosuppressive behavior. Altogether, this article explains well the complexity of cell populations found around the cribriform plate during inflammation and are suggestive of different interactions that trigger these different phenotypes from immune cells.

Strengths:

Beautiful images of a unique CNS: peripheral interface that support a novel scRNA approach to understanding how different cell populations engage in functional interactions in vivo.

Weaknesses:

It is unclear how the sorted populations reflect in vivo interactions, or a propensity to form aggregates during ex vivo processing. Future work will be needed to address which poplanin expressing cells are most relevant.

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 #2 (Public review):

Summary:

This highly original and well-designed study provides insight into how honeybee picorna-like viruses, Deformed wing virus ( DWV) and Sacbrood virus (SBV), affect flight performance, and reveals the role of the octopamine (OA) pathway in virus-honeybee interactions. The authors used a flight mill to quantify the flight performance of bees with different levels of DWV and SBV. Bees were treated with OA and/or epinastine (EP) - an OA receptor antagonist; the study also quantified virus loads and expression of two key genes involved in OA biosynthesis.

The results showed that reduced flight performance associated with high DWV levels could be alleviated by OA administration. In contrast, increased levels of SBV had the opposite effect, leading to enhanced flight performance. This suggests distinct physiological responses to DWV and SBV infections. Administration of EP had led to a reduction of flight performance in SBV-infected bees, indicating the involvement of the OA pathway.

The authors also quantified levels of mRNAs of enzymes involved in OA synthesis, tyrosine decarboxylase (TDC) and tyramine beta-hydroxylase (TbH), and concluded that DWV induced expression of TbH, while SBV upregulated expression of TDC. Furthermore, the study identified upregulated and downregulated genes in response to SBV, DWV and DWV in combination with OA.

Strengths:

The study reported opposing effects of infections of related viruses, SBV and DWV, on honeybee flight performance, and identified the central role of the octopamine (OA) signaling pathway in the effect of viruses on honeybee flights.

These findings were achieved by using a combination of approaches, including experimental measurement of flight distance, virus infections, and introduction of OA and EP. Experimental work with honeybees is technically challenging and requires specialized expertise, which makes the results produced in this study more valuable.

DWV and SBV are among the most important honeybee pathogens affecting honeybee health and threatening the pollination service. Therefore, an understanding of the mechanisms underlying DWV and SBV pathogenesis has the potential to develop novel approaches to mitigate the negative impact of these viruses.

Weaknesses:

No weaknesses were identified by this reviewer.

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 #2 (Public review):

Summary:

In this study, the authors report the hitherto unobserved types of HTT assemblies observed in human fibroblasts and iPCS-derived neurons in 2D and 3D culture, applying a state-of-the-art confocal microscopy imaging with near 64 nm resolution to decode their structures. They further demonstrate that these assemblies closely contact with various types of Golgi ribbons, stacks, vesicles, and Golgi-derived clathrin-coated vesicles but not mitochondria. They also used single-cell RNAseq to show some interesting findings that supported the suggested defects in Golgi-related function, specifically by downregulation of various cellular processes related to Golgi and vesicle transport functions. They also replicate mHTT nuclear accumulations in striatal neurons, which is considered to be a hallmark of HD pathology, by using long-term neuronal culture. Furthermore, the assemblies showed differential responses to glucose starvation and to autophagy enhancer treatment by onjisaponin F for mutant HTT assemblies, but not for the healthy siblings, in fibroblasts and neurons. Onjisaponin F treatment did not reverse nuclear deposition. They also showed that ASO shortens these polyQ assemblies but does not change neuronal firings that are detected by HD-MEA. Notably, they also used human brain samples to show the existence of polyQ assemblies in fetal and child brain samples. This part is impressive.

Overall, this work reports a novel polyQ assembly, which was previously reported as a pathogenic factor, has not been reported before for HTT, is related to Golgi activities and vesicular transport, and is dismantled in HD patient cells. The intensive immunostaining and super-resolution scanning are impressive and definitely strengthened by the impact of the findings. The scRNAseq data adds another layer to the observed Golgi impairments and their suggested relationship to Golgi function. The drug testing for polyQ assemblies, especially polyQ assemblies in HD cells, is preliminary. However, the data in this study are enough to support the existence of polyQ assemblies in human cells and their specific relationships with the Golgi apparatus.

Strengths:

In this study, the authors used the cells from a large HD family and fetal/child brain samples to decode the structure of endogenous polyQ assemblies. This part is impressive. The intensive staining and super-resolution scanning are amazing. The spatial relationships of polyQ assemblies with the Golgi apparatus and mitochondria are well illustrated.

Weaknesses:

Although they used healthy sibling cells as a control, an isogenic control (genetic correction of the mutant gene) is lacking. Based on the Golgipathy of mHTT, they did a drug screening. The drug testing for polyQ assemblies is preliminary. More rigorous validation, such as scRNA seq and proteomic analysis, etc., is necessary to reach a systemic conclusion.

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 #3 (Public review):

Summary:

Due to the low SNR of cryo-EM micrographs necessitated by radiation damage, determining the structure of proteins smaller than 50 kDa is exceedingly challenging, such that only a handful have been solved to date. This work aims to improve the reconstruction of small proteins in single-particle cryo-EM by using high-resolution 2D template matching, an algorithm previously used to locate and align macromolecules in situ, to align and reconstruct small proteins. This approach uses an existing macromolecular structure, either experimentally determined or predicted by AlphaFold, to simulate a noise-free 3D reference and generates whitened projections, crucially including high-spatial-frequency information, to align particles by the orientation with maximal cross-correlation. They demonstrate the success of this approach by generating a 3D reconstruction from an existing dataset of a 41.3 kDa protein kinase that had previously evaded attempts at high-resolution structure determination. To alleviate concerns that this is purely from template bias, they demonstrate clear density at two regions that were not present in the template: 6 residues in an alpha helix and an ATP in the ligand binding pocket. The latter is particularly important for its implications in determining structures of ligand-bound proteins for drug discovery. They also produce a composite omit map from 36 partial-deletion reconstructions spanning the entire protein, demonstrating a reconstruction can be obtained without template bias. Additionally, the authors provide an update to the classic calculation in Henderson 1995 to predict the minimum molecular mass of a protein that can be solved by single-particle cryo-EM.

Strengths:

I am in no doubt that this technique can be used to gain valuable insights into the structures of small proteins, and this is an important advancement for the field. It is complementary to single-particle cryo-EM and provides an extra tool for the experimentalist that may work better in certain cases. For cases where only a small region of the structure is of interest, such as in drug screening, this method provides a simple workflow to screen many structures.

The claim that using high-spatial frequency information is essential for aligning small proteins is a valuable insight. A recent pre-print published at a similar time to this manuscript used high-resolution information in standard ab-initio reconstruction to generate a high-resolution reconstruction from the same dataset, supporting the claims made in the manuscript.

The theoretical section outlined in the appendix is also theoretically sound. It uses the same logic as Henderson, but applies more up-to-date knowledge, such as incorporating dose-weighting and altering the cross-correlation based noise estimation. This update is valuable for understanding factors preventing us from reaching the theoretical limit.

Weaknesses:

The applicability of this technique to more than a single target was not demonstrated. Nor was it compared to more recent strategies for processing SPA data from small molecules, such as Blush regularization or HR-HAIR. Additionally, although the authors have demonstrated convincingly that their method selects a stack of high-quality particles, it is less clear whether it performs better than RELION when using the same stack of particles, particularly in the ATP binding pocket. This places this method as a complementary technique, and whether it outperforms those methods for a wide variety of molecules is yet to be determined. The method presented here also introduces template bias, so only parts of the reconstruction not in the initial template are free of template bias. Producing a full reconstruction through a composite omit map is computationally expensive, meaning that unless this method outperforms modern SPA methods, its major use case will be ligand binding studies instead of 3D reconstructions.

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 #2 (Public review):

Summary:

Singh et al. apply MOA-seq to map transcription factor occupancy genome-wide in HUVECs across a hypoxia time course. The study provides a well-validated, high-resolution view of cistrome dynamics and identifies both HIF1A-associated and independent regulatory programs.

Major Comments:

Methodological validation is strong. MOA-seq's ability to map protein-bound DNA at near-nucleotide resolution without factor-specific antibodies is a genuine advance, and the cross-validation against independent ChIP-seq and ENCODE datasets is convincing. As noted, future work with additional biological replicates could further strengthen confidence in the smaller kinetic clusters.

Imaging-based validation would strengthen the key biological claims. The kinetic clustering and pathway enrichments are computationally inferred. Orthogonal approaches, for example, live-cell fluorescence imaging of HIF1A nuclear translocation to confirm the proposed temporal binding waves, would provide independent experimental support.

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 #2 (Public review):

Summary:

This is an important study of the molecular mechanisms of GABA vs. glutamate release by coreleasing neurons that project from the EPN to LHB. The conclusion is that separate pools of vesicles release each transmitter and use different molecular machinery to do so. This is in contrast to and in disagreement with functional studies of the same synapse that conclude that the transmitters are copackaged.

As detailed below, the study has a major flaw. It uses an incorrect Cre line, which is also expressed in a purely glutamatergic population in the EPN that also projects to the LHB. In addition, there is little quantification and validation of important tools and no histological confirmation of the sites of expression of viral-encoded proteins.

Strengths:

The strength of the study is in the importance of the question addressed and in the ambition of the tools used.

Weaknesses:

(1) The study uses Vglut2-IRES-Cre mouse to gain control over EPN to LHB projections. However, as has been shown by several groups, this line is not exclusive to the EPN co-releasing population. It is also expressed in glutamatergic EPN PV neurons that project solely to the EPN. Therefore, all of the studies here are contaminated with analysis of a purely glutamatergic Vglut2+ projection. This calls into question all the conclusions about the differential localization and function of synaptic proteins.

(2) It is unclear from the paper, but it seems that some experiments may have been done with no Cre control, which likely led to contamination in neighboring brain regions, some of which project to LHB as well.

(3) Histology: There is no histology shown for the mice used in the study. This is a crucial point. We need to see that the injection was clean and specific for each mouse used in the study (although, given the use of Vglut2-Cre, it cannot be specific to the coreleasing population). Whole-brain histology is necessary.

(4) ASO KO: Unfortunately, there is little validation of the ASO KO. The effects shown in Figure S2 show a very small effect, if any. There appear to be no statistics. The functional effects in the main figure are also relatively subtle.

(5) Other concerns: There are many typos and errors, including in important claims.

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 #2 (Public review):

Summary:

Authors examined neural substrates for cognitive empathy (conceptually understanding others' emotions) versus affective empathy (automatically sharing others' emotions) development in 3-5-year-old toddlers, and argued that cognitive empathy emerges earlier than affective empathy, challenging the predominant view that affective empathy develops earlier. The authors developed an empathy test for toddlers while measuring their brain activity with fNIRS (particularly in MPFC, STG, DLPFC, and TPJ) and heart rate. They found different brain region activation in cognitive versus affective empathy tasks, as well as age-related changes in the activation of right MPFC and right TPJ.

Strengths:

This work investigated the development of different components of empathy, which is a quite understudied topic. The authors developed an age-appropriate task for toddlers to measure their cognitive empathy and affective empathy, which is likely useful for future research in this field. Their methods are sound, and give a relatively large sample; the results look interesting and relatively solid, except for certain details in the reporting of methods and results.

Weaknesses:

(1) My major concern is the roles of brain regions hypothesized and found in this paper (MPFC, STG, DLPFC, and TPJ) - the authors seemed to have omitted a large portion of the literature on this topic. Prior works have found that these brain regions may be involved in more than one process, or involved in processes that are common to both cognitive and affective empathy (see Schurz et al., 2021). In particular, MPFC seems to be indicated more often in cognitive empathy, and STG may be involved in both cognitive empathy and intermediate processes, which is contradictory to what the author claimed and hypothesized. Relatedly, when the authors made statements like "these results highlight that regions underpinning affective and cognitive empathy in preschoolers largely resemble those documented in adults" (without proper citations), I found it unconvincing due to the disagreements in the past adult research about brain regions related to empathy, which were not quite discussed in the current paper. It may be helpful if the authors do a more thorough literature review and provide a more comprehensive view of how their results fit in the existing literature.

(2) Given the disagreement in the past research about the roles of these brain regions, I feel like the authors' hypotheses may be insufficiently justified, and their claim that cognitive empathy develops earlier than affective empathy is a bit overly strong - would it be possible that these brain regions' different rates/patterns of development are irrelevant to specific components of empathy? Given that behavioral data did not show any age difference, and that each brain region can engage in many functions besides empathy (e.g., generic social and emotional processing), I would be more cautious when interpreting these results.

(3) It would be helpful if the authors report certain parts of their methods and results in more detail.<br /> a) During the cognitive/affective empathy tasks, it is not explicitly clear which part of the fNIRS data were included in the analysis.<br /> b) When the authors did FDR corrections, they should include the q values and adjusted p values. I was also confused about how the FDR correction was conducted - were analyses performed on all 10 ROIs or only the hypothesized regions? I think if the authors have hypotheses about specific regions, they should test their hypotheses first, and then everything else would be exploratory analyses.<br /> c) Additionally, it is unclear what brain template was used and what procedure was followed to map channels of fNIRS data to the template.

References:

Schurz, M., Radua, J., Tholen, M. G., Maliske, L., Margulies, D. S., Mars, R. B., ... & Kanske, P. (2021). Toward a hierarchical model of social cognition: A neuroimaging meta-analysis and integrative review of empathy and theory of mind. Psychological bulletin, 147(3), 293.

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 #2 (Public review):

Summary:

The study demonstrated that Par, but not other polarity genes, Crumbs or Scrib, regulates cell polarity during PSC transition to primed state as well as neural tube formation.

Strengths:

The use of KO convinces the role of Par in NPT. Scrib and Crumbs KO data are informative to the field. The conditioned medium experiment is informative. They suggested the potential secreted factors over 50kDa are responsible for maintaining the polarity of NPT in Par KO.

Weaknesses:

Most importantly, how Par is important for PSC maintenance and differentiation is not clear. The data provided are dome shape formation, endoderm lineage tendency, and neural tube formation reduction. The manuscript lacks a core message of the physiological importance of Par. Is Par critical of PSC maintenance? Is Par critical for neural system development?

Secondly, AKT-FURIN-...... axis still lacks supportive data. Various inhibitors were used to rescue the Par KO. But the link between each component in the axis is missing and rather superficial.

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 #2 (Public review):

Summary:

The authors examine the effects of activating the dorsal raphe nucleus serotonergic system using a combination of calcium imaging and optogenetics in freely moving larval zebrafish. Their findings show that optogenetic stimulation induces a state of behavioral quiescence.

They further investigate whether this state corresponds to sleep or reduced motor activity. Analyses of posture and sleep-related paradigms indicate that serotonergic activation primarily suppresses motor output rather than promoting sleep. Notably, this suppression appears to be bout type-dependent, with stronger effects on neurons associated with larger tail amplitudes and turning angles.

In addition, auditory stimulation experiments reveal no significant impact of serotonin on sound encoding.

Strengths:

The study combines advanced experimental techniques with state-of-the-art analytical methods, enabling precise and compelling insights into the role of serotonergic modulation. The experiments and analyses are well aligned with the questions being addressed, and the results appear robust and reliable.

Moreover, the implementation of experiments that combine calcium imaging and optogenetics in freely moving animals is technically challenging and appears well justified in the context of the research questions.

Weaknesses:

While the authors discuss different quiescent states mediated by serotonin reported in previous studies, more thorough attempt to determine whether the observed state corresponds to any of the previously described forms of quiescence, or represents a subset or variant of them, would strengthen the manuscript. This would help better integrate the findings with the existing literature.

While addressing these questions may require substantial further work, potentially beyond the scope of the present study, the availability of whole-brain data provides an opportunity to at least explore or discuss these possibilities. In particular, it would be interesting to examine the recruitment of regions not directly stimulated but known to be associated with other neuromodulatory systems or promoting glial activation (e.g., the locus coeruleus).

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 #2 (Public review):

Summary:

In this manuscript, the authors investigated magnesium isoglycyrrhizinate (MgIG)'s hepatoprotective actions in chronic-binge alcohol-associated liver disease (ALD) mouse models and ethanol/palmitic acid-challenged AML-12 hepatocytes. They found that MgIG markedly attenuated alcohol-induced liver injury, evidenced by ameliorated histological damage, reduced hepatic steatosis, and normalized liver-to-body weight ratios. RNA sequencing identified isopentenyl diphosphate delta isomerase 1 (IDI1) as a key downstream effector. Hepatocyte-specific genetic manipulations confirmed that MgIG modulates the SREBP2-IDI1 axis. The mechanistic studies suggested that MgIG could directly target HSD11B1 and modulate the HSD11B1-SREBP2-IDI1 axis to attenuate ALD. This manuscript is of interest to the research field of ALD.

Strengths:

The authors have performed both in vivo and in vitro studies to demonstrate the action of magnesium isoglycyrrhizinate on hepatocytes and an animal model of alcohol-associated liver disease.

My first question: All the treatment arms (A-control, MgIG-25 mg/kg, MgIG-50 mg/kg) showed significant body weight loss compared to the untreated controls (Supplemental Figure 1A), but the body weight significantly increased in the treatment arms (A-control and MgIG-50 mg/kg) compared to the untreated controls (Figure 1E). Why?

My second question: Mice with MgIG (25 mg/kg) showed the lowest body weight, compared to either A-control or MgIG (50 mg/kg) treatment. According to the authors' explanation, the MgIG (25 mg/kg) caused bodyweight loss are attributed to inter-individual variability, differences in metabolic adaptation, or sample size-related variation. Did these differences happen in MgIG (25 mg/kg) only? or in all other groups? The mouse group assignment should be randomized; however, a large variation in bodyweight was seen in MgIG (25 mg/kg) group. It is not convincing for the author to select MgIG (50 mg/kg) group for subsequent animal experiments, because of a large variation in MgIG (25 mg/kg) group, and because that MgIG (50 mg/kg) group demonstrated more consistent and stable improvements across multiple parameters. The author should reanalyze and compare all the raw data between MgIG (50 mg/kg) group and MgIG (25 mg/kg) group, and address the issues being pointed out and justify rationale for the animal group assignment.

The author's response did not answer my question. If the authors believe it could be experimental constraints associated with the MgIG formulation, then it is questionable for this MgIG formulation used in all other associated experiments. The experiments, at least those the MgIG formulation associated experiments, need to be repeated.

The author explained the relative expression was normalized to GAPDH (fold change), but they did not answer my question. My question is for Figure 5B. in Figure 5B (left, Hsd11b1-KD), scramble control showed over 100 (unit), however, in Figure 5B (right, Hsd11b1-OE), scramble control showed only 0.5-1 (unit). The data seemed that authors used same scramble control for both KD and OE? If yes, they should provide more details of the KD and OE experiments and explain why this happened. If they used plasmid for OE control, they also need to clarify it. In addition, qPCR is not a good assay to show the success of KD or OE, Western blotting should be done as convincing data to show the success of KD or OE.

Comments on revised version.

In this revision, all the issues are addressed.

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 #2 (Public review):

Summary and strengths:

In this manuscript, Karjee and colleagues used coalescent based effective population size reconstruction (PSMC) from single genomes to understand past population trends in island birds and related this to life history traits and glacial patterns. In this analysis they chose to use a generation time of 2 years for passerines and 1 year for non-passerines. Non-passerine birds include Amazona vittata which only reaches sexual maturity at 3-5 years; Amazona guildingii which reaches sexual maturity at ~5 years; Amblyornis subalaris at 7 years etc. This means that the choice of generation time is very poorly matched to the species biology of many of the focal systems. What this will do is to "squash" the PSMC plot, meaning that population trends will not match with when they actually occurred. As a result, glaciation windows are not correctly placed. It is my opinion that the results are not interpretable in the current form.

The authors must adjust the generation time to roughly the median period between average age of sexual maturity and age of death. It should represent the time when an individual has had 50% of their offspring. After which all analyses must be repeated.

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 #3 (Public review):

Summary:

In this manuscript Bohra et al. measure the effects of estrogen responsive gene expression upon induction on nearby target genes using a TAD containing the genes TFF1 and TFF3 as a model. The authors propose that there is a sort competition for transcriptional machinery between TFF1 (estrogen responsive) and TFF3 (not responsive) such that when TFF1 is activated and machinery is recruited, TFF3 is activated after a time delay. The authors attribute this time delay to transcriptional machinery that was being sequestered at TFF1 becomes available to the proximal TFF3 locus. The authors demonstrate that this activation is not dependent on contact with the TFF1 enhancer through deletion, instead they conclude that it is dependent on a phase-separated condensate which can sequester transcriptional machinery. Although the manuscript reports an interesting observation that there is a dose dependence and time delay on the expression of TFF1 relative to TFF3, there is much room for improvement in the analysis and reporting of the data. Most importantly there is no direct test of condensate formation at the locus in the context of this study: i.e. dissolution upon the enhancer deletion, decay in a temporal manner, and dependence of TFF1 expression on condensate formation. Using 1,6' hexanediol to draw conclusion on this matter is not adequate to draw conclusions on the effect of condensates on a specific genes activity given current knowledge on its non-specificity and multitude of indirect effects. Thus, in my opinion the major claim that this effect of a time delayed expression of TFF3 being dependent on condensates in not supported by the current data.

Strengths:

The depends of TFF1 expression on a single enhancer and the temporal delay in TFF3 is a very interesting finding.

The non-linear dependence of TFF1 and TTF3 expression on ER concentration is very interesting with potentially broader implications.

The combined use of smFISH, enhancer deletion, and 4C to build a coherent model is a good approach.

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:

The authors discovered that HDAC1/2 are degraded in HSV-1 and PRV infections. They attempted to establish a new mechanism by which HDAC1/2 are translocated to the cytoplasm to be degraded in HSV-1 infection, and the degradation causes changes in histone acetylation to affect the DDR pathway.

Strengths:

(1) Interesting findings of HDAC1/2 degradation during HSV-1 and PRV infection, and it may impact more than the virology field.

(2) Significant work to identify the ubiquitin site in HDAC1/2 and K63 linkage.

Comments on revised version:

The authors added experiments to address the previous comments. The added knockdown and overexpression experiments provided sufficient support for the proposed mechanism. The conclusions are now strengthened. However, a few essential controls are still missing.

(1) Figure 3K: How does the expression level of Flag-HDAC1 variants compare to the endogenous HDAC1 level? The stripe probed by Flag antibody should be reprobed by HDAC1 antibody. Also, how does the K74R mutant affect histone acetylation? Moreover, the numbers between the panels are hard to read and have not been explained.

(2) Figure 3M and 3L: DNA transfection per se frequently stimulates cell reactions that inhibit HSV-1 replication. Is the HSV-1 only sample transfected by empty vector or untransfected?

(3) Figure 4G-4J: What is the MDM2 knockdown efficiency?

(4) Figure 5F and line 400-401: "thereby preventing HDAC1 degradation-markedly impaired HSV-1 replication (Fig. 5F)." However, viral replication is not demonstrated in Figure 5F.

(5) Figure 5K: also need a control of empty vector. Furthermore, how does the HDAC1 NES expression affect histone acetylation and DDR responses?

(6) Statements listed below are better moved to discussion after all data being presented. They are quite a stretch when looking at each figure by itself.

(i) Line 268-270: "Together, these findings indicate that HSV-1 selectively degrades class I HDACs, resulting in widespread histone hyperacetylation that fosters a chromatin state conducive to viral replication". ----may be okay for a statement.

(ii) Line 291-292: "providing initial evidence that HSV-1 infection promotes DDR activation through downregulation of HDAC1 expression"

(iii) Line 331-333: "Together, these results indicate that HSV-1 infection promotes K63-linked polyubiquitination of HDAC1/2 at conserved lysine residues, ultimately leading to their proteasomal degradation."

(iv) Line 334-336 is a repeated sentence.

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 #3 (Public review):

Summary:

This study from Jia et al carried out a variety of analyses of terminating ribosomes, including the development of eRF1-seq to map termination sites, identification of a GA-rich motif that promotes ribosome pausing, characterization of tissue-specific termination dynamics, and elucidation of the regulatory roles of 18S rRNA and RPS26. Overall, the study is thoughtfully designed, and its biological conclusions are well supported by complementary experiments. The tools and datasets generated provide valuable resources for researchers investigating the mechanisms of RNA translation.

Strengths:

(1) The study introduces eRF1-seq, a novel approach for mapping translation termination sites, providing a methodological advance for studying ribosome termination.

(2) Through integrative bioinformatic analyses and complementary MPRA experiments, the authors demonstrate that GA-rich motifs promote ribosome pausing at termination sites and reveal possible regulatory roles of 18S rRNA in this process.

(3) The study characterizes tissue-specific ribosome termination dynamics, showing that the testis exhibits stronger ribosome pausing at stop codons compared to other tissues. Follow-up experiments suggest that RPS26 may contribute to this tissue specificity.

Weaknesses:

The biological significance of ribosome pausing regulation at translation termination sites or of translational readthrough, for example across different tissue types, remains unclear. Nevertheless, this question lies beyond the primary scope of the current study.

Comments on the latest version:

The authors addressed my comments by revising the claims in the manuscript.

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 #2 (Public review):

Summary:

The authors aim to address whether nuclear pore complex components localize and function at PD in plant cells to mediate cell-to-cell communication.

Strengths:

(1) Novelty and Significance:

The core hypothesis, drawing parallels between PD and NPC transport, is highly original and addresses a critical gap in understanding plant intercellular communication. The idea that phase-separated domains formed by FG-NUPs could act as diffusion barriers at PD offers an alternative and plausible explanation for their complex transport properties, including size exclusion and facilitated translocation. This could fundamentally change how we view PD transport and function.

(2) Comprehensive Evidence:

The study employs a rigorous and diverse set of experimental approaches, including a comprehensive bioinformatic analysis of both moss and Arabidopsis NUPs in available PD proteomic datasets, extensive imaging analysis of Nup localization in vivo, and functional transport assays using a loss-of-function nup mutant (cpr5). The transport assay is particularly important to provide functional evidence linking CPR5 to PD-mediated transport. The finding that callose levels were not significantly different in cpr5 mutants under these conditions is helpful and supports a distinct, callose-independent mechanism of transport regulation.

(3) Objectivity:

The authors are forthright in discussing the limitations and potential artifacts of their own data, clearly distinguishing between observations and definitive conclusions.

Weaknesses:

While the claims are generally justified as hypotheses or consistent observations, the authors themselves extensively detail the caveats, which are worth reiterating for clarity:

(1) Potential Overexpression Artifacts in Localization:

Although efforts were made to control expression levels, the authors acknowledge that transient overexpression could still lead to NUP accumulation at PD, either as a physiologically irrelevant accumulation under excess conditions or due to mis-targeting. Note that they provided data showing Nup62 PD localization at a near native level.

(2) CPR5 Mutant Interpretation:

While cpr5 mutants exhibited reduced macromolecular transport, the authors state that they cannot exclude that the reduced transport is due to secondary effects in the cpr5 mutants, which show rather severe phenotypic defects. This is an important distinction, as CPR5 has known roles in defense responses and hormone signaling that could indirectly influence PD integrity, independent of callose deposition. The lack of effect on small molecule transport is a good control, but the broader pleiotropic effects of cpr5 mutants remain a consideration.

(3) Conceptual Distinction between NPC and PD:

The authors correctly point out that while similarities exist, the physical assembly of NUPs at PD must differ from that at the NPC due to the presence of the desmotubule and smaller cytoplasmic sleeve width at PD. Moreover, nucleocytoplasmic transport depends on kayropherin proteins (importins) that interact with the NPC central channel to complete the transport. Yet the role of karyopherins in this case is not clear. Therefore, the proposed "PD pore complex" may bear some NPC features, but not identical.

Reviewer #3 (Public review):

Summary:

This manuscript presents a step towards testing the hypothesis that plasmodesmata have homology to nuclear pores. The similarities between the two structures have long been noted as both structures allow the transport of proteins and nucleic acids and both structures are composed of curved membranes. The manuscript has identified nuclear pore proteins (NUPs) in plasmodesmal protein fractions and uses live imaging in a non-endogenous system and functional assays of a mutant to propose that this might be a bone fide association.

The conclusions the authors seek to draw are that: NUPs are present in plasmodesmal protein fractions; NUPs localise at plasmodesmata; NUPs might form a pore-gating complex at plasmodesmata, regulating non-specific (2xGFP) and specific (SHR) transport through plasmodesmata.

The authors then use these conclusions to propose the possibility that phase separation mediates transport through plasmodesmata. If there is phase separation at plasmodesmata or a nuclear pore-like complex, it would revolutionise the community. However, this data is insufficient to act as a cornerstone for such a discovery.

Strengths:

The strength of the manuscript lies in the boldness and novelty of the idea.

Weaknesses:

The weaknesses lie in the lack of resolution over the specificity of the plasmodesmal association of the NUPs. The authors' own assessments of their data suggest they agree with this - in their abstract alone they point out that the transport defects they observe might be off-target effects and suggest there is a requirement in the future to determine whether the NUPs are bona fide PD components.

Across the proteomic and live imaging experiments, the authors have tried to make their initial conclusions stronger by comparing the NUP localisation and accumulation with ER proteins. Thus, they have demonstrated that there are some differences in the localisations between the NUPs and an ER-lumen marker, although there are also many similarities. Indeed, for CPR5 they have demonstrated that the protein in ER located and their imaging shows a very clear association with ER beyond the plasmodesmata. Residence in the ER does not prevent the possibility that the protein has a plasmodesmal function, but it does raise questions of specificity of the localisation at the plasmodesmata (and nuclear envelope) when it is evident throughout the ER. The authors acknowledge the possibility that PD accumulation is artefactual, so they are aware of this.

In my initial review I suggested that super-resolution imaging of an ER marker would help interpret the structures revealed by CPR5 in Figure 6. The authors indicated that because the localisation of NUPs looked different to the ER luminal marker that this wasn't a priority. However, they have shown that CPR5 is an ER-resident protein and so I disagree with this conclusion. I think this experiment would provide valuable information regarding whether there is any specificity in CPR5 accumulation at plasmodesmata.

Regarding the proteomic identification of NUPs in plasmodesmal fractions, the authors place significant weight on their own metric for PD enrichment, the PD score. As I understand it, this a metric derived from addition of two factors: a two component enrichment score that is the difference between intensity of peptides of a given protein in the PD fraction and cell wall fraction, added to the difference between intensity of peptides of a given protein in the PD fraction and total cell fraction, and a feature score that is a factor that describes representation of protein domains contained in said given protein in the plasmodesmal fraction relative to the representation of that domain in proteins in the whole proteome. The features chosen for analysis are not indicated and the feature factor, as I understand it is a score common to all proteins with a given feature. While each of the factors carries a measure of meaning and information, I do not understand how adding them is mathematically or biologically meaningful.

Regarding the possibility that there is a pore-gating complex at plasmodesmata. If NUPs are specifically located at plasmodesmata, this is a strong hypothesis. The authors approach this functionally by assaying for protein and dye movement through plasmodesmata in the cpr5 mutants. These experiments suggest that cpr5 mutants have reduced transport through plasmodesmata for both proteins, but not for a smaller dye. In their introduction the authors identify how PD structure can modify transport capacity so there are many technical and biological phenomena that could explain these data. Further, as the authors themselves acknowledge, altered protein movement might also arise from an off-target developmental phenotype. Many proteins have been shown to have no association with plasmodesmata but an indirect effect on their function. This hasn't been investigated and so cannot be ruled out.

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 #2 (Public review):

Summary:

The study presents novel results on the presence of the Entner-Doudoroff pathway in Synechocystis sp. PCC 6803. In contrast to an earlier study, compelling evidence is given that this strain lacks both an ED pathway and a glucose dehydrogenase/glucokinase bypass but contains a promiscuous aldolase, which also decarboxylates oxaloacetate and cleaves 2-keto-4-hydroxyglutarate (as it occurs in proline degradation). The study concludes with successfully reconciling data from different studies and with lessons learned from the previous misconception.

Strengths:

Solid biochemical data are presented to reconcile contradicting data of earlier studies and to serve as a basis for disclosing possible functions of a promiscuous aldolase. Earlier misconceptions and lessons to be learned are well discussed.

Weaknesses:

The materials and methods section is rather lengthy, suffering from a lack of conciseness and repetition, and nevertheless misses some specifications.

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 #2 (Public review):

Summary:

The authors set out to determine whether people can adjust how narrowly or broadly they focus attention in advance based on expectations about how difficult an upcoming visual task will be. Specifically, they aimed to test whether expecting a more demanding search leads to a narrower focus of attention or instead strengthens attention at the relevant location without changing its spatial extent.

Strengths:

The study addresses a timely and interesting question about how expectations influence the preparation of attention before a task begins. The experimental design is well suited to isolating anticipatory effects by manipulating expectations about task difficulty independently of moment-to-moment stimulus information. The manuscript is clearly written, and the methods are described in sufficient detail to support transparency and reproducibility.

Comments on revised version.

During the review process the authors addressed my previous concerns. The revisions have improved the clarity of the analyses and the interpretation of the results, and I have no further substantive comments.

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 #2 (Public review):

Summary:

This manuscript examines the association between atovaquone/proguanil use, zoster vaccination, toxoplasmosis serostatus and Alzheimer's Disease, using 2 databases of claims data. The manuscript is well written and concise. The major concerns about the manuscript center around the indications of atovaquone/proguanil use, which would not typically be active against toxoplasmosis at doses given, and the lack of control for potential confounders in the analysis.

Strengths:

(1) Use of 2 databases of claims data.

(2) Unbiased review of medications associated with AD, which identified zoster vaccination associated with decreased risk of AD, replicating findings from other studies.

Weaknesses:

(1) Given that atovaquone/proguanil is likely to be given to a healthy population who is able to travel, concern that there are unmeasured confounders driving the association.

(2) The dose of atovaquone in atovaquone/proguanil is unlikely to be adequate suppression of toxo (much less for treatment/elimination of toxo), raising questions about the mechanism.

(3) Unmeasured bias in the small number of people who had toxoplasma serology in the TriNetX cohort.

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 #2 (Public review):

Summary:

The authors propose that bidirectional redistribution of actomyosin drives tissue invagination in Ciona siphon tube formation. They suggest a two-stage model where actomyosin first accumulates apically to drive a slow initial invagination, followed by redistribution to lateral domains to accelerate the invagination process through cell shortening. They have shown that actomyosin activity is important for invagination - modulation of myosin activity through expression of myosin mutants altered the timing and speed of invagination; furthermore, optogenetic inhibition of myosin during the transition of the slow and fast stages disrupted invagination. The authors further developed a vertex model to validate the relationship between contractile force distribution and epithelial invagination.

Strengths:

(1) The authors employed various techniques to address the research question, including optogenetics, use of MRLC mutants, and vertex modelling.

(2) The authors provide quantitative analyses for a substantial portion of their imaging data, including cell and tissue geometry parameters as well as actin and myosin distributions. The sample sizes used in these analyses appear appropriate.

(3) The authors combined experimental measurements with computer modeling to test the proposed mechanical models, which represents a strength of the study. It provides a framework to explore the mechanical principles underlying the observed morphogenesis.

Comments on the revision.

The revised manuscript has been substantially improved. The authors have addressed many of my previous concerns through the addition of new data, analyses, and discussion. The characterization of epithelial folding in the ascidian Ciona provides valuable insight into a comparatively less explored morphogenetic system, and the imaging and quantitative analyses are overall compelling. That said, a few important points remain to be addressed.

One remaining issue concerns the mechanistic novelty of the actomyosin redistribution described in this study. The authors emphasize that the key novelty lies in the stepwise translocation of actomyosin from the lateral membrane to the apical domain during the initial stage (apical constriction), followed by redistribution from the apical domain back to the lateral domain during the accelerated stage (invagination). I agree that the dynamic redistribution itself is potentially interesting and may represent an underexplored aspect of epithelial morphogenesis. However, as I discussed in my previous review comments, from a mechanics perspective, the role of apical actomyosin in driving apical constriction and of lateral actomyosin in contributing to tissue folding/invagination have already been demonstrated in multiple systems, although to varying extents depending on the model. Therefore, while the current study convincingly documents a distinct spatiotemporal sequence of actomyosin localization in Ciona atrial siphon tube formation, it could be clarified further to what extent this work advances new mechanical principles underlying epithelial folding, as opposed to revealing a variation in the deployment of previously described force-generating modules.

Importantly, I think the manuscript has the potential to provide deeper conceptual insight if the authors more explicitly consider the significance of the "redistribution" process itself. Redistribution does not only involve the appearance of actomyosin at a new membrane domain; it also necessarily involves its disappearance from the previous domain. The latter aspect has, in my view, been much less explored in the literature. For example: Is the removal of lateral actomyosin during the early phase important for efficient apical constriction? Conversely, is the reduction of apical actomyosin during the later accelerated phase important for proper invagination mechanics? These questions are particularly interesting because they address whether redistribution between domains serves an active mechanical regulatory role, rather than focusing on the role of force-generating actomyosin at a given location.

I acknowledge that addressing these questions experimentally could be technically challenging. One potentially powerful way to address this would be through the revised computational model. For example, the authors could test whether tissue folding is altered when actomyosin is allowed to accumulate at a new domain without being concomitantly depleted from the original domain. Such analyses could help distinguish whether redistribution itself has functional mechanical importance, rather than merely reflecting sequential recruitment to different cellular regions. In my opinion, incorporating this aspect would substantially strengthen the conceptual and mechanistic novelty of the study.

My other concern relates to the new optogenetic data presented in Figure 4-figure supplement 2. In the "Dark" samples, active myosin does not appear to be clearly enriched along the membrane, but instead seems relatively diffuse within the cytoplasm. This appears distinct from the images shown in Figure 2, where active myosin exhibits clear membrane enrichment. Could the authors provide top-view images for the samples shown in Figure 4-figure supplement 2? This would help clarify whether active myosin is indeed enriched along the apical membrane at 16 hpf and along the lateral membrane at 17 hpf in the "Dark" condition.

In addition, the tissue morphology in the "17 hpf Light 1 hr" panel of Figure 4-figure supplement 2 appears noticeably different from that shown in Figure 4. Specifically, the apical side of the tissue in Figure 4 appears substantially more relaxed than in Figure 4-figure supplement 2. Based on the authors' interpretation of the optogenetic experiments, apical active myosin is not strongly affected by the treatment described in Figure 4. If so, one would expect apical constriction to remain largely intact. However, the more relaxed apical domain shown in Figure 4 seems to suggest that apical constriction may in fact be perturbed by the optogenetic manipulation. This apparent discrepancy complicates the interpretation of the experiment and seems somewhat inconsistent with the authors' main conclusion from this figure.

Reviewer #3 (Public review):

Summary:

In this revised manuscript by Qiao et al., the authors seek to uncover force and contractility dynamics that drive tissue morphogenesis, using the Ciona atrial siphon primordium as a model. Specifically, the authors perform a detailed examination of epithelial folding dynamics. Generally, the authors' claims were supported by their data, and the conceptual advances may have broader implications for other epithelial morphogenesis processes in other systems.

Strengths:

The strengths of this manuscript include the variety of experimental and theoretical methods, including generally rigorous imaging and quantitative analyses of actomyosin dynamics during this epithelial folding process, and the derivation of a mathematical model based on their empirical data, which they perturb in order to gain novel insights into the process of epithelial morphogenesis.

Weaknesses:

Concerns raised in the initial submission were addressed in the revised manuscript.

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 #2 (Public review):

In the present manuscript, Li et al. use biochemical fractionation of "RNA granules" from P5 wildtype and FMR1 knock-out mouse brains to analyze their protein/RNA content, determine a single particle cryo-EM structure of contained ribosomes, and perform ribo-seq analysis of ribosome-protected RNA fragments (RPFs). The authors conclude from these that neither the composition of the ribosome granules, nor the state of their contained ribosomes, nor the mRNA positions with high ribosome occupancy change significantly. Besides minor changes in mRNA occupancy, the one change the authors identified is a decrease in puromycylated punctae in distal neurites of cultured primary neurons of the same mice, and their enhanced resistance to different pharmacological treatments. These results directly build on their earlier work (Anadolu et al., 2023) using analogous preparations of rat brains; the authors now perform a very similar study using WT and FMR1-KO mouse brains. This is an important topic, aiming to identify the molecular underpinnings of the FMRP protein, which is the basis of a major neurological disease. Unfortunately, several limitations of this study prevent it from being more convincing in its present form.

In order to improve this study, our main suggestions are as follows:

(1) The authors equate their biochemically purified "RG" fraction with their imaging-based detection of puromycin-positive punctae. They claim essentially no differences in RGs but detect differences in the latter (mostly their abundance and sensitivity to DHPG/HHT/Aniso). In the discussion the authors acknowledge the inconsistency between these two modalities: "An inconsistency in our findings is the loss of distal RPM puncta coupled with an increase in the immunoreactivity for S6 in the RG." and "Thus, it may be that the RG is not simply made up of ribosomes from the large liquid-liquid phase RNA granules."<br /> How can the authors be sure that they are in fact analysing the same entities in both modalities? A more parsimonious explanation of their results would be that, while there might be some overlap, two different entities are analyzed. Much of the main message rests on this equivalence and I believe the authors should show its validity.

(2) The authors show that increased nuclease digestion (and magnesium concentration) led to a reduction of their RPF sizes down to levels also seen by other researchers. Analyzing these now properly digested RPFs, the authors state that the CDS coverage and periodicity drastically improved, and that spurious enrichments of secretory mRNAs, which made up one of the major fractions in their previous work, are now reduced. In my opinion this would be more appropriately communicated as a correction to their previous work, not as a main Figure in another manuscript.

(3) The fold changes reported in Figure 7 (ranging between log2(-0.2) and log2(+0.25)) are all extremely small and in my opinion should not be used to derive claims such as "The loss of FMRP significantly affected the abundance and occupancy of FMRP-Clipped mRNAs in WT and FMR1-KO RG (Fig 7A, 7B), but not their enrichment between RG and RCs".

(4) Fig 8 / S8-1 - The authors show that ~2/3 of their reads stem from PCR duplicates, but that even after removing those, the majority of peaks remains unaltered. At the same time, Fig S8-1 shows the total number of peaks to be 615 compared with 1392 before duplicate removal. Can the authors comment on this discrepancy? In addition, the dataset with properly removed artefacts should be used for their main display item instead of the current Fig 8.

(5) Fig 9 / S9-1, the density of punctae in both WT and FMR1-KO actually increases after treatment of HHT or Anisomycin (Fig S9-1 B-C). Even if a large fraction would now be "resistant to run-off", there should not be an increase. While this effect is deemed not significant, a much smaller effect in Fig 9C is deemed significant. Can the authors explain this? Given how vastly different the sample sizes are (ranging from 23 neurites in Fig S9-1 to 5,171 neurites in Fig 9), the authors should (randomly) sample to the same size and repeat their statistical analysis again to improve their credibility.

Comments on revised version.

We can see that the authors invested substantial effort to improve the manuscript and we believe it is improved.

Reviewer #3 (Public review):

Summary:

Li et al describe a set of experiments to probe the role of FMRP in ribosome stalling and RNA granule composition. The authors are able to recapitulate findings from a previous study performed in rats (this one is in mice).

Strengths:

(1) The work addresses an important and challenging issue, investigating mechanisms that regulate stalled ribosomes that are part of stress granules, and focusing on the role of FMRP. This is a complicated problem, given the heterogeneity of the granules and the challenges related to their purification. This work is a solid attempt at addressing this issue, which is widely understudied.

(2) The interpretation of the results could be interesting, if supported by solid data. The idea that FMRP could control the formation and release of stress granules, rather than the elongation by stalled ribosomes is of high importance to the field, offering a fresh perspective into translational regulation by FMRP.

(3) The authors focused on recapitulating previous findings, published elsewhere (Anadolu et al., 2023) by the same group, but using rat tissue, rather than mouse tissue. Overall, they succeeded in doing so, demonstrating, among other findings, that stalled ribosomes are enriched in consensus mRNA motifs that are linked to FMRP. These interesting findings reinforce the role of FMRP in formation and stabilization of RNA granules. It would be nice to see extensive characterization of the mouse granules as performed in Figure 1 of Anadolu and colleagues, 2023.

(4) Some of the techniques incorporated aid in creating novel hypotheses, such as the ribopuromycilation assay and the cryo-EM of granule ribosomes.

Comments on revised version:

I am satisfied with the authors response to my comments.

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 #2 (Public review):

Summary:

In the manuscript by Walter-McNeill, Kruglyak and team, the authors provide solid evidence of another toxin-antidote (TA) system in C. elegans. Generally, TA systems involve selfish and linked genetic elements, one encoding a toxin that kills progeny inheriting it, unless an antidote (the second element) is also present. Currently, only two TA systems have been characterized in this species, pointing to the importance of identifying new instances of such systems to understand their transmission dynamics, prevalence, and functions in shaping worm populations.

The manuscript has been improved in some aspects upon revision. We remain enthusiastic for the overall findings and the identification of a new toxin/anti-toxin system and note that the strengths and weaknesses we detailed previously remain. We reiterate our critique regarding the strength of conclusions that can be made about small RNA pathway regulation based on meta-analysis of other datasets. While we agree that the observations presented are suggestive of small RNA regulation, likely due to piRNA targeting and subsequent 22G-RNA regulation, until these hypotheses are tested experimentally in the future by mutation of the piRNA target sites, testing ago/piRNA pathway and other 22G-RNA pathway mutants for tmrl-1 expression, etc., we think it is important to use precise language in presenting the conclusions. In particular, the abstract states:

"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. The N2 haplotype represents the first naturally occurring unlinked toxin-antidote system where the toxin is post-transcriptionally suppressed by endogenous small RNA pathways."

We therefore recommend moderating this statement to "...is likely to be post-transcriptionally suppressed by endogenous small RNA pathways."

Previously noted strengths and weaknesses remain relevant to this revision.

Strengths:

This novel TA system (mll-1/smll-1) was identified on LGV in wild C. elegans isolates from the Hawaiian Islands, by crossing divergent strains and observing allele frequency distortions by high throughput genome sequencing after 10 generations. These allele frequency distortions were subsequently confirmed in another set of crosses with a separate divergent strain, and crosses of heterozygous males or hermaphrodites resulted in a pattern of L1 lethality in progeny (with a rod arrest phenotype) that suggested the maternal transmission of this TA system from the XZ1516 genetic background. By elegantly combining the use of near-isogenic lines, CRISPR editing to generate knock-outs, and a transgene rescue of the antidote gene, the authors identified the genes encoding the toxin and the antidote, which they refer to as mll-1 and smll-1. Moreover, the specific mll-1 isoform responsible for the production of the toxin was identified and mll-1 transcripts were observed by FISH in early and late embryos, as well as in larvae. Inducible expression of the toxin in various strains resulted in larval arrest and rod phenotypes. The authors then characterized the genetic variation of 550 wild isolates at the toxin/antidote region on LGV and distinguished three clades: 1) one with the conserved TA system, 2) one having lost the toxin and retaining a mostly functional antidote, and 3) one having lost the antidote and retaining a divergent yet coding toxin (this includes the reference strain Bristol N2, in which the homologous toxin gene has acquired mutations and is known as B0250.8). Further, the authors show that this region is under positive selection. These data are compelling and provide very strong evidence of a new TA system in this species.

Weaknesses:

The question remained as to how one clade, including N2, could retain the toxin gene but not possess a functional antidote. In the second part of the manuscript, the authors hypothesized that small RNA targeting (RNAi) of the toxin transcript could provide the necessary repression to allow worms to survive without the antidote. Through a meta-analysis of multiple small RNA datasets from the literature, the authors found evidence to support this idea, in which the toxin transcript is targeted by 22G siRNAs whose biogenesis is dependent on the Mutator foci protein, MUT-16. They note that from previous studies, mut-16 null mutants displayed a varied penetrance of larval arrest. In their own hands, mut-16 mutants displayed 15% varied larval arrest and 2% rod phenotypes. In an attempt to link B0250.8 to mut-16/siRNAs, they made a double mutant and examined body length as a proxy for developmental stage. Here, they observed a partial rescue of the mut-16 size defect by B0250.8 mutation. Finally, the authors also highlight data from further meta-analysis which predicts the recognition of B0250.8 by several piRNAs. Also based on existing data from the literature, the authors link loss of Piwi (PRG-1), which binds piRNAs, to a depletion of 22G-RNAs targeting B0250.8 and an upregulation of B0250.8 expression in gonads, suggesting that piRNAs are the primary small RNAs that target B0250.8 for down-regulation. The data in this portion of the manuscript are intriguing, but somewhat incomplete, as they are based on little primary experimentation and a collection of different datasets (which have been acquired by slightly different methods in most cases). This portion of the study would require subsequent experimentation to firmly establish this mechanistic link. For example, to be able to claim that "the N2 toxin allele has acquired mutations that enable piRNA binding to initiate MUT-16-dependent 22G small RNA amplification that targets the transcript for degradation" the identified piRNA sites should be mutated and protein and transcript levels analysed in wild-type and in the strain with mutated piRNA sites. At a minimum, the protein levels in wild-type and mut-16, prg-1, and/or wago-1 mutants should be measured by western blot and/or by live imaging (introducing a GFP or some other tag to the endogenous protein via CRISPR editing) to show that the toxin is not accumulated as a protein in wt, but increases in levels in these mutants. mRNA levels in Fig S5A suggest there is still some expression of the B0250.8 transcript in a wild type situation.

Comments on revised version.

We have no further recommendations for the authors, other than those provided above.

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 #2 (Public review):

Summary:

Previous work in the field highlighted the role of the kinesin-10 motor protein Kid (KIF22) in the polar ejection force during prometaphase. However, the biochemical and biophysical properties of Kid that enabled it to serve in this role were unclear. The authors demonstrate that human and xenopus Kid proteins are processive kinesins that function as homodimeric molecules. The data are solid and support the findings although the text could use some editing to improve clarity.

Strengths:

A highlight of the work is the reconstitution of DNA transport in vitro.

A second highlight is the demonstration that the monomer vs dimer state is dependent on protein concentration.

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 #2 (Public review):

Summary:

This work presents three tools: SqueakPose Studio, which is used for pose estimation; SqueakView, which is used for real-time video and sensor data capture and analysis; and MouseHouse, which is a behavioral and sensor suite for mouse experiments. Together, these tools provide a comprehensive behavioral platform for acquiring and analyzing video, sensor, and behavioral data. The work is open source and provided as a resource for the field.

Strengths:

(1) Squeakpose Studio was relatively easy to install and use. We were impressed that we were able to install it and test our own videos with minimal struggles. The authors provide installation tutorial videos that were very helpful.

(2) The GUI environment for SqueakPose Studio was very usable, and the authors should be commended on the time and effort that went into improving the useability of their system. The keypoint and skeleton configuration was flexible, allowing us to define custom body part sets without modifying code directly. The pose estimation accuracy on our own videos was good right out of the box, without requiring fine-tuning or retraining. For a tool being evaluated for the first time, this was all very impressive!

Weaknesses:

(1) While we were able to install and test Squeakpose Studio, it was not entirely seamless. The primary installation resource is a tutorial video, and we would recommend supplementing this with a written installation checklist that explicitly lists all required software dependencies (e.g. Python, UV, Visual Studio). The tutorial video was also at times unclear in distinguishing required from optional components. For example, Visual Studio is described as not necessary, yet the tutorial demonstrates the workflow entirely within that environment, so it may be challenging for a user to follow along without that. We recommend that the authors adopt a stricter, step-by-step installation guide that is prescriptive about required software and leaves little room for confusion.

(2) The paper also describes SqueakView and MouseHouse. Unfortunately, we were unable to evaluate these components as both require the MouseHouse hardware platform. Even without directly using MouseHouse, we noticed some incompleteness here, as we could not locate a bill of materials, component pricing, or assembly guide in the paper or associated GitHub repositories. Given that affordability and accessibility are central claims, a consolidated parts list, approximate costs, and a build guide or video would be necessary for most labs to realistically decide whether they plan to replicate the hardware and evaluate this functionality that the paper describes. In this regard, we felt that MouseHouse and potentially SqueakView were not sufficiently documented for publication.

(3) The benchmarking comparison to DeepLabCut (DLC) introduced multiple challenges that left us unclear if the head-to-head comparison was appropriate as described. First, the dataset used for benchmarking was small and homogeneous, from the methods they used "10 min open-field tasks of single mice with bilateral photometry cables." As such, the claims about comparisons between SqueakPose Studio and DLC may be too broad, given this single test case. Specifically, this dataset does not test robustness across lighting conditions, coat colors, species, occlusions, different-shaped arenas, etc. Second, the comparison to DLC in Figure 1 does not include any quantitative statistical comparisons, which are needed to evaluate the claims that were made. For instance, the error in Figure 1e looks worse for their system than DLC, although statistical comparisons were not made. Third, there are many settings and optimizations that can be made for both systems. Without more detail, this makes it hard to know if the head-to-head comparison is really fair. Fourth - the metrics are given as very specific numbers from single runs, i.e., an inference time of 71.59 minutes in Figure 1d. This metric would be more meaningful if it reported the mean of multiple runs, with error estimation. Finally, while the code is available, the trained datasets are made available only on "reasonable request". Given the importance of these datasets to evaluating the method and allowing others to benchmark it against other systems, these should be made available on GitHub. Overall, I would recommend toning down the comparison to DLC and focusing on the strengths of Squeakpose Studio on its own merits.

(4) The paper at times makes general statements that are beyond what is shown. For instance, discussions of use in human applications are aspirational and should be treated much more conservatively in the discussion, or possibly even removed. As it stands, the discussion implies that this system can already do "zero-shot tracking of human posture and movement", enabling "a bridge between preclinical and clinical behavioral analysis". In principle, this may be true, but even for a Discussion section, this goes far beyond the capabilities that the paper actually shows.

(5) While the comprehensive nature of the system and its 3 parts is impressive, I felt that it also detracted from the main focus of the paper, which was Squeakpose Studio. I might recommend dropping the other two parts, as they also require a much higher bar for a user to evaluate, and only present the Squeakpose Studio in this paper, presenting this as a general resource for pose estimation. This would also allow them more space to more comprehensively benchmark SqueakPose Studio.

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 #2 (Public review):

Summary:

In this manuscript, Coward and colleagues report on the role of insulin/IGF axis in podocyte gene transcription. They knocked out both the insulin and IGFR1 mice. Dual KO mice manifested a severe phenotype, with albuminuria, glomerulosclerosis, renal failure and death at 4-24 weeks.

Long read RNA sequencing was used to assess splicing events. Podocyte transcripts manifesting intron retention were identified. Dual knock-out podocytes manifested more transcripts with intron retention (18%) compared wild-type controls (18%), with an overlap between experiments of ~30%.

Transcript productivity was also assessed using FLAIR-mark-intron-retention software. Intron retention w seen in 18% of ciDKO podocyte transcripts compared to 14% of wild-type podocyte transcripts (P=0.004), with an overlap between experiments of ~30% (indicating the variability of results with this method). Interestingly, ciDKO podocytes showed downregulation of proteins involved in spliceosome function and RNA processing, as suggested by LC/MS and confirmed by Western blot.

Pladienolide (a spliceosome inhibitor) was cytotoxic to HeLa cells and to mouse podocytes, but no toxicity was seen in murine glomerular endothelial cells.

The manuscript is generally clear and well-written. Mouse work was approved in advance. The four figures are generally well-designed, bars/superimposed dot-plots.

Methods are generally well described.

Comments on previous version:

Coward and colleagues have done an excellent job of responding to all the reviewer comments.

Reviewer #4 (Public review):

This report entitled "The insulin/IGF axis is critically important (for) controlling gene transcription in the podocyte" from Hurcombe et al is based on a mouse double knockdown of the IR and IGF1R and a parallel cultured mouse podocyte model. Insulin/IGF signaling system in mammals evolved as three gene reduplicated peptides (insulin, IGF-1, and IGF-2) and their two receptors IR and IGF1R that cross-react to variable extents with the peptides, are ubiquitously expressed, and signal through parallel pathways. The major downstream effect of insulin is to regulate glucose uptake and metabolism, while that of the IGF pathways is to regulate growth and cell cycling in part through mTORC1. The GH-IGF-1-IGF1R pathway regulates post-natal growth. IGF-2 signaling is thought to play a major role in regulating intrauterine growth and development, although IGF-2 is also present at high levels in post-natal life. Thus, one would anticipate that reducing IR/IGF1R signaling in any cell would slow growth and cell cycling by reducing growth factor and metabolic mTORC1-mediated and other processes including the splicing of RNA for protein synthesis.

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 #2 (Public review):

This study investigates the visual information that is used for the recognition of faces. This is an important question in vision research and is critical for social interactions more generally. The authors ask whether our ability to recognise faces, across different viewpoints, varies as a function of the orientation information available in the image. Consistent with previous findings from this group and others, they find that horizontally filtered faces were recognised better than vertically filtered faces. Next, they probe the mechanism underlying this pattern of data by designing two model observers. The first was optimised for faces at a specific viewpoint (view-selective). The second was generalised across viewpoints (view-tolerant). In contrast to the human data, the view-specific model shows that the information that is useful for identity judgements varies according to viewpoint. For example, frontal face identities are again optimally discriminated with horizontal orientation information, but profiles are optimally discriminated with more vertical orientation information. These findings show human face recognition is biased toward horizontal orientation information, even though this may be suboptimal for the recognition of profile views of the face.

One issue in the design of this study was the lowering of the signal-to-noise ratio in the view-selective observer. This decision was taken to avoid ceiling effects. However, it is not clear how this affects the similarity with the human observers.

Another issue is the decision to normalise image energy across orientations and viewpoints. I can see the logic in wanting to control for these effects, but this does reflect natural variation in image properties. So, again, I wonder what the results would look like without this step.

Despite the bias toward horizontal orientations in human observers, there were some differences in the orientation preference at each viewpoint. For example, frontal faces were biased to horizontal (90 deg) but other viewpoints had biases that were slightly off horizontal (e.g. right profile: 80 deg, left profile: 100 deg). This does seem to show that differences in statistical information at different viewpoints (more horizontal information for frontal and more vertical information for profile) do influence human perception. It would be good to reflect on this nuance in the data.

Comments on revisions:

I am happy with the response and changes to the comments in my review. The key findings from this study are: (1) that there is bias toward the use of horizontal information across all viewpoints for face recognition in humans using an old-new recognition task. (2) In contrast, the optimal information for matching faces varies as a function of viewpoint. The view-selective model shows horizontal information is dominant for frontal views and vertical information is dominant for profile views.

The data from the view-tolerant model is less easy to interpret as it doesn't fit with any theoretically plausible model of face recognition. It might be a useful model for a face matching task in which participants had to match unfamiliar faces across viewpoints. This might be a possible extension of the current work.

Nonetheless, I still think this is an interesting contribution to the literature.

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 #2 (Public review):

Summary:

This manuscript examines whether the theta-beta ratio as derived from EEG data relates to ADHD diagnoses. To do so, it performs a multiverse analysis across a large number of analytical choices, applied to a large EEG dataset, and corroborated in an additional validation set. The results overall show that the TBR is not a reliable indicator of ADHD diagnosis. In discussing the patterns of results across analytical choices, the authors also demonstrate some key points about what appears to be driving the ratio measures, noting that significant results appear to be driven by choices regarding aperiodic-correction and the use of individualized alpha frequencies, suggesting TBR measures can be affected by these features rather than reflecting theta and/or beta activity.

Strengths:

This manuscript addresses a clearly posed and important question in the literature, addressing a longstanding discussion on the relationship between TBR and ADHD, and uses a large dataset and an expansive analysis approach to provide a definitive answer. The strengths of the approach allow for a clear answer, providing a notable contribution to the field.

Weaknesses:

I find no notable weaknesses in the current manuscript nor any major issues that I think challenge the key findings of this manuscript.

Reviewer #3 (Public review):

Summary:

In this manuscript, Strzelczyk, Vetsch, and Langer tackle an incredibly important question in clinical neuroscience: the use of the theta/beta ratio as a biomarker of attention deficit hyperactivity disorder (ADHD). The theta/beta ratio is argued to be so reliable as an ADHD biomarker that, in the United States, the Food and Drug Administration has approved its use as a biomarker for ADHD diagnosis. However, there is mounting evidence that the theta/beta ratio is likely not really measuring the relative power between two oscillations - the theta rhythm and the beta rhythm - but rather reflects differences in a singular, non-oscillatory aperiodic process. In this very convincing study, Strzelczyk and colleagues take a "multiverse" analysis approach to show that aperiodic activity differences between healthy controls and people with ADHD are driving the apparent theta/beta ratio differences. While in a vacuum, where a measure is a measure and if it's related to a diagnosis it's still useful no matter what, this distinction might not seem important, from a neuroscientific perspective this is a critical distinction, because the ratio between two oscillations has fundamentally very different underlying physiological mechanisms than aperiodic differences, and this framing has a major impact on guiding research on the diagnosis and treatment of ADHD.

Strengths:

While smaller studies and analyses have already hinted at similar results as shown here, the current study's multiverse analysis approach is comprehensive, convincing, and very well done. The large sample size of 1,499 participants is very impressive, as is the use of an independent validation sample of 381 participants.

Overall, the technical and statistical aspects are very well done: the multiverse approach, the validation set, the resampling methods, and even the shiny apps. The authors should be applauded for being so thorough and making their data and analyses publicly accessible.

Weaknesses:

To be clear, I see no breaking weaknesses in the theoretical foundations, methods, statistical analyses, or interpretations.

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 #2 (Public review):

Summary:

This study describes the development of GPR52-1.0, a novel genetically encoded fluorescent sensor for the orphan GPCR, GPR52. The authors also utilized this sensor in vivo in brain slices and discovered that striatal neuron excititation may activate GPR52.

Strengths:

(1) The design and validation of the sensor are elegant, thorough, and rigorous. The authors conducted a systematic and impressive optimization screen of numerous variants to arrive at the top-performing GPR52-1.0 sensor. The subsequent characterization is thorough, showing excellent membrane trafficking, appropriate pharmacological profiles (EC50, IC50) by the GPR52 chemical agonist/antagonist, rapid kinetics, and high specificity against a panel of common neurotransmitters. The functional characterization was also performed in multiple experimental systems.

(2) The most exciting result is the observation that electrical stimulation may activate GPR52 in the striatum, an area where GPR52 is natively expressed. The blockade by a specific GPR52 antagonist confirms its specificity and provides the first direct evidence for activity-dependent, native GPR52 ligand in striata. This finding alone is a significant step forward and strongly justifies the sensor's development.

(3) The manuscript is well-written and logically structured. The figures are clear and effectively illustrate the key data, from the initial screening process to the final ex vivo validation. The authors did not overstate their discoveries.

Weaknesses:

(1) The sensor specificity is largely based on a single agonist/antagonist, and it might be desired for future studies to confirm this by additional agonists/antagonists or by point mutagenesis that is known to influence GPR52 activation (for example, the ones reported in (PMID: 40087539).

(2) The discovery of the existence of activity-dependent, native GPR52 ligand(s) in striata is extremely exciting. This might be further strengthened by inhibiting synaptic transmitter release with TTX, calcium channel blockers, or SNARE complex disruptors, etc.

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 #2 (Public review):

Summary:

Overview of questions being answered and study design: The authors have used a knock-in mouse model to explore late in life amyloid effects on sleep. This is an excellent model as the mutated genes are regulated by the endogenous promoter system. The sleep study techniques and statistical analyses are also first rate.

The group finds an age-dependent increase in motor activity in advanced age in the NLGF homozygous knock-in mice (NLGF), with a parallel age dependent increase in body temperature, both effects predominate in the dark period. Interestingly the sleep patterns do not quite follow the sleep changes. Wake time is increased in NLGF mice and there is no progression in increased wake over time. NREMS and REM sleep are both reduced and there is no progression. Sleep wake effects, however, show a robust light:dark effect with larger effects in the dark period. These findings support distinct effects of this mutation on activity and temperature and on sleep. This is the first description of the temporal pattern of these effects. NLGF mice show wake stability (longer bout durations in the dark period (their active period) and fewer brief arousals from sleep. Sleep homeostasis across the lights on period is normal. Wake power spectral density is unaffected in NLGF mice at either age. Only REM power spectra are affected with NLGF mice showing less theta and more delta. There are interesting sex differences with females showing no gene difference on wake bout number, while males show a gene effect. Similarly, gene effects on NREM bout number seems larger in males than in females. Although there was no difference in homeostatic response there was normalization of sleep wake activity after sleep deprivation.

Strengths:

Approach (model extent of sleep phenotyping), analysis

Weaknesses:

Summarized below. Viewed as "addressable."

(1) The term insomnia. Insomnia is defined as a subjective dissatisfaction with sleep, and that cannot be ascertained in a mouse model. The findings across baseline sleep in NLGF mice support increased wake consolidation in the active period. The predominant sleep period (lights on) is largely unaffected, and the active period (lights off) shows increased activity and increased wake with longer bouts. There is a fantastic clue where NLGF effects are consistent with increased hypocretinergic (orexinergic) neuron activity in the dark period, and/or increased drive to hypocretin neurons from PVH.

(2) Sleep-wake transitions are impaired: This should not be termed an impairment. Could actually be beneficial to have greater state stability especially wake stability in the dark or active period. There is reduced sleep in the model that can be normalized by short-term sleep loss. It is fascinating that recovery sleep normalized sleep in the NLGF in the immediate lights on and light off period. This is a key finding.

Comments on revised version:

An important point has been missed but otherwise authors have been responsive:

The sleep predominant period for APPnlgf mice has few abnormalities in the predominant sleep (lights on) period to warrant "insomnia" as the descriptor, and this is an important point. Traditionally in dementias, there has been an emphasis to study insomnia as sleep is important for brain health and the night disturbances disturb caregivers as well, but a point that is not clearly emphasized is that this work is consistent with a new consideration in Alzheimer's and dementia sleep research that there may be early on in disease a hyperactivity of wake promoting neurons (orexin or locus coeruleus neurons), that contributes to the phenotype (maybe as "sundowning', agitation in the wake periods, but is also important to understand. Thus, it should be at least acknowledged that this may represent abnormal wake rather than a primary sleep abnormality. There is a new preprint by the Weinshenker group that demonstrates increased locus coeruleus activity in a tau model.

Reviewer #3 (Public review):

Summary:

In this study, Tisdale et al. studied the sleep/wake patterns in the biological mouse model of Alzheimer's disease. The results in this study together with the established literature on the relationship of sleep and Alzheimer's disease progression, guided authors to propose this mouse model for the mechanistic understanding of sleep states that translates to Alzheimer's disease patients. However, the manuscript currently suffers from a disconnect between the physiological data and the mechanistic interpretations. Specifically, the claim of "impaired transitions" is logically at odds with the observed increase in wake-state stability or possible hyperactivity. Additionally, the description of the methods, quantification and figure presentation need substantial improvement. Without going over all the flaws and ways to improve the paper, I am pointing out some of my concerns below.

Strengths:

Selection of the knock-in model is a notable strength as it avoids the artifacts associated with APP overexpression and more closely mimics human pathology. The study utilizes continuous 14-day EEG recordings, providing a unique dataset for assessing chronic changes in arousal states. The assessment of sex as a biological variable identifies a more severe "insomniac-like" phenotype in females, which aligns with the higher prevalence and severity of Alzheimer's disease in women.

Weaknesses:

The study seems to lack a clear hypothesis driven approach and relies mostly on explorative investigations. Moreover, lack of quantitative analytical methods as well as shaky logical conclusions, possibly not supported by data in its current form, leaves room for major improvement effort.

Since this paper studied sleep states, the "Methods" section is quite unclear on what specific criteria were used to classify sleep states. There is no quantitative description of classifying sleep based on clear reproducible procedures. There are many reasonably well characterized sleep scoring systems used in rat electrophysiological literature which could be useful here. The authors are generally expected to describe movement speed and/or EMG and/or EEG (theta/delta/gamma) criteria used to classify these epochs. The subjective (manual) nature of this procedure provides no verifiable validation on accuracy and interpretability regarding the results.

One of the bigger claims is that "state transition mechanism(s)" are impaired. However, Figure 7 shows that model mice exhibit significantly more long wake bouts (>260s) and fewer short wake bouts (<60s). Logically, an "impaired switch" (the flip-flop model, Saper et al., 2010) results in state fragmentation. The data here show the opposite: the wake state has become too stable. This suggests the primary defect is not in the transition mechanism itself, but possibly in a pathological increase in arousal drive (hyper-arousal), likely linked to the dark-phase hyperactivity shown in Figures 4 and 5. Also, point to note is that this finding is not new.

Figure 3 heatmaps lack color bars and units. As per eLife standards, spectral power must be quantitatively defined and methods well explained in the Methods section. Without these, the reader cannot discern if the "reduced power" in females is a global suppression of signal or a frequency-specific shift. Additionally, the representative example used to claim shorter sleep bouts lacks the statistical weight required for a major physiological conclusion. How does cooler color (not clear what range and what the interpretation is) mean shorter sleep bout in female mice? Authors should clearly mark the frequency ranges that support their claims. In this figure, there is a question mark following theta/delta range. Authors should avoid speculation and state their claims based on significant results. Please, also add the theta and delta ranges in the plot such that readers can draw their own conclusions.

Figure 8 and the MSLT results show that model mice are "no sleepier than WT mice" and have a functional homeostatic rebound. This presents a logical flaw in the "insomnia" narrative. True insomnia in AD patients typically involves a failure of the homeostatic process or a debilitating accumulation of sleep debt. If these mice do not show increased sleepiness (shorter latency) despite ~19% less sleep, the authors might be describing a "reduced need" for sleep or a "hyper-aroused" state, possibly not a clinical insomnia phenotype.

In Figure 9 LFP power shown and compared in percentages is problematic, as the LFP power distribution is known to be skewed (follows power law). This is particularly problematic here because all the frequencies above ~20 Hz seem to be totally flattened or nonexistent, which makes this comparison of power severely limited and biased towards the relative frequency in the highly skewed portion of the LFP power spectrum i.e very low frequency ranges like delta, theta and possibly beta. This ignores low, mid and high gamma as well as ripple band frequencies. NREM sleep is known to have relatively greater ripple band (100-250 Hz) power bursts in hippocampal regions and REM sleep are known to have synchronous theta-gamma relationships.

Comments on revised version:

The revised manuscript has made some improvements specifically in presentation of results as well as revising the title. However, more broadly authors have failed to address most of the concerns raised in the original review. As an example, the sleep scoring system is still subjective without any quantifiable and reproducible criteria. Another instance is regarding fig 9 comments, in which authors failed to address any of the raised concerns and reiterated their results. Hence, in the current form the results in the paper are incomplete with only partial support from the methods and evidence.

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 #2 (Public review):

The paper by Freas and Wystrach is an interesting computational study, exploring the detailed mechanisms of how simple neural circuits could explain complex behavioral patterns observed in navigating ants. The authors compare detailed, high speed video recordings of Australian desert ants (Melophorus bagoti) with predictions made by their new computational model and find convincing similarities between the model and the behavioral data, at a level of detail not previously studied. Particularly interesting are emerging properties of the model, yielding behavioral motifs it was not designed to reproduce, but which occur in natural ant behavior.

A strength of the study is that the model is based on previous models, without making major novel assumptions. It combines existing models of the insect central complex with a model of the lateral accessory lobe and adds a stochastic inhibition of forward velocity to the interaction of central complex and lateral accessory lobes. In essence, the central complex provides corrective steering signals when the goal direction and the current heading of the insect are not aligned, while the lateral accessory lobes provide an intrinsic oscillator underlying the behavioral oscillations shown by walking ants at all times. These background oscillations are modulated by the steering signals from the central complex. Depending on which phase of the intrinsic oscillations coincides with the corrective signals, and how fast the ant is moving forward during this time, a complex set of behaviors emerges.

Most prominently, scanning behaviors, which are regularly carried out by the ants, are recapitulated in great detail by the model. Additionally, other behaviors, such as full loops, emerge naturally from the model. While computational models are not to be seen as definite evidence for any biological reality, they can provide strong support for particular neural implementations. The current study is an excellent example in that it provides evidence for a serial arrangement of central complex circuits upstream of the lateral accessory lobe circuits, modulated by speed regulating input. While the latter is hypothetical, it yields a clear hypothesis that can be validated by connectomics studies and functional work in the future.

The computational model is explained in detail and information about all model parameters is provided in an accessible way. The approach is thus transparent and reproducible, leaving it to the readers to assess the assumptions made in the model and how the studied complex behaviors emerge. This also provides the possibility to combine this new model with existing models to expand the scope and to more comprehensively capture the behavioral repertoire of ants, and insects in general.

Importantly, the study shows that even complex behavioral motifs do not require dedicated neural modules, but can rather emerge from the interplay of already known circuits - highlighting the efficiency of insect brains and possibly providing the path towards embodied hardware solutions of such circuits in autonomous agents.

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 #2 (Public review):

Medial superior olivary neurons are sensitive to interaural time differences in the microsecond range, and many cellular mechanisms have been advanced to explain this temporal sensitivity. This study provides experimental and computational evidence for a new mechanism in which a range of asymmetric dendritic delays permits individual MSO neurons to represent the full range of biologically relevant ITDs. Using elegant 2-photon guided simultaneous recordings from distal dendrite and soma, along with compartmental modeling on anatomically reconstructed neurons, the authors provide compelling evidence that this mechanism contributes to microsecond-level tuning. The experimental design, analyses, and narrative are all well-crafted. It's a beautiful study. As outlined below, I have two general questions about interpretations drawn from the experimental data and modeling.

(1) Both excitatory and inhibitory synapses on MSO neurons display significant short-term depression (Couchman et al., 2010). Given the amount of attenuation at the soma, the role that the distal inputs would play after stimulus onset has not been tested. Were simulated EPSC pulse trains with endogenous short-term plasticity kinetics injected into distal dendrites? If not, were EPSP and IPSP trains with endogenous short-term plasticity kinetics studied in the model? The fundamental question is how much distal synapses contribute to somatic spike initiation as a function of synaptic pulse number.

(2) The model provides a credible line of evidence that synaptic inputs from distal and tertiary compartments can generate reliable increases in the time of arrival at the soma. It would be relatively simple to sequentially prune dendritic compartments to address how the time difference at which the maximal firing rate scales with tertiary or distal compartments. Similarly, one could eliminate the primary dendrites to determine whether or not they play a functional role. I would expect these chores to be largely confirmatory, but since EPSP delay and amplitude are convolved, it would increase confidence in the interpretation.

(3) Two technical questions. The age range is fairly broad, and it is not clear at which ages the experimental recordings were obtained, especially for the key experimental graphs that show correlations between delay (Figure 1d) or tau (Figure 2e) and distance. In addition, age could be added to Supplementary Figure 1, and the data could be ordered from youngest to oldest. Second, the Methods section indicates that brain slices were gradually cooled to 25 {degree sign}C, but should specify whether or not the recordings were obtained at this temperature.

Reviewer #3 (Public review):

Summary:

The study addresses how mammalian medial superior olive (MSO) neurons generate the internal delays required for interaural time difference (ITD) coding and sound localization. The authors demonstrate that dendritic morphology, particularly asymmetry between lateral and medial dendritic arbors, contributes to differential EPSP propagation delays and thereby shifts the optimal ITD of individual MSO neurons, using two-photon-guided paired dendritic and somatic recordings with compartmental modeling. This is a strong and potentially impactful manuscript. The work provides compelling evidence that dendritic morphology contributes to coincidence detection and ITD tuning in MSO neurons.

Strengths:

A major strength of the study is its technically rigorous combination of experimental electrophysiology, detailed neuronal reconstructions, and computational modeling. The use of paired dendritic and somatic recordings provides direct physiological insight into EPSP propagation, while the modeling approach allows the authors to test how cell-specific morphology influences coincidence detection. The analysis of multiple reconstructed MSO neurons further supports that dendritic asymmetry generates differential EPSP propagation delays that contribute to ITD tuning. This is a novel and potentially important mechanism that may complement classical axonal delay-line models. The study is strong in its anatomical and electrophysiological approach.

Weaknesses:

No major weakness. However, some aspects of the methods and interpretation would benefit from clarification. First, the assumptions used in the compartmental models should be more explicitly described, including the distribution of glutamatergic synaptic inputs and synaptic conductance parameters. It would be useful to clarify whether excitatory inputs were assumed to be homogeneously distributed along primary and higher-order dendritic branches or assigned based on known MSO input organization. Anatomical validation using VGluT staining together with dendritic labeling could strengthen the physiological relevance of the modeled input patterns. Second, the morphological analysis is informative, but additional measures of dendritic complexity could further support the conclusions. In addition to path length and membrane surface area, analyses of primary neurite number, branch points, and terminal arbors, using Sholl profiles or fractal dimension, could provide a more comprehensive assessment of lateral-medial dendritic asymmetry.

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 #2 (Public review):

Summary:

This manuscript investigates the protein composition and functional role of the C2a projection of the central apparatus (CA) in vertebrate motile cilia. Using three knockout mouse models (Ccdc108, Mycbpap, and Cfap70), the authors demonstrate that these genes - homologs of Chlamydomonas FAP65, FAP147, and FAP70 - are required for normal motile cilia function in ependymal and tracheal multiciliated cells. Specifically, the authors show that:

(1) Knockout mice for each gene exhibit primary ciliary dyskinesia phenotypes (hydrocephalus and sinusitis), accompanied by abnormal ciliary motion and reduced ciliary beat frequency.

(2) CCDC108, MYCBPAP, and CFAP70 physically interact and localize to the axonemal central lumen, consistent with the C2a projection.

(3) Loss of any one of these proteins destabilizes the others and disrupts CA integrity in a tissue-specific manner.

(4) ARMC3 and MYCBP are C2a-associated proteins.

Strengths:

(1) Clarity: the results are presented in a coherent sequence that facilitates understanding of both the rationale and conclusions.

(2) Genetic rigor: three independent knockout mouse lines that exhibit consistent motile cilia phenotypes provide in vivo support for the proposed role of these proteins.

(3) Integration of structural and functional analyses: combination of ultrastructural (TEM) and immunofluorescence data with CBF measurements provides convincing correlation between structural defects and impaired ciliary function.

(4) Mutual dependency model: reciprocal destabilization of CCDC108, MYCBPAP, and CFAP70 supports their interdependence in the C2a assembly.

(5) Expansion of the vertebrate C2a proteome: the identification of ARMC3 and MYCBP as C2a-associated proteins provides a foundation for future mechanistic studies.

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 #2 (Public review):

Summary:

Gaurav et al. investigate residue-level interactions within the MUT-16 FFR condensate using all-atom molecular dynamics simulations. The authors first argue, based on sequence analysis, that MUT-16 FFR is more representative than the widely studied FUS LCD. They then characterize the UCST phase behavior of MUT-16 FFR experimentally, followed by a detailed analysis of residue-level contact frequencies and lifetimes. In addition, the manuscript examines ion-residue interactions and water-mediated interactions. Overall, this work provides a comprehensive view of the dynamic interactions within the MUT-16 FFR condensate.

Strengths:

Large-scale all-atom molecular dynamics simulations have been performed to investigate dynamical interactions within condensates. The analysis is comprehensive and rigorous, and the claims are strongly justified by the data.

Weaknesses:

The large amount of detail in the results section sometimes makes it difficult to identify the central take-home messages. I encourage the authors to more clearly highlight the principal findings and the physical insights that may generalize to other condensate-forming systems. The authors may also consider streamlining parts of the Results section to improve focus and readability.

Reviewer #3 (Public review):

Summary:

The authors aim to characterize the molecular interaction network inside phase-separated condensates formed by the MUT-16 foci-forming region (FFR), using atomistic simulations combined with residue-resolved analyses of contact frequencies, contact lifetimes, specific non-covalent interactions, ions, and water.

Strengths:

The work addresses an interesting and biologically relevant system, and the combination of large-scale atomistic simulations with an extensive contact analysis has clear potential value for the broader condensate field.

Weaknesses:

In its current form, several technical issues need to be addressed before the main conclusions can be considered robust. Most importantly, the simulated sequence is 172 residues long, while the atomistic slab has box dimensions of only 12 nm in two directions. This length scale is comparable to the expected end-to-end distances of a disordered 172-residue chain. It is therefore not clear whether individual protein chains interact with their own periodic images, which could substantially affect overall chain dynamics and subsequently bias contact lifetimes, residue-residue interaction statistics, and the inferred condensate dynamics. The authors should check, for each chain, histograms of end-to-end distances. For chains for which more than ~2-3% of the end-to-end distances exceed ~11 nm, the authors should explicitly check for self-image interactions (for example, using "gmx mindist -pi") and report whether such interactions occur and for what fraction of the trajectory. Without this control, at least in the Supporting Information, I do not think the simulation-derived contact dynamics are sufficiently trustworthy.

A second major concern is the treatment of ions. The manuscript makes important conclusions about Na⁺ association and Na⁺-mediated bridging, but the atomistic ion model is not explicitly stated. This is a reproducibility problem and also affects interpretation - for example, standard Amber ions are known to bind too strongly to the oppositely charged residues. In their results, one acidic residue appears to interact on average with roughly two Na⁺ ions, which is not obviously expected from charge balance alone. The authors should state the exact Na⁺/Cl⁻ parameters used, justify their compatibility with TIP4P-D and the protein force field, and explicitly interpret why such a strong Na⁺ association with acidic residues is observed.

More generally, because the manuscript is centered on contact lifetimes, the choice of the atomistic force field needs stronger justification. Salt bridges, cation-pi contacts, pi-pi stacking, ion coordination, and water-mediated interactions are all force-field-sensitive. Since there is no direct experimental observable used here to validate the simulations, the authors should discuss the expected limitations of the chosen force field (while I do acknowledge that testing different force fields would be computationally too demanding).

I also find the sequence-comparison section somewhat confusing. The authors compare one specific IDR, MUT-16 FFR, with the average properties of human IDRs and then frame it as more representative than FUS LCD. It is not clear how informative this is because IDR behavior depends strongly on sequence-specific patterning, molecular connectivity, and the particular interaction network of each protein. Averages over human IDRs may provide a broad context, but they do not necessarily define what is physically or biologically representative for phase separation. In addition, FUS LCD is not intended to be a representative human IDR; it is an unusually low-complexity, phase-separating domain. Therefore, the "more representative than FUS" framing should be toned down. At most, this analysis shows that MUT-16 FFR is compositionally less extreme than FUS LCD.

The ion- and water-bridging analyses are also potentially overinterpreted. A distance-based simultaneous contact with two residues does not by itself establish functional mediation or regulation of condensate dynamics. The authors should either add appropriate controls, such as local-density-normalized baselines or randomized-contact expectations, or soften the language to describe these as geometrically defined co-contact events rather than mechanistic bridging interactions.

Finally, the independence of the atomistic replicas is unclear. The manuscript should state whether all ten all-atom simulations were initiated from the same coarse-grained condensate configuration or from distinct CG frames. If the starting structures came from one CG trajectory, the authors should report how far apart those frames were in simulation time and provide evidence that the initial atomistic configurations are structurally independent. If only velocities differ, the simulations should not be described as fully independent structural replicas.

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.

Reviewer #2 (Public review):

Summary:

This population-based cohort study found no evidence that physical activity, whether self-reported or objectively measured, positively influenced brain structure (hippocampal volume or BrainAGE) or cognitive function (Trail Making Test scores). Notably, longitudinal analyses suggested the opposite temporal relationship: a higher BrainAGE at baseline predicted higher physical capacity at follow-up, more in line with reverse causation rather than a neuroprotective effect of physical activity.

Strengths:

The study's statistical approach is thorough and well documented, and the inclusion of two measurements of physical activity (self-report questionnaire and objective accelerometer data) is a strength. The longitudinal aspect also represents a strength.

Weaknesses:

Several aspects of the measurement timing warrant consideration. Physical activity was assessed over 7-day periods, creating a potential mismatch with (commonly less dynamic) brain outcomes examined (hippocampal volume, BrainAGE), which may reflect cumulative exposures over longer timescales. Additionally, the asynchronous measurement protocol (cognitive testing preceding accelerometry, and the MRI occurring weeks after baseline visits) may introduce time lags that attenuate associations. The observed null associations may be influenced by timing misalignment rather than reflecting the absence of consistent effects of physical activity on brain health and cognition.

Other measurement characteristics also warrant consideration when interpreting the null findings. Physical activity was assessed using short-form self-report questionnaires and averaged accelerometer MET/day values, both of which have limited reliability. Additionally, the modest accelerometer subsample size and low/insufficient variation in activity levels observed in this cohort increase the likelihood of missing effects. These factors collectively raise the possibility that true physical activity-brain health associations may have been obscured.

The study's conclusions regarding brain health, structure, and cognitive functioning are broad despite the scope of the selection of outcomes examined. The analyses focus on hippocampal volume, BrainAGE (a global aging metric), and Trail Making Test performance (processing speed and executive function), while omitting other important neuroimaging markers such as cortical thickness, functional connectivity, or white matter microstructure. The null findings presented here cannot exclude positive effects of physical activity on broader constructs of brain health or cognitive functioning.

While the authors appropriately note the use of different physical activity instruments across time points (IPAQ at baseline, VSAQ at follow-up) in the limitations section, the discussion should more explicitly address the interpretive challenges this creates. The observed association between higher baseline brain age gap and lower follow-up physical activity may reflect: (1) a true temporal relationship, (2) an artifact of switching from behavior-focused (IPAQ) to capacity-focused (VSAQ) measurement, or (3) some combination of both. This ambiguity substantially limits causal inference.

Comments on the revised version:

I have briefly reviewed the responses to the reviewer comments, as well as the tracked changes in the expanded limitations section of the revised manuscript, and these adequately address my previous concerns.

Joint Public Review:

Summary:

Lengyel et al. present a normative model of single-neuron activity in area MT, which is known for its role in processing visual motion. The authors focus on responses to a center and a surround that move at different velocities. Both the center and surround are rigid: picture a set of dots all moving at the same velocity. The center dots are arranged in a disc; the surround dots in an annulus, and in both cases, the velocity of each is time-varying.

The core proposal is that the brain does not process motion in a fixed coordinate system, but instead infers a latent reference frame, and that MT neurons encode motion either in retinal coordinates or relative to this inferred reference frame. The model is meant to overcome a challenge in the existing literature on area MT: on the one hand, experimental findings are heterogeneous, including both surround suppression and surround facilitation of neural responses; on the other, existing models are either designed ad hoc to capture specific phenomena or they are somewhat general (e.g., divisive normalization), but in either case they can't explain the full range of responses. This manuscript proposes that the full range of responses in MT is explained as Bayesian inference over the reference frame in which center motion speed and direction should be estimated. The model extends one introduced in a previous publication from the same lab (Shivkumar et al. 2025). That publication focused on human perception of motion; this one makes predictions about MT mean responses and across-trial variability.

Strengths:

Processing visual motion is important for normal visual function, including for the integration and segmentation of visual objects. This manuscript presents a normative theory, supported by recent human perceptual data, and extends it to make predictions about neural firing rate and variability in area MT. The theory is well motivated and supported by the simulation analysis and comparison to data. It provides new insight into how causal inference of relative motion reference frames can modulate neural activity in MT. The richness of the theory's prediction can guide future experiments. In particular, the theory explains both center-surround suppression and facilitation, unifying disparate empirical observations in MT for which no unified explanation had been proposed. The manuscript also demonstrates a new method to map ideal observer predictions (posterior distributions over speed and direction, which are dependent on the posterior inference over reference frames) onto predicted neural activity for center-surround stimuli, by only considering basic tuning curves measured in the center-alone condition. This is a useful methodological contribution. The manuscript offers a thorough review of CS modulation studies in MT.

Weaknesses:

We found this paper difficult to read for two reasons. First, math is generally explained in words. This made it extremely difficult (impossible for some reviewers) to understand the details of the model, which are important. We're not against words, but it's critical that they be accompanied by equations.

Second, the manuscript is not self-contained in the sense that many of the motivations, assumptions, and limitations of the approach are only evident if one carefully reads the groups' prior work, Shivkumar et al. (2025). Following up on previous work isn't necessarily a flaw, but the introduction of the paper is written from a very broad perspective that does not effectively summarize the prior work and lay out the specific questions that motivate the current study. For example, it is not clear from the introduction whether the authors believe this framework can explain all sorts of center-surround interactions (including in non-motion stimuli and in other areas like the retina), or if the focus is only on area MT.

Finally, the connection to neural data is confusing and mostly qualitative. The authors create a library of "hypothetical but plausible tuning curves" and show that their modeling framework is flexible enough to capture a variety of center-surround interactions. Although they do state that their model can't explain all possible tuning curves, it's still hard to tell whether they have particularly strong evidence for the Bayesian causal inference hypothesis.

We also have several technical, but potentially important, comments.

Line 427: 'Our framework not only reinterprets past findings but also generates new, testable predictions. The model makes directly testable predictions for surround modulation. Facilitation, for instance, is predicted for neurons encoding retinal-centric motion (v_center) under high sensory uncertainty. In contrast, suppression is the hallmark of neurons encoding relative motion (v^relative_center) with respect to a surround-influenced reference frame.' It seems that to test the predictions of the model, one would need to first determine if a neuron encodes retinal or relative motion, without relying on the patterns predicted by this model, and then test if the two types of neurons behave as predicted. It is unclear how one can obtain this labeling of neurons independently of the model predictions.

Line 492: 'This offers a principled account of how the same population of neurons can support both perceptual states (integration and segmentation)'. However, because the theory assumes each neuron encodes either center velocity or center velocity relative to a moving reference frame, but not both, it does not explain that the same neuron could shift from suppression to facilitation. It may be worth considering another possibility, using V1 surround modulation as an analogy. Different neuron types are required to implement the surround computation: in mouse V1, SST interneurons are surround-facilitated, and they are necessary to implement surround suppression of pyramidal neurons https://pmc.ncbi.nlm.nih.gov/articles/PMC3621107, but their (SST) outputs are not communicated to downstream targets. In that view, facilitation is therefore not a signature of some neurons encoding a type of latent variable; it is only there as an intermediate step in the computation of the other latents (those that require suppression).

Misspecification of either the prior or likelihood can be a problem for Bayesian inference. Discussion of this point -- and in particular evidence (say from analysis of natural scene statistics in the case of the prior) that both are well-specified -- would strengthen the manuscript.

Reviewer #1 (Public review):

In this work, Jiqi Shao and colleagues evaluate the microbial iron competition and siderophore-mediated interactions combining (a) a dynamic modeling framework based on the consumer-resource model, including multiple siderophore and siderophore-receptor types, and (b) a graph-theory framework based on directed graphs to quantify the ecological dependencies of the community (referred to as Benefit Transfer Graph). Through a plethora of simulation experiments, by changing the number of species in the community, the ratio of pure-cheaters, and the number of foreign siderophores a partial-producers can utilize (referred to in this study as 'Cheating Breadth'), the authors found:

(1) Using simulations of small communities of 5 or fewer members, they observe that closed benefit-transfer loops (commensalism/mutualism loops) serve as the structural scaffold for diversity, observing coexistence, dominance, or dynamic fluctuations in function of the fraction of receptors in species and the number of community members.

(2) Using simulations of large communities of 50 members, they observed a paradox on the capacity of partial producers to utilize different foreign siderophores (referred to in this study as 'The Paradox of Cheating'). They observed that broad 'Cheating Breadth' of partial-producer members increases the probability of community-wide extinction and can act as destabilizing forces. However, at the same time, 'Cheating Breath' of partial-producer members promotes species richness and community biodiversity.

(3) The application of graph-theory framework helps to unveil ecological complexities of small and large microbial communities, explaining the aforementioned Paradox of Cheating.

As major strengths of this work, the authors present a novel modeling framework considering the ecological complexity of siderophore-mediated interactions by differentiating types of community members (pure-producers, partial-producers, and pure-cheaters), siderophore/receptor pairs, and exploring a wide range of situations (such as the number of community members, the ratio of pure-cheaters, or the siderophore breadth of partial-producers). Moreover, the discussion and conclusions of this study are mechanistically well-founded with a graph-theory framework (Benefit Transfer Graph). All computer code and scripts to replicate the simulations, analysis, and figure generation are public in the Zenodo repository.

However, this study still has some work to do before it meets the expected standards, presenting some weaknesses to be addressed. Please regard the following paragraph as constructive feedback aimed at improving your work. The main weakness of the actual version is the Abstract, the missing Methods section, the structure of the Results section, and the results displaying (i.e., Figures), and how partial-producers are considered as cheaters (including how they referred to the capacity of partial-producers to use different siderophores as 'Cheating Breath'). The Abstract could be significantly improved with a better introduction of the system (cooperators and cheaters, and the concept of the 'Tragedy of Commons'), a better description of the modeling framework, and other details included in 'Recommendations for the authors'. The current version of the manuscript misses a proper 'Methods' section.

Moreover, the authors could include (1) a section with the simulated systems and parameter choices of simulation experiments, (2) the key model assumptions, and (3) a separate (and more detailed) section explaining the graph-theory framework applied in this study (Benefit Transfer Graph). Most of this information is included in Supporting Information, but including it in the main text will facilitate the comprehension of the work. The structure of the results displayed (i.e., Figures) is quite confusing, especially in the section 'Closed Benefit Loops Drive Transitions from Exclusion to Coexistence and Chaos'. Moreover, important results are included in Supportive Information when they should be in the main text. Also, the lack of a proper Method section makes it harder to follow the Results sections. I have included some recommendations/suggestions to improve the Results structure. This study reveals an interesting ecological dynamic in siderophore-mediated interactions. The authors suggest the existence (and further explanation) of the 'Paradox of Cheating'. However, this paradox (and their discussion) may come from a misunderstanding of concepts and/or terminologies used by the authors applied here (and maybe widely applied in cooperator-cheaters systems). The authors refer to the capacity of 'partial-producers' to utilize foreign siderophores (i.e., siderophores of other species) as cheating. Also, they refer to the number of foreign siderophores that a 'partial-producer' can utilize as 'Cheating Breadth'. A microbial cheater is one that has receptors for siderophore uptake but does not pay the cost of producing siderophore themselves. Because 'partial-producers' are generating at least one type of siderophore, these are not technically cheaters (although they may act as 'pure-cheaters', changing their gene expression and do not synthesize any siderophore for the community). All this may entail a misleading of the results and a potentially overstated title and conclusions of this work. Community members 'pure-producers', 'partial-producers' cheaters may be called in a different way, e.g., 'single-receptor producer', 'multiple-receptor producers' and 'nonproducers', respectively [Gu. et al. (2025), doi: 10.1126/sciadv.adq5038]. A better terminology for 'the number of foreign siderophores that a partial-producer can utilize' could be 'Siderophore Breadth', and instead of stating a 'Paradox of Cheating', it can be a 'Paradox of Multiple-receptor Producers'. The discussion of the authors aligns better with the presented results if the proposed terms 'single-receptor producer/multiple-receptor producer and cheater' are used, considering multiple-receptor producers as cooperative members rather than 'moderate cheating'. On the other hand, the Paradox of Multiple-receptor Producers (or Paradox of Cheating by the authors) could be a modeling artifact. Although some species possess multiple siderophore receptors in their genome (some studies suggest that Pseudomonas species and other environmental strains' genomes can have up to 20-30 siderophore receptors), that does not mean that they are all expressed simultaneously.

Regardless of the weaknesses and the major points to be improved, the findings presented in this work substantially advance our understanding of complex ecological interactions between cooperators and cheaters mediated by siderophore and siderophore-receptor syntheses, especially when multiple-receptor producers are present. Moreover, the modeling and graph-theory frameworks presented by the authors can be applied in other microbial systems, such as collaboration/competition/cheating for substrates or nutrients. Fundamental modeling exercises are indispensable to unveil ground ecological rules of complex microbial communities, accelerating the advances in ecology by developing theory-based hypotheses for future experimental and environmental studies.

Reviewer #2 (Public review):

Summary:

This study investigates how cheating affects microbial diversity, using a chemostat model of a microbial community in which species compete for a shared iron pool through siderophore-mediated uptake. After analyzing minimal communities, the study simulates large randomly generated communities in which species either produce no siderophore or produce a single siderophore type. Producers can differ in siderophore type and production level, while all species can differ in the siderophore-specific receptor types they express. Siderophore production trades off with resource allocation to growth. Total receptor expression is normalized, so increasing expression of one receptor type reduces expression of other receptor types. A key parameter in these simulations is the average number of "cheating receptor types," i.e., receptor types that allow a species to use siderophores it does not produce itself. The authors use this parameter as one axis for characterizing cheating behavior and term it "cheating breadth." The results reveal a statistical pattern the authors report as a "paradox": increasing cheating breadth increases the frequency of whole-community extinction, but also increases the mean number of surviving species per non-extinct community. To explain this pattern, the study reduces a community's producer-receiver network into components by retaining only the link from each producer to its maximal beneficiary, i.e., the species receiving the largest growth benefit from that producer. The study finds that the core topology of such a component predicts the community's ecological fate, namely, extinction, single-species survival, or multi-species coexistence, when biomass is concentrated in that component. The study argues that increasing cheating breadth reduces the probability that a community contains components predicting single-species survival, while increasing the probabilities that it contains components predicting extinction or multi-species coexistence. This argument is used to explain why greater cheating breadth increases both community extinction risk and diversity. Based on these results, the study concludes that microbial diversity not only tolerates but requires moderate cheating.

Strengths:

The major strengths of this study are that it presents an interesting mathematical model of microbial interactions mediated by diverse siderophores and that it reduces simulation results to simple predictive patterns by focusing on one primary beneficiary per producer, as summarized above.

Weaknesses:

The study also has two major weaknesses. First, the observed diversity is not shown to be evolutionarily stable, which limits the biological relevance of the findings. The cycle structure that supports this diversity may be vulnerable to invasion by mutants that disrupt this structure and can thereby drive many species, or even the whole community, extinct. This concern is suggested by previous studies on the hypercycle, which is analogous to the cycle structure found in this study (Eigen and Schuster, The Hypercycle, Springer-Verlag, pages 32-57, 1979 https://doi.org/10.1007/978-3-642-67247-7). For example, a community with a cyclic network may be invaded by mutants that increase growth allocation at the cost of siderophore production (Maynard Smith, Nature 280:445-446, 1979 https://doi.org/10.1038/280445a0). It may also be destabilized by mutants that increase the expression of the "self-receptor," the receptor for the siderophore they produce themselves. Another possibility is a "short-circuit mutant" that expresses receptors in a way that bypasses intermediate species in a cycle (Bresch et al., Journal of Theoretical Biology 85:399-405, 1980 https://doi.org/10.1016/0022-5193(80)90314-8). Cyclic networks may remain evolutionarily unstable even when spatial self-organization is considered (Hogeweg and Takeuchi, Origins of Life and Evolution of the Biosphere 33:375-403, 2003 https://doi.org/10.1023/A:1025754907141). Without demonstrating robustness to these plausible evolutionary hazards, the study's coexistence results may have limited biological relevance.

The second weakness is that the study treats cheating breadth as if it were a pure measure of increased cheating, framing the observed pattern as a paradox that increasing cheating breadth increases diversity within surviving communities while also increasing community extinction risk. However, increasing cheating breadth decreases the mean expression level of all expressed receptors, a confounding effect that arises from the normalization of total receptor expression. Consequently, increasing cheating breadth also reduces the mean benefit a producer gains from its own siderophore production. In other words, increasing cheating breadth spreads each producer's dependence across diverse siderophores at the cost of a reduced return on the self-produced siderophore. Once these coupled effects are recognized, the reported pattern is less paradoxical: increasing cheating breadth might be expected to increase diversity within surviving communities by distributing dependence, while also increasing extinction risk by reducing self-reliance. Therefore, the apparent paradox may arise from the way cheating behavior is parameterized rather than from a direct effect of increased cheating alone.

Additional context:

The present study can be considered alongside previous studies proposing that cheating can, in some contexts, promote microbial diversity by generating ecological dependencies. The Black Queen hypothesis proposes that such dependencies can be created by adaptive gene loss and reliance on functions performed by other community members (Morris et al., mBio 3:e00036-12, 2012, https://doi.org/10.1128/mbio.00036-12). A related study by Fullmer et al. discusses how mutual cheating can contribute to microbial diversity (Frontiers in Microbiology 6:728, 2015, https://doi.org/10.3389/fmicb.2015.00728).

Reviewer #1 (Public review):

Summary:

One of the most important fundamental questions in base excision repair (BER) is how chromatin structure affects the action of specific components of the BER pathway. Previous work from this and other groups has began to address this question. In this report, the authors study the activity of Pol beta on a gapped or nicked DNA substrate 23 bases from the entry/exit site of a 603 nucleosome core particle in the presence and absence of PARP1, PARP2, HPF1, or FEN1. They show that H1 and PARP block pol beta incorporation, which is relieved by NAD+.

Strengths:

They show, not unexpectedly, that HPF1 and PARP activity help to displace H1, allowing Pol beta incorporation. PARP1 and PARP2 suppress Pol beta activity, which is mitigated by autoparylation. PARP2 has a strong impact on strand displacement synthesis. This is an important contribution to the field.

Weaknesses:

This present work incrementally builds upon their previous work, and what has been known previously about the activity of PARP1/2, HPF1, and the modification of histones.

Reviewer #2 (Public review):

Summary:

The authors have shown some interesting data on DNA repair synthesis by PolB, acting on a BER substrate in the presence of a core nucleosome, and the effects of some accessory chromatin proteins. FEN1 and PARP proteins were also assessed for their effects on repair synthesis by PolB. However, the story for the PARP proteins seems a bit underdeveloped, or perhaps it just needs additional clarity in the writing. The concept that strand displacement synthesis by PolB in linker DNA and into the NCP is limited by these interactions is useful, although we need to bear in mind that the study does not address the role of the final repair enzyme, DNA ligase, which might itself limit the products. Likewise, the possible effects of competing DNA polymerases remain unexplored, notably the replication enzymes delta and epsilon. There are circumstances where these appear to be the main DNA repair polymerases for BER substrates. Addressing these and other issues, as listed below, would greatly improve a paper that is already fairly strong.

Specific Points:

(1) Substrates:

The gap substrate was prepared by treating a U-containing substrate with UDG + APE1. Consequently, it is not exactly a gap, but a repair intermediate with a 5-abasic site on one side of the break. It should be described more clearly in the text.

The nicked substrate was prepared by incubating the "gap" substrate with PolB and dTTP, the nucleotide to replace the excised U. It is expected that this substrate has the 5'-abasic site removed by the PolB lyase, and only one dTMP residue inserted. Has either of these expectations been verified? For example, PolB can insert more than one nucleotide in a prolonged incubation, and the enzyme has no intrinsic 3'-exonuclease to trim the extension.

Finally, it appears that these procedures were performed with the NCP already in place; therefore, the presence of the nucleosome is expected to influence the processing done to prepare the gap and nick substrates. What do we know about that?

(2) Figure 1c:

The rate difference for gap vs. NCP is modest, perhaps 2-fold in the data shown. Some statistical analysis is needed to solidify this observation.

(3) As noted on page 4, the histone tails might be important for some of the observed effects. While individual histones had no effect, the critical test would be in the context of the NCP. There are many modified or mutant histones now available that would enable this. While such experiments would be more for future work, the possibility should be mentioned in this paper.

(4) What are the molar ratios of the various enzymes to the substrates? Can we say whether that reflects the levels that might be found in vivo? For the in vitro studies, the stoichiometry would also influence competing binding reactions. Indeed, Figure 2 indicates that the NCP substrate has multiple, competing binding sites for PolB. Why are the multiple NCP-PolB species not better resolved in EMSA (Supplementary Figure 2a)? Perhaps the higher-order ones are more unstable in the gel? That would be consistent with Table 1.

(5) Wouldn't the incremental 3-nucleotide steps seen with PolB + FEN1 be a relatively inefficient process? Of course, one expects that the presence of a DNA ligase would effectively limit this process to just one synthesis/excision cycle. Hasn't that been tested with these substrates?

(6) In many of the gel images, it can be hard to tell S from the +1 products, especially further from the side of the gel. Is there an independent way to verify that just a single nucleotide was replaced?

Reviewer #3 (Public review):

This manuscript by Shtanov et al. attempts to define how DNA Polymerase β performs gap-filling DNA synthesis and strand displacement synthesis in linker DNA adjacent to a nucleosome. The authors show that DNA Polymerase β strand displacement synthesis activity is stimulated in linker DNA when the 1-nt gap is positioned 23 bp away from a nucleosome core particle. The authors further show that histone H1, known to bind linker DNA, disrupts the ability of DNA Polymerase β to perform strand displacement synthesis within this context. They then provide some evidence that PARP1 and PARP2 regulate DNA Polymerase β strand displacement synthesis in linker DNA adjacent to a nucleosome, possibly pointing to a role for PARP1 and PARP2 in base excision repair sub-pathway choice. While this study has some intriguing observations, these observations are severely underdeveloped, and many of the stated conclusions are inadequately justified by the experimental data.

Strengths:

(1) The authors have identified that DNA Polymerase β strand displacement synthesis is stimulated in linker DNA by the presence of an adjacent nucleosome, though the generalizability of this finding is unclear (see weaknesses).

(2) The authors convincingly show that the presence of histone H1 negatively regulates DNA Polymerase β strand displacement synthesis in linker DNA adjacent to a nucleosome core particle.

Weaknesses:

(1) Throughout the manuscript, the authors perform a variety of enzyme kinetic assays to show that DNA Polymerase β strand displacement synthesis is stimulated in linker DNA by the presence of an adjacent nucleosome, and that other chromatin factors (PARP1, PARP2, and histone H1) regulate strand displacement synthesis. The enzyme kinetic experiments presented have several issues that severely impact their interpretability. This includes the lack of proper substrate controls, a general lack of quantification and statistical analysis, the use of varied enzyme kinetics regimes that impede comparison between experiments, and a general lack of clarity regarding experimental replication/reproducibility.

(2) The general context where an adjacent nucleosome core particle would stimulate DNA Polymerase β strand displacement synthesis is severely underdeveloped, which limits the generalizability of these findings. It's unclear if this stimulation is dependent on the linker DNA length, the distance of the 1-nt gap from the nucleosome core particle, or the directionality of strand displacement synthesis (towards vs away from the nucleosome core particle). Given the data presented, it's possible that stimulation of DNA Polymerase β strand displacement synthesis by an adjacent nucleosome is a phenomenon that is unique to a 1-nt gap precisely 23 nts away from the nucleosome core particle.

(3) The conclusion that the N-terminal histone tails do not stimulate DNA Polymerase β strand displacement synthesis comes from an experiment where Gap-DNA227 was incubated with free core histones, and a reduction in strand displacement synthesis was observed. As designed, this experiment is simply unable to prove that the N-terminal tails do not stimulate DNA Polymerase β strand displacement synthesis.

(4) The observation of apparent cooperativity in DNA Polymerase β binding to Gap-NCP227 from the mass photometry data is intriguing. However, the relationship between this observation and the stimulation of DNA Polymerase β strand displacement synthesis in linker DNA adjacent to a nucleosome core particle is unclear.

(5) The general claims regarding differential specificity of PARP1 and PARP2 for nicks and gaps in linker DNA adjacent to the nucleosome come from experiments lacking a proper control using an undamaged linker-nucleosome substrate. This is particularly problematic as PARP1 and PARP2 are known to engage the terminal ends of DNA as they partially mimic DNA double-strand breaks.

(6) While the authors clearly show that PARP1 and PARP2 regulate DNA Polymerase β strand displacement synthesis in linker DNA, the interpretation that this is through direct competition for 1-nt gap binding cannot be proven from the experiments presented.

(7) The claim that the presence of histone H1 changes the yield and length of PARylated core histones is overstated. The quantification would suggest a subtle difference (particularly for PARP1), but the lack of statistical analysis related to the experiments makes interpretation challenging.

Reviewer #1 (Public review):

This manuscript investigates the conformational flexibility and membrane-interaction behavior of the N-terminal segment of the VP4 protein from non-enveloped viruses, such as Coxsackievirus B3, with particular emphasis on the role of myristoylation, an essential process implicated in viral entry and transmission. The authors employ a multiscale simulation framework, combining all-atom (AA) and coarse-grained (CG) molecular dynamics simulations, to characterize the behavior of VP4 peptides in both bulk aqueous and membrane environments.

AA simulations suggest that the VP4 N-terminus remains predominantly disordered in bulk water, whereas CG simulations highlight the importance of conformational flexibility during interactions with a POPC membrane. The CG approach is further used to demonstrate an enhanced aggregation tendency of myristoylated VP4 monomers compared to non-myristoylated forms and to estimate the free-energy barriers associated with VP4 translocation across the membrane in monomeric and aggregated states. The study proposes a connection between VP4 aggregation, membrane remodeling, and peptide insertion into the membrane. Finally, well-tempered metadynamics simulations are used to explore changes in VP4 helicity during pore formation.

Overall, the study addresses an important problem and applies appropriate computational approaches. However, several aspects of the methodology, interpretation of results, and consistency with existing literature require clarification before the conclusions can be fully supported. The authors should revise the manuscript with due attention to the comments below.

(1) Disordered State of VP4 in Bulk Water

Figures 1(f-g, i-j) indicate that both myristoylated and non-myristoylated VP4 peptides adopt largely disordered conformations in bulk water. This finding appears to contradict prior experimental and computational reports discussed in the Introduction, which suggest partial or transient helicity in this region. A more detailed explanation is required to reconcile these differences with the existing literature. Additionally, since α-RMSD (aRMSD) is a direct and quantitative measure of helicity, the authors may consider reporting helical content explicitly using this metric to strengthen the analysis.

(2) Lack of Backmapped Atomistic Data for Membrane-Bound States

Figure 2 presents membrane-bound conformations of VP4 obtained from CG simulations. While this provides useful qualitative insight, the absence of backmapped all-atom representations limits the ability to extract detailed information regarding residue-level interactions, peptide conformations, and specific binding modes at the membrane interface. Inclusion and analysis of backmapped atomistic data would significantly strengthen the mechanistic interpretation of VP4-membrane interactions.

(3) VP4 Binding to Membrane

Figure 2(H): The key takeaway from the exercise using multiple different rigidity for the peptide was that the different sections of the peptide have reduced membrane contacts, particularly the N-terminus. However, the contribution from each membrane component is not very apparent due to stacked transparent plots. Re-plotting using bars placed side to side or using a line representation will help to make this clearer.

(4) Aggregation Stability in Bulk Versus Membrane Environments

The manuscript states that the aggregation rate and stability of VP4 20-mers in bulk water are weaker than in the presence of a membrane, as shown in Figure S5. However, no clear or significant reduction in aggregation stability is apparent from the figure as currently presented. The authors should clarify which quantitative metrics support this claim and, if necessary, provide additional analysis to substantiate the reported difference.

(5) Decoding the Role of MYR on the VP4 n-mer Aggregation

The authors have suggested that the MYR tail plays a key role in the recruitment of VP4 peptides into the aggregate. This is based solely on visual evidence from the simulation. This can be tested directly by using a combination of MYR and non-MYR VP4 molecules, with MYR VP4 acting as membrane anchors. The change in aggregation rate or the number of clusters will give a more complete picture of this phenomenon. In the case of 20 non-MYR VP4 peptides, the aggregate forms within 2 µs, which is comparable to the complete aggregation in the case of MYR-VP4 6-mer. This further brings into question whether the faster aggregation for MYR cases is due to the proximity to the membrane or due to the lipid recruitment aspect of the MYR group.

(6) Interpretation of Umbrella Sampling Results and Membrane Remodeling

Figure 4 reports CG umbrella sampling results indicating a reduced translocation free-energy barrier for VP4 in aggregated (condensate) form, which is linked to membrane curvature and remodeling. Additional methodological details are required to support this interpretation:<br /> (a) What is the nature of the membrane used in the umbrella sampling simulations? Specifically, was the membrane initially flat or curved, and was the same membrane (with identical curvature and properties) used for the single, 6-mer, and 20-mer cases? Differences in membrane geometry would directly influence the translocation free-energy profiles.<br /> (b) Additional details regarding the peptide models used in umbrella sampling simulations should be provided, including peptide length, aggregation state definition, restraints applied (if any), and reference configurations, to improve clarity.

(7) VP4 n-mer Condensate Dynamics

The authors have performed an autocorrelation analysis of Rg of VP4 in the 6 and 20-mer condensates and found that the decay is slower in the 6-mer. This suggests a higher degree of rearrangement within the VP4 20-mer. This could be due to a faster relaxation time upon formation for the 6-mer compared to the 20-mer owing to its smaller size. It would be informative to look at whether these differences still hold when the 20-mer simulations are extended beyond 10 µs.

(8) Comparison Between Metadynamics and Backmapped Membrane-Bound Structures

Figure 5 presents Well-Tempered Metadynamics results for VP4 in a membrane environment. To strengthen the conclusions regarding peptide binding and conformational behavior, it would be valuable to directly compare the peptide conformations and interaction characteristics observed in the Metadynamics simulations with those obtained from the backmapped structures corresponding to Figure 2.

(9) Interpretation of the Z-Coordinate in Free-Energy Profiles

Figure 5(a) shows the free-energy landscape of the VP4 peptide as a function of reaction coordinates. However, the corresponding Z-position of the peptide relative to the membrane is not clearly defined. The authors should clarify whether the reported Z-values correspond to peptide conformations at the membrane surface, within the hydrophobic core, or fully translocated across the membrane, as this is essential for proper interpretation of the free-energy minima.

(10) Helicity in Bulk Water from Metadynamics Simulations

Figure 5(b) shows a free-energy minimum at relatively high helicity (~0.6) even at a peptide-membrane distance of approximately 3.6 nm, which appears to correspond to a bulk-water-like environment. This observation contradicts the predominantly disordered peptide behavior reported in bulk water simulations (Figure 1). The authors should provide a mechanistic explanation for this inconsistency between the bulk AA simulations and the Metadynamics results.

(11) Folding and Insertion Free Energy of VP4

The free energy calculation for folding of VP4 using metadynamics in the POPC membrane and the 2D free energy calculated using umbrella sampling do not show the same picture. As in the first case, the deeper insertion into the membrane promotes a higher helicity, which is not present in the 2D free energy landscape. Assuming the same scale bar for the free energy between the two plots, as that is not mentioned for the free energy obtained from the metadynamics simulations, we see a massive preference towards a helicity fraction of >0.6. This is absent, both in the aqueous and the membrane-embedded environment of the 2D free energy simulations. It will also be useful to mention the plane of the phosphate groups to demarcate the hydrophilic and hydrophobic sections of the membrane

Final Recommendation

The manuscript presents interesting and potentially impactful findings on the conformational dynamics and membrane interactions of VP4. However, substantial clarification and additional analysis addressing the points above are required to ensure consistency, rigor, and alignment with existing literature. I recommend major revisions.b

Reviewer #2 (Public review):

Summary:

The authors Huang et al. studied how a small disordered VP4 protein present in the viral capsid of naked viruses, such as Coxsackievirus B3, enables the transfer of the viral genome into the host cell by breaching the host cell membrane. The authors show that post-translational myristoylation of VP4 plays a critical role in this process. Using computer simulations of VP4 and its interactions with the membrane, the authors show that myristoylated VP4 anchors to the membrane faster, aggregates faster to form dense phases via LLPS, and remodels the membrane, thereby lowering the energy barrier for the protein to insert into the membrane. The authors further showed, through simulations, that the myristoylated VP4 forms helices within the membrane with higher stability, which then form structured pores, disrupting the membrane and enabling the transfer of the viral genome into the host cell.

Strengths:

The strength of the manuscript is that different sets of unbiased and enhanced-sampling simulations using all-atom and coarse-grained models of the protein and membrane are performed to bridge multiple time and length scales involved in the transfer of the viral genome into the host cell. There is experimental support for most of the conclusions arrived at from the simulations.

Weaknesses:

The drawback is that experimental evidence was lacking to support the pore-formation proposal from the simulations.

Reviewer #1 (Public review):

Summary:

The authors utilize genetic code expansion to tag TDP-43 and G3BP1, and evaluate this protein tagging system (ANAP) compared to antibodies and evaluate protein trafficking and stress granule formation in response to stress with sodium arsenite treatment. They find similar staining to antibodies in HeLa cells, mouse embryonic stem cells and primary mouse cortical neurons. By incorporating the intrinsically fluorescent noncanonical amino acid Anap at carefully selected sites, the authors enable live-cell and neuronal visualization of protein localization, stress-induced redistribution, and dynamic behavior without the structural and functional compromises often associated with large fluorescent protein tags. The work provides technical framework that will be useful for live imaging of tagged proteins.

Strengths:

A key strength is the demonstration of the specificity of the Anap fluorescence signal through appropriate controls and the agreement between Anap labeling and antibody-based detection across multiple cell types, including primary neurons. The ability to visualize stress-induced redistribution of both G3BP1 and TDP 43 in living cells highlights the practical value of this approach.

The functional validation of TDP 43-Anap is compelling. The rescue of both cell viability and RNA splicing defects in TDP 43 knockout models provides evidence that Anap incorporation preserves core protein functions. This is important, as functional disruption is a central concern for any alternative tagging strategy applied to aggregation-prone or RNA-binding proteins.

Weaknesses:

While some inherent limitations of genetic code expansion remain (e.g., variable amber suppression efficiency and the inability to directly assess endogenous protein behavior), these are acknowledged and discussed appropriately. Importantly, these limitations do not undermine the central contributions of the study.

Reviewer #2 (Public review):

In this manuscript, Chen and colleagues describe a novel means of labeling two RNA binding proteins, G3BP1 and TDP-43, using genetic code expansion. Overexpressed constructs that incorporate the intrinsically-fluorescent non-canonical amino acid Anap redistribute to cytoplasmic granules upon application of external stressors such as sodium arsenite. Similar labeling and redistribution of overexpressed G3BP1 and TDP-43 was observed in cultures of mouse primary neurons.

Genetic code expansion and non-canonical amino acid labeling have many advantages over traditional fusion proteins for tracking protein redistribution in living cells. The authors show that they are able to label exogenous G3BP1 and TDP-43 with the non-canonical amino acid Anap, and follow labeled proteins in living cells with and without stress.

I suspect that this method could be incredibly valuable to many investigators studying the dynamics and interactions of proteins that are difficult to label or detect by conventional methods.

Comment on revised version:

The revised manuscript is significantly improved, with added controls and experiments to confirm expression and Anap labeling of G3BP1 and TDP-43.

Reviewer #1 (Public review):

Summary:

This study by Damphousse, Calvin, and Redish investigates how the hippocampus represents competing future outcomes during approach-avoidance conflict. Using an ethologically relevant robotic predator foraging paradigm, the authors aimed to dissociate hippocampal activity associated with reactive defensive responses (escape) from that linked to anticipatory withdrawal decisions. The central finding is that dorsal hippocampal representations differentiate these two modes of defensive behavior within a single naturalistic assay. Specifically, the authors show that attack-triggered retreats and mid-track aborts differ in movement dynamics and hippocampal spatial decoding despite sharing a common behavioral endpoint, that hippocampal representations during pauses predict subsequent behavioral outcomes, and that these representational biases emerge before overt behavioral divergence. The main importance of the study lies in moving beyond viewing the hippocampus as merely encoding spatial location or threat salience, instead suggesting that hippocampal ensemble activity dynamically tracks and differentially weights threat-related, reward-related, and safety-oriented future states to bias behavior before overt action occurs.

Strengths:

The study has several notable strengths. First, the behavioral decomposition into retreats, mid-track aborts, and mid-track continues is rigorous and provides a highly interpretable analytical framework. Second, replication across two independent cohorts - despite differences in arena configuration, robot design, and extinction procedures - meaningfully strengthens confidence in the robustness of the findings. Third, the unified reanalysis pipeline across cohorts reflects strong analytical discipline, and the Bayesian decoding framework is well-suited to addressing the central representational questions. Fourth, the ethological relevance of the robotic predator paradigm is a major advantage, allowing the authors to examine a richer repertoire of defensive and decision-related behaviors than is possible in conventional fear-conditioning assays. Overall, the experiments are well designed, the data are clearly presented, and the findings make a valuable contribution to understanding how the hippocampus supports decision-making under threat.

Weaknesses:

The study is technically strong, but a few modest revisions would further enhance it.

(1) First, the abstract mentions extinction and reinstatement effects, but neural analyses focus primarily on the attack phase. It would be helpful to clarify or adjust the abstract accordingly.

(2) Second, some interpretive language ("guide," "bias") leans toward causal phrasing. Given the correlational data, using "predict" or "correlate with" would be more precise.

(3) Third, given the relationship between running speed and hippocampal theta, considering speed-related contributions to decoding differences would be useful.

(4) Fourth, reporting turnaround positions for mid-track abort and continue trials (Figure 7) would provide helpful context.

(5) Fifth, a figure comparing stimulated vs. non-stimulated sessions in cohort 2 would support the claim that closed-loop stimulation had no measurable effect.

(6) Finally, reporting effect sizes for key decoding comparisons would add clarity.

Reviewer #2 (Public review):

Summary:

This manuscript extends previous work from Calvin et al. and examines hippocampal representations during approach-avoidance conflict in a robotic predator foraging task. The paradigm itself is very interesting and addresses an important but relatively understudied question in the navigation and foraging literature: how the brain balances risk versus reward during goal-directed behavior. While hippocampal representations of positively valenced goals and future intentions have been extensively studied, much less is known about how these representations evolve during risk-reward tradeoffs involving threat.

The authors use a relatively simple and interpretable decoding approach together with thoughtful behavioral comparisons to ask whether future behavioral outcomes can be read out from hippocampal activity before behavior diverges. The most compelling comparison is between mid-track aborts (MTAs) and mid-track continues (MTCs), where the animals initially exhibit very similar pause behavior but ultimately either abort or continue the trajectory. The authors show that decoded location during these pauses differs prior to the overt manifestation of the behavioral decision, suggesting that hippocampal representations may reflect evolving internal evaluation processes during approach-avoidance conflict.

Strengths:

A major strength of the work is the behavioral paradigm itself. This type of risk-reward conflict task is relatively uncommon in the hippocampal navigation literature and provides a rich framework for examining defensive decision-making during naturalistic foraging behavior.

The decoding analyses are also relatively simple and easy to interpret. Rather than relying on highly complex modeling approaches, the authors use straightforward comparisons of decoded spatial representations across behavioral conditions, making the results accessible and conceptually clear.

Another strength is the use of behavioral controls to isolate comparisons between related behaviors. In particular, the comparison between MTAs and MTCs is compelling because the animals exhibit similar pause states before the behavioral outcomes diverge. This provides a useful framework for asking whether hippocampal activity reflects future behavioral outcome before the decision is overtly expressed.

Overall, the study asks an interesting question using a novel paradigm and provides evidence that hippocampal representations during approach-avoidance conflict may reflect future behavioral trajectory.

Weaknesses:

The main weakness is that many of the reported effects are relatively subtle and are not sufficiently controlled for differences in speed, trajectory structure, and other behavioral variables across conditions. While the subtraction plots (green versus purple decoding differences) appear visually striking, the actual effect sizes are fairly small, making it difficult to assess how robust or behaviorally meaningful these differences are.

Relatedly, many of the most interesting questions in this task concern how behavior unfolds dynamically within a trial, yet much of the analysis averages across events and trajectories. As a result, potentially important aspects of the behavior may be obscured.

In particular, the manuscript would benefit from richer characterization of the animals' actual movement trajectories and spatial strategies. Because the analyses rely heavily on linearized position, it is difficult to determine whether animals behave differently in two-dimensional space across conditions. For example, during continued approaches, do animals preferentially hug the wall opposite the robot? Do different behavioral conditions show distinct lateral occupancy or trajectory structure? These types of analyses would make the behavioral interpretation substantially more compelling.

More generally, while the results are suggestive and interesting, the relatively small decoding differences and substantial behavioral confounds make it difficult to conclude that the observed effects reflect distinct internal evaluative or threat-related states.

Reviewer #3 (Public review):

Summary:

The study reanalyzes data from a previously published cohort together with an additional cohort to investigate hippocampal activity during approach-avoidance conflict. Unlike many prior studies that isolate reward- or threat-based learning, this task requires animals to evaluate reward and threat concurrently. The central finding is that hippocampal representations differ between hesitant behaviors that lead to approach versus avoidance outcomes, with representations of the attack zone more likely during pauses preceding abort decisions. This is an important extension of prior work on hippocampal activity and deliberation, suggesting that the hippocampal content may help shape the eventual outcome.

Strengths:

All behavioral findings are replicated independently across cohorts, making the behavioral results highly convincing. The design is robust, and the task is especially valuable for studying approach-avoidance conflict. The behavioral paradigm is complex and rare, and neuronal recordings in such a paradigm are of great value.

The major strength of the study is the comparison of neural activity during hesitant behavior leading to different outcomes, namely, pauses followed by the animal aborting the approach (mid-track aborts), and pauses followed by the animal committing to the approach (mid-track continues). Hippocampal activity differed between the two pauses: the attack zone was more likely to be represented during mid-track aborts. The same effect was observed on the journey before the pause: even before the animal hesitates, hippocampal activity before a pause that led to a mid-track abort was more likely to represent the attack zone than hippocampal activity before pauses that led to continued approach. This analysis suggests that hippocampal content before and during deliberative behavior is predictive of the animal's decision.

Weaknesses:

The interpretation of the retreat-related decoding results is less clear. The study compares two sets of retreating behavior: on the one hand, retreat after being attacked, and on the other hand, retreat after hesitation in the absence of an attack (a mid-track abort). Hippocampal activity represents the attack zone more after the animal is attacked. However, these two retreating behaviors originate from different spatial locations: retreats always start past the "attack threshold", while mid-track aborts always start before this threshold. Given that hippocampal decoding is strongly location-dependent, this difference in position makes the neural decoding results difficult to interpret. The increased representation may be due to differences in physical location, rather than the distinct processing of immediate threat and an anticipatory return state.

Reviewer #1 (Public review):

Summary:

The manuscript by Sustar et al. takes a methodical approach to document the types of glutamate receptor subunits that reside in Drosophila muscles, examining developmental stages spanning from larvae to adults. Prior work thoroughly documented the subunits operating in Drosophila larval body wall muscles. Most subsequent research focused on the glutamate receptor heterotetramers found in the body wall, composed of GluRIIA/C/D/E or GluRIIB/C/D/E subunits, along with auxiliary subunits like isoforms of Neto.

For the current work, the authors report that the larval muscle glutamate receptor composition is not universal for all Drosophila muscles. They examine the following muscle systems: larval body wall, adult abdomen, adult leg coxa, and adult indirect flight. They also briefly examine adult muscle structures associated with the proboscis, neck, and haltere. The authors find that the receptor subunits in the adult abdomen (mostly) match those in the larval body wall. This makes sense given that the adult abdominal muscles are derived from the larval body wall. Yet not much else matches the larval body wall. For example, all (or most) of the GluRII-type subunits are missing from the adult indirect flight muscles. Leg muscles have GluRII-type subunits, but they do not have all of them expressed prominently, and they are missing GluRIIB. Additionally, leg muscles express a glutamate-gated chloride channel, which could be a source of inhibitory glutamatergic transmission. Interestingly, when it comes to non-abdominal adult muscles, one general theme seems to be an active promoter (GAL4 driver) for the kainate-type glutamate receptor called Clumsy. The authors propose that Clumsy could be key to understanding how functional GluR complexes are assembled in adult insects.

Strengths:

(1) Documenting the types of glutamate receptors that operate in diverse insect muscle systems is important because it uncovers fundamental information.

(2) Much of the prior research focus has been on how the body wall muscle tetramers assemble and operate. It is a strength to demonstrate the other receptor solutions used by adult NMJs.

(3) The work uses GAL4 drivers and immunohistochemistry (when possible) in combination to draw conclusions.

(4) The muscle anatomical analyses are of high quality. This allows the research group to reach refined conclusions.

(5) The confocal-level images of synaptic active zones and their apposed glutamate receptor clusters are of high quality.

Weaknesses:

(1) There is a strawman argument that is used repeatedly to highlight the significance of the work. The argument implies that the field broadly assumes (or "tacitly" assumes) that the larval body wall glutamate receptor composition extrapolates to all muscles of the fly, including the adult. This reviewer cannot find evidence that this assumption or argument has been explicitly promulgated by others. More likely, others have not examined these muscles directly, and thus, they have not speculated one way or the other.

(2) Related - to the extent that there has been any tacit assumption about GluRIIC/D/E-anchored receptors being ubiquitous among adult muscles, tacit doubt was raised by Rivilin et al., 2004 (cited by the authors but not as a source of doubt) and by RNAseq datasets like FlyAtlas from 2022 (replicated in Figures s11 and s12). To be clear, the current analysis is better than a bulk transcript analysis from adult tissues. But rather than "overturning" a field or being paradigm-shifting, the current data seem confirmatory of FlyAtlas - and confirmatory of Rivlin et al., 2004, which explicitly concluded that larval and adult NMJs were different .

(3) One can draw expression-level conclusions from these data. But genetic tests (e.g., would clumsy losses of function impair leg muscles?) could help the authors and the field draw stronger conclusions about the roles of some of these glutamate receptor gene products. The current dataset falls short of definitively establishing the function of alternate glutamate receptor modules.

(4) The confocal synaptic images are of high quality. They are good enough that one could analyze how well Brp directly apposes a specific glutamate receptor subunit for all the associated imaging data underlying Figures S1-S8. No such analysis is done, but understanding what components seem to directly oppose the site of release could lead to better conclusions.

Overall Assessment and Discussion:

The data in this study are of high quality, and the results support the main conclusion: adult muscle glutamate receptor clusters do not recapitulate the "canonical" larval body wall clusters. This is important, and the data stand on their own. That is the most important part. This reviewer does have suggestions on how to put the current work in proper context; the current draft appears to overstate the novelty of the findings. Additionally, some sentences need editing for accuracy. None of those concerns impeach the excellent foundational data.

Reviewer #2 (Public review):

Summary:

This manuscript presents a broad survey of glutamate receptor composition at the neuromuscular junction in Drosophila across developmental stages and muscle types. The topic is clearly important, and the central observation-that adult muscles differ substantially from the canonical larval NMJ-is interesting and potentially impactful. The dataset is extensive and will likely be of value to the community. However, in my view, there are significant limitations in how the data are generated and interpreted, which at present reduce the strength of the conclusions.

Strengths:

The study addresses a relevant and timely question and provides a large and systematic dataset. The finding that adult muscles diverge from larval NMJ organization is compelling and challenges a widely held assumption in the field. The breadth of approaches, including genetic reporters, immunohistochemistry, endogenous tagging, and transcriptomic data, is, in principle, a strong aspect of the work and allows for a broad overview of receptor expression across tissues and developmental stages. Even in its current form, the manuscript provides useful descriptive information that will be of interest to the community.

Weaknesses:

A major concern is the reliance on a heterogeneous combination of detection methods (GAL4 reporters, antibody staining, endogenous tagging, and RNA), which are treated largely as equivalent lines of evidence. These approaches differ substantially in what they measure and in their sensitivity and specificity. While convergence across methods can in principle be convincing, here this convergence is often inferred from the shared absence of signal. This is problematic because all methods used are susceptible to false negatives for different reasons. As a result, the repeated conclusion that specific GluR subunits are "absent" from adult muscles, including those previously considered essential, is not fully justified by the data presented.

This issue is not only theoretical. The manuscript itself seemingly contains examples where methods disagree, demonstrating that detection is incomplete and method-dependent. These discrepancies could be better integrated into the interpretation. Instead, negative results across methods are often taken as strong evidence for absence, which overstates the certainty of the findings.

In addition, antibody validation appears to rely largely on prior work in larval tissue. Given the structural and biochemical differences in adult muscles, it is not clear that staining performance is equivalent, particularly in cases where the signal is weak or undetected. This further complicates the interpretation of negative results.

More generally, the manuscript moves in several places from descriptive observations to functional or mechanistic implications that are not directly supported. The suggestion that adult muscles operate with fundamentally different receptor assemblies is intriguing, but remains speculative without functional validation. At a minimum, the distinction between observation and interpretation should be made more explicit.

I thus think that the current conclusions need to be more carefully constrained. Ideally, the study would be strengthened by at least one functional experiment, such as electrophysiological recordings from adult NMJs or perturbation of candidate receptors like GluClα or Clumsy. This would help to anchor the expression data in synaptic function.

In summary, this is an interesting and potentially important study, but the current manuscript somewhat overinterprets heterogeneous and partly indirect evidence. It will already be useful in its present form, but could be more convincing if the authors more rigorously account for methodological limitations and moderate their claims accordingly.

Reviewer #3 (Public review):

The Sustar et al. manuscript catalogs glutamate receptor composition across distinct Drosophila NMJs: larval and adult abdominal NMJs, as well as NMJs on adult leg and flight muscles. This work is important and probably overdue. The larval NMJ is the exemplar NMJ in this system, and the identity of "essential" and "alternative" subunits at this stage is assumed by many to hold across developmental stages and NMJ types. Here, the authors show that there is surprising diversification among NMJ types and that the notion of essential/alternative subunits only holds true at larval NMJs.

The study will generate interest in the Clumsy GluR subunit, which has not been well-characterized at all, but is widely expressed at adult NMJs. They also find striking extrasynaptic expression of glutamate-gated chloride channel GluRClalpha in adult leg and flight muscles, raising questions about its role. The study is interesting, logical, and well-written. The figures are clear, and the discussion was particularly thoughtful. I have a couple of comments that the authors could consider.

(1) They cite Rivlin et al., (2004) in the Introduction as the sole previous study to investigate the molecular composition of adult NMJs, but do not mention this work again. In the Discussion, it would be helpful to compare/contrast their finding with those of the earlier work.

(2) Were these analyses done in adults of consistent ages? It seems possible that the GluR subunit composition could be different in very young adults or in aged flies. The age of the animals should be mentioned in the Methods.

(3) The broad expression of GluCl:V5 in adult leg and flight muscles is surprisingly robust and appears to light up the edges of all muscle fibers. Would the authors comment on the controls that were done to ensure that this staining is real and specific to animals carrying that V5 endogenous tag?

(4) The snRNAseq data in Figure S12 differ a bit from the IHC/GAL4 data summarized in the table in Figure 2. In particular, the data suggests that Ukar and Grik are widely expressed in adult muscles. Is there a reason not to include an "snRNA seq" column in Figure 2 alongside the data from GAL4 lines and IHC? To my mind, it is about as reliable as GAL4 lines that often capture only a subset of the full expression pattern. In this case, the snRNAseq data suggest that Ukar/Grik are likely at adult flight muscle NMJs, which might be important since NMJ was negative for everything except Neto-beta by IHC.

Joint Public Review:

Summary:

Kalburge et al. investigate a task in which human subjects make a decision based on the accumulation of noisy evidence. Tasks like this have been studied for decades, but always with the same essential ingredient: noisy moment-by-moment evidence has to be integrated internally by the subjects, and so is not observed by the experimenter.

In this study, the authors depart from this scenario and make the evidence visible. Specifically, subjects see a pigeon moving stochastically on a screen, and they have to determine whether the net motion is to the right or to the left. This provides the experimenter direct access - on a trial-by-trial basis - to the bounds the subjects use to make their decision.

The authors apply this paradigm across a range of tasks, each one differing in how the signal-to-noise ratio (SNR; defined to be the ratio of the drift rate of the pigeons to the standard deviation of the noise) changes over time and across trials. The tasks range from the standard case of constant SNR to the non-standard case where the SNR changes abruptly in the middle of the task.

The authors determined, on a trial-by-trial basis, the bounds used by the subjects. Setting the bounds optimally when the SNR changes over time or across trials is a non-trivial problem; not surprisingly, then, the subjects were suboptimal. However, they weren't very suboptimal; instead, their behavior was "satisficing" (in the words of the authors), meaning their bounds were reasonably close to the optimal ones. Since the loss is relatively flat near the maximum, and finding the optimal bounds is hard, this is a sensible strategy.

Strengths:

The main strength of this work is the introduction of a new paradigm that supports a trial-by-trial measure of the decision bound. This allows direct measurement of the bound at decision time within individual trials. This, in turn, allows experimenters to determine whether the decision bound differs across decision time or fluctuates for the same decision time across trials. This is harder, although not impossible, to do with tasks in which decision bounds have to be estimated across multiple trials, especially when the SNR is changing.

The authors use this paradigm to show that the decision bounds are mostly constant when the SNR is constant within and across trials. This has been shown indirectly before by fitting models with different parametric boundary shapes, but not directly by measuring the boundary separately for different decision times (but see Kira, Yang, and Shadlen, 2015). They also demonstrate that variability in these bound estimates arises from measurement noise rather than trial-by-trial variability in bound heights, something that could not have been done with previous paradigms.

They furthermore replicate findings that subjects adjust their bounds, including weak collapse, to changing reward contingencies and SNRs, further validating their paradigm. And finally, the work demonstrates an apparent within-trial bound change if the SNR changes (predictably) mid-trial, as predicted by their previous work (Barendregt et al., 2022). This is -- to our knowledge -- the first confirmation of this prediction.

Weaknesses:

There are two non-technical weaknesses.

First, comparison to optimal behavior was mainly qualitative; a quantitative comparison would greatly strengthen the work.

Second (although not exactly a weakness), the work does not leverage the full potential of trial-by-trial estimates of the decision bound, which is a missed opportunity. To our understanding, the only finding that relied on trial-by-trial access to the bound was that the variability in the bound estimate was a major source of measurement noise. Their finding that the bound changes to reward contingencies and SNR, on the other hand, did not require such a trial-by-trial estimate. However, with this task (and not standard paradigms), the authors could determine how the bounds change during learning, which would give insight into the learning rules that participants use to adjust their bounds.

There are also a few technical issues.

(1) The authors argue that they don't observe a collapsing bound when the SNR varied across blocks (Figure 5). However, they only seem to perform this analysis on the difference in boundaries between trials with different SNRs (Figsures 5B, D). Observing a zero difference implies that the boundary shape is the same across SNRs, but does not rule out a collapse.

(2) The evidence for a within-trial boundary change for conditions with a within-trial SNR change could be stronger. The data shown in Figures 6C, D is very noisy, and there are no error bars. For individual participants, is the estimated change in bound larger than the variability in bound estimates before and after the SNR changepoint? Are there potentially other measures that could be used to make the point of a clear change in boundary within individual trials more convincing?

(3) The work assumes that bound height estimates are biased due to the bounded accumulation nature of the decision process, and it corrects for these biases with a simulation-based correction (Methods and Figure 7). To our understanding, this correction assumes that the decision time is the first time that this boundary is crossed. However, the authors do not demonstrate that this is the strategy that participants use; they need to explicitly rule out the possibility that there are significant pigeon excursions across the boundary before the decision time.

(4) The authors did not consider other stopping rules, such as a decision based on the last few trials. Showing that a stopping rule based purely on the bound fits the data better than other possible rules would strengthen the manuscript.

Reviewer #1 (Public review):

This manuscript presents compelling evidence from a wild chickadee population linking heritable spatial cognition to extra-pair paternity success, supporting sexual selection via good genes in a food-caching species. The integration of RFID cognition tests with ddRAD paternity assignment is methodologically strong and timely for behavioral ecology, though causal mechanisms and confounds warrant clarification.

Overall, a major revision of the manuscript is recommended, addressing the points below.

(1) Confirmation of manipulation and treatment effects. The central claim hinges on spatial cognition driving EP siring, but direct evidence that cognition predicts observed copulations (vs. post-copulatory mechanisms) is absent. While territories do not cluster by performance (Figure S4), quantify male aggression/movement data during fertile periods to rule out intrusion-based EPP. The authors should provide metrics like nearest-neighbor distances for EP sires or playback responses linking cognition to dominance, as in prior chickadee work. Without this, causal female preference remains correlational.

(2) Female cognition-EPY link inconsistency. Poor female cognition predicts more EPY (first-20-trials: offspring-level χ²=6.21, P=0.013; nests: χ²=6.79, P=0.009), but not for full-task (P>0.5). The authors should discuss why (e.g., learning speed vs. memory stability) and add exploratory correlations (female errors vs. EPY proportion). They should soften claims in the Discussion section of "female-driven" without consistent support and should frame this as a hypothesis.

(3) Cognitive task sensitivity and validity. Mean errors aggregate learning curves effectively, but single feeder-assignment (non-preferred) confounds neophobia/motivation with spatial ability. The authors should report trial-by-trial improvements (Figure S7 subset) or criterion-to-learn metrics. Justify excluding high-error birds (<3 mean); sensitivity analysis needed to check bias toward high performers.

(4) Paternity assignment robustness. ddRAD-CERVUS with bimodal LODs (Figure S8) is solid, but unassigned EPY (social-genotyped but no sire) implies missing sires (~?% of EPY?). Include all alive males as candidates yearly? Test power simulations for LOD thresholds. 2019 exclusion justified, but multi-year SNP alignment could boost resolution.

(5) Mechanistic speculation vs. data. Discussion invokes hippocampus genes (GWAS priors) and good genes, but no offspring cognition/survival data. Label as hypotheses; suggest tracking EPY recruitment. No brood size costs for EP sires is key, but monitor long-term nest investment (e.g., feeding rates).

Reviewer #2 (Public review):

Summary:

In this study, the authors ask whether spatial cognition is under sexual selection in mountain chickadees. To do so, the authors examined a large dataset that includes a) spatial cognition data for both males and females (obtained via use of a clever RFID-based feeder system) and b) social and extra-pair paternity nesting data. As predicted, males with higher spatial cognition sired more extra-pair offspring, and extra-pair sires had, on average, higher spatial cognition scores than the males they cuckolded. Interestingly, females with lower spatial cognition scores were more likely to seek extra-pair copulations, potentially to compensate for their own low spatial cognition. Surprisingly, there was no difference in spatial cognition scores between males that sired their own offspring and those that lost paternity at the nest. Also surprising was the fact that there were no differences in patterns of extra-pair paternity and spatial cognition between high- and low-elevation sites. The latter is particularly surprising in that spatial cognition should be under stronger selection at the high elevation site. Overall, this is a fascinating study that demonstrates that spatial cognition - a trait under natural selection as it directly impacts winter foraging and survival behaviour -is also under sexual selection.

Strengths:

The authors have a robust dataset (n = 732 offspring sampled over 3 years), high-quality spatial cognition data collected with a procedure that has been well-honed over the years, and couple the data with solid statistical procedures that address many potential covariates and potentially confounding factors. In addition, the authors are careful in the discussion to elaborate on the many potential alternative explanations from the results and questions that are likely to arise in the minds of readers (e.g., how are females assessing male spatial ability?)

Weaknesses:

Overall, no major weaknesses were identified in this study. As always, there are editorial issues that I would encourage the authors to consider, including presentation of data/results and clarification on some statistical issues. Overall, however, this is an excellent study that will make an important contribution to our understanding of the evolution of cognition and targets of sexual selection.

Reviewer #3 (Public review):

Summary:

The authors presented evidence that spatial cognition in this population is under sexual selection, with extra-pair males, primarily chosen by the females, having better spatial cognition than males they cuckolded and males with better spatial cognition having more extra-pair young.

Strengths:

This cognitive ecology study was conducted on a well-known long-term study population of free-ranging mountain chickadees. This strong base, alongside a thorough study design and extensive statistical analyses, enabled the authors to address research questions that few other labs can address, making this a potentially powerful study of broad general interest.

Weaknesses:

Throughout the manuscript, there is a focus on the "mean number of location errors per trial over the first 20 trials". Performance changes across trials, so why weren't learning vs peak performance analyzed separately? Similarly, authors also describe results in the context of the entire task, but sometimes in the context of the first 20 trials - why is one prioritised over the other, and why is the emphasis not always consistent? Are the results across the two generally the same? A more thorough explanation addressing all these points is necessary.

Lines 429-432: Why was a categorical (i.e., chi-square test) and not a numerical comparison implemented? A numerical statistical test would capture more of the variation (i.e., the number of years separating the social and EPY males).

Reviewer #1 (Public review):

Summary:

This is important and significant work because it helps describe the complexity of interactions between system components where two herbivores interact with vegetation. Whereas other studies have shown that the larger ungulate (yaks, Bos grunniens, in this case) can facilitate the abundance and population growth of the smaller (the semi-fossorial lagomorph, Ochotona curzoniae, plateau pika hereafter), this study flips the tables and shows that, at least under some conditions, moderate densities of the plateau facilitate the nutritional condition of yaks.

The study was not designed to investigate the reasons that pikas clip Stellera chamaejasme. That said, based on other studies and general knowledge of the ecology of these pikas, it is likely that they clip (although do not eat) this plant because its relatively large size hinders predator detection. This species of pika does better where vegetation height is low than where it is higher.

Strengths:

Notably, the strong inference the authors can claim for their results is supported by the careful experimental design. A weaker paper would have simply noted correlations between pika burrow density and yak feeding efficiency without experimental removal. This paper, to its credit, not only used experimental removals but also documented the various intermediary results that support the ultimate conclusions. The statistical approaches used appear to be appropriate. (Readers are encouraged to read the full Materials and Methods, which are available in the Supplementary Materials section.)

Weaknesses:

Although the study was well designed and executed, and its conclusions appear strongly supported, readers interested in the management implications of the Qinghai-Tibetan Plateau should be mindful of its limitations. First, the study site, at approximately 3,200 m elevation, was relatively low by Qinghai-Tibetan Plateau standards. Stellera chamaejasme becomes less common at elevations > 4,000 m, where a majority of livestock grazing occurs. Thus, it would be instructive to learn, through follow-up studies, whether similar facilitation occurs where unpalatable (and mildly poisonous) species in such genera as Astragalus, Oxytropis, and Thermopsis replace S. chamaejasme as the problematic plant for pastoralists. Second, the authors make no mention of wild ungulates, so it is unclear what, if any, role they may have played in this system. At least one study in Qinghai Province, albeit at a slightly higher elevation, showed that not only pikas, but also Tibetan gazelles (Procapra picticaudata), which were commonly observed on grazed pastures, grazed more frequently on some dicots avoided by domestic sheep than did the livestock themselves (Harris et al. 2015). It would also be instructive to learn if similar facilitation as observed here applied to the other principal livestock species in the area, domestic sheep (which are often herded together with smaller numbers of domestic goats). Finally, as suggested by this study, the interactions between all components of the system are complex and interactive. If pika facilitation of yak nutrition at the densities documented results in herders increasing yak density, might the increased herbivory from the domestic animals provide the conditions for the pika population to increase beyond the densities observed here, and thus toward the levels where facilitation yields to competition?

Citation:

Harris RB, Wang, WY, Badinqiuying , Smith AT, Bedunah DJ (2015) Herbivory and Competition of Tibetan Steppe Vegetation in Winter Pasture: Effects of Livestock Exclosure and Plateau Pika Reduction. PLoS ONE 10(7): e0132897. doi:10.1371/journal.pone.0132897

Reviewer #2 (Public review):

Summary:

This study uses a combination of field sampling and manipulative experiments to test for facilitative impacts of pikas on yaks via suppression of a poisonous forb. The authors found that, when Stellera forbs were present, yak weight increases over the growing season were greater in the presence of pikas compared to in their absence. This occurred because, although pikas do not consume Stellera, they clip it and use it in nest/burrow construction, thereby decreasing its relative abundance in the plant community. Thus, overall, the study contributes to our understanding of how herbivores of different size classes indirectly affect each other via the use of shared resources.

Strengths:

It is well known that large herbivores on grasslands impact smaller animals, but the reciprocal interaction is rarely tested. Thus, this study asks a valuable question, and the experiment is well-designed to test it. The authors also do a good job of demonstrating the potential conservation impacts of their research.

Weaknesses:

What the authors tested is really cool, but their claims go far beyond what they can say based on their experimental design. For example, the authors claim to show that pika impacts on yaks display density-dependent transitions from competition to facilitation. However, their experiment only looked at the presence (at moderate densities) and absence of pikas, and they only tested for facilitation, not competition.

The paper would also benefit from changes to the framing in the introduction and discussion. For example, the authors pitch the work as a test of the stress-gradient hypothesis. However, there is no abiotic stress gradient in the study, which is an essential component of the SGH. They also pitch the work in terms of density dependence, but there is no significant variation in population densities beyond the presence-absence binary. The paper would be stronger if they focused their framing around the literature on facilitative interactions across mammals of different size classes, especially indirect facilitation via use of shared resources, which is what this paper is really about.

Finally, the paper has significant weaknesses in the experimental and statistical methodology. Most importantly, there are inconsistencies in what is visualized in the figures compared to the model results. For example, the results section in several places notes a lack of significant interaction terms in the model but shows interactions in the p-values on the figures. The authors also plot smoothed lines rather than their model results and then draw interpretations from those lines that cannot be tested in the models that they used. There are also missing details that are important for model interpretation, including the distributions used and the sample sizes. Another major concern with experimental design is in the forage nutrient analyses. The authors picked plants along a grazing trail, then measured nutrient content without standardizing based on plant species, so any differences across treatments could be because of what they happened to grab rather than overall forage quality.

Reviewer #1 (Public review):

The multi-species approach of testing the model in macaque and mouse is excellent, as it improves the chances that the observed findings are a general property of mammalian visual cortex. It would be useful to delineate however any notable differences between these species, which are to be expected given their lifestyle.

The overall performance of the model appears to be excellent in V1, with over 80% performance, but falls substantially in V4. It would be important to consider the implications of this finding; for example, in the context of studying temporal lobe structures that are central to recognizing objects. Would one expect that model performance decreases further here, and what measures could be taken to avoid this? Or is this type of model better restricted to V1 or even LGN?

While the manuscript delineates novel axes of inhibitory interactions, it remains unclear what exactly these axes are and how they arise. What are the steps that need to be taken to make progress along these lines?

Comments on revised version.

The authors have adequately addressed the points I raised in my review during the revision.

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 all the comments raised in the previous round of review. The revised manuscript includes new labeling experiments revealing boundary compression at the cardiac poles consistent with the authors predicted dynamic model of heart tube formation.]

Summary:

The study by Raiola et al. conducted a quantitative analysis of tissue deformation during the formation of the primitive heart tube from the cardiac crescent in mouse embryos. Using the tools developed to analyze growth, anisotropy, strain, and cell fate from time-lapse imaging data of mouse embryos, the authors elucidated the compartmentalization of tissue deformation during heart tube formation and ventricular expansion. This paper describes how each region of the cardiac tissue changes to form the heart tube and ventricular chamber, contributing to our understanding of the earliest stages of cardiac development.

In order to understand tissue deformation in cardiac formation, it is commendable that the authors effectively utilized time-lapse imaging data, a data pipeline, and in silico fate mapping. The study clarifies the compartmentalization of tissue deformation by integrating growth, anisotropy, and strain patterns in each region of the heart.

Reviewer #2 (Public review):

The authors address an important challenge in developmental biology: the quantitative description of tissue deformation during organogenesis. They have developed a new pipeline to quantify early heart tube morphogenesis in the mouse, with cellular resolution. They adopt an elegant approach by integrating multiple 3D time-lapse datasets into a dynamic atlas of cardiac morphogenesis in order to compute spatio-temporal deformation patterns. The main findings highlight a strong compartmentalization of cell behaviors, with tissue growth and anisotropy exhibiting complementary and spatially segregated patterns. Using these data, the authors developed an in-silico fate mapping tool to interrogate cell displacement within the myocardium. This virtual model provides new mechanistic insights into how the bilateral cardiac primordia converge and transform into a three-dimensional heart tube. The authors identify "belt-like" constraints at the arterial and venous poles that prevent tissue expansion and thus shape the ventricular barrel morphology.

The computational framework is highly innovative and impressive, providing an unprecedented 3D model of tissue deformation during heart morphogenesis. It also opens avenues for testing hypotheses regarding tissue growth and the forces that cause cell motion.

Overall, this carefully performed study provides a new model for exploring tissue deformation during organogenesis and will be of broad interest to computational and developmental biologists.

Reviewer #3 (Public review):

Summary:

The manuscript by Raiola and colleagues entitled "Quantitative computerized analysis demonstrates strongly compartmentalized tissue deformation patterns underlying mammalian heart tube formation" takes a highly quantitative approach to interrogating the earliest stages of cardiogenesis (12 hours, from early cardiac crescent to early heart tube) in a new and innovative way. The paper presents a new computational framework to help identify both regional and temporal patterns of tissue deformation at cellular resolution. The method is applied to live embryo imaging data (newly generated and from the group's previous pioneering work). In the initial setup, the new model was applied directly to raw time-lapse data, and the results were compared to actual cell tracks identified manually, showing close correlations of the model with the manual tracking. Next, they integrated spatial and temporal information from different embryos to generate a new model for tissue movement, driven by parameters such as tissue growth and anisotropy. Key findings from their model suggest that there are distinct compartments of tissue deformation patterns as the bilateral cardiac crescent develops into the linear heart tube, and that the ventricular chamber forms by a defined expansion pattern, as a 'hemi-barrel shape', with the arterial and venous poles (IFT and OFT) acting as the harnessing belts constraining the expansion of the chamber further. Lastly, the model is tested for its ability to predict future residence of cardiac crescent cells in the heart tube, which it seems to be able to do successfully based on fate tracking validation experiments.

The manuscript provides an exceptionally careful analysis of a critical stage during heart development - that of the earliest stages of morphogenesis, when the heart forms its first tube and chamber structures. While numerous studies have interrogated this stage of heart development, few studies have performed time-lapse imaging, and, to my knowledge, no other report has performed such in in-depth quantitative analysis and modeling of this complex process. The computational model applied to normal heart development of the myocardium (labelled by Nkx2-5) has revealed multiple new and interesting concepts, such as the distinct compartments of tissue deformation patterns and the growth trajectories of the emerging ventricle. The fact that the model operates at cellular resolution and over a nearly continuous time period of approximately 12 hours allows for unprecedented depth of the analysis in a largely unbiased manner. Going forward, one can imagine such models revealing additional information on these processes, performing analyses of subpopulations that form the heart, and maybe most importantly, applying the model to various perturbation models (genetic or otherwise). The manuscript is very well written, and the data display is accessible and transparent.

No major weaknesses are noted with the study. It would have been very exciting to see the model applied to any kind of perturbation, for example, a left-right defect model, or a model with compromised cardiac progenitor populations. However, the amount of live imaging required for such analyses renders this out of scope for the current study.

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 Rayan et al. aims to elucidate the role of RNA as a context-dependent modulator of liquid-liquid phase separation (LLPS), aggregation, and bioactivity of the amyloidogenic peptides PSMα3 and LL-37, motivated by their structural and functional similarities.

Strengths:

The authors combine extensive biophysical characterization with cell-based assays to investigate how RNA differentially regulates peptide aggregation states and associated cytotoxic and antimicrobial functions.

Reviewer #2 (Public review):

In this paper, Rayan et al. report that RNA influences cytotoxic activity of the staphylococcal secreted peptide cytolysin PSMalpha3 versus human cells and E. coli by impacting its aggregation. The authors used sophisticated methods of structural analysis and describe the associated liquid-liquid phase separation. They also compare to the influence of RNA on aggregation and activity of LL-37, which shows differences to that on PSMalpha3.

Major comments on the previous version:

(1) The premise, as stated in the introduction and elsewhere, that PSMalpha3 amyloids are biologically functional, is highly debatable and has never been conclusively substantiated. The property that matters most for the present study, cytotoxicity, is generally attributed to PSM monomers, not amyloids. The likely erroneous notion that PSM amyloids are the predominant cytotoxic form is derived from an earlier study by the authors that has described a specific amyloid structure of aggregated PSMalpha3. Other authors have later produced evidence that, quite unsurprisingly, indicated that aggregation into amyloids decreases, rather than increases, PSM cytotoxicity. Unfortunately, yet other groups have in the meantime published in-vitro studies on "functional amyloids" by PSMs without critically challenging the concept of PSM amyloid "functionality". Of note, the authors' own data in the present study that show strongly decreased cytotoxicity of PSMalpha3 after prolonged incubation are in agreement with monomer-associated cytotoxicity as they can be easily explained by the removal of biologically active monomers from the solution.

In their revision and in the rebuttal, the authors have further described their concept regarding what they call "functionality" of PSMalpha3 amyloids. They now admit that monomers are the active cytolytic form, like other researchers have stressed, whereas amyloids are not. This represents a considerable difference to earlier papers in which they ascribed functionality, i.e. cytolytic capacity, to PSMalpha3 amyloids, a claim that has raised considerable controversy. Now, they use the term "functional " to describe that PSMalpha3 amyloids, while not cytolytic, can be reversed to a cytolytic monomeric state, calling them a "dynamic reservoir". There is no evidence that such a reservoir is necessary for the cytolytic activity of the monomers to be established; also, there is no evidence that in a biological system, such an amyloid reservoir exists. To continue calling PSMalpha3 amyloids "functional" based on this - considerably changed - concept of the authors appears inappropriate, given the finally admitted absence of cytolytic activity of the PSM amyloids in addition to the continuing complete lack of evidence of any biological relevance of PSM amyloid formation.

(2) That RNA may interfere with PSM aggregation and influence activity is not very surprising, given that PSM attachment to nucleic acids - while not studied in as much detail as here - has been described. Importantly, it does not become clear whether this effect has biologically significant consequences beyond influencing, again not surprisingly, cytotoxicity in vitro. The authors do show in nice microscopic analyses that labeled PSMalpha3 attaches to nuclei when incubated with HeLa cells. However, given that the cells are killed rapidly by membrane perturbation by the applied PSM concentrations, it remains unclear and untested whether the attachment to nucleic acids in dying cells makes any contribution to PSM-induced cell death or has any other biological significance.

Reviewer #1 (Public review):

Summary:

Here the authors address the organization of reach-related activity in layer 2/3 across a broad swath of anterodorsal neocortex that included large subregions of M1, M2, and S1. In mice performing a novel variant water-reaching task, the authors measured activity using two-photon fluorescence imaging of a GECI expressed in excitatory projection neurons. The authors found a substantial diversity of response patterns using a number of metrics they developed for characterizing the PETHs of neurons across reach conditions (target locations). By mapping single-neuron properties across cortex, the authors found substantial spatial variation, only some of which aligned with traditional boundaries between cortical regions. Using Gaussian mixture models, the authors found evidence of distinct response types in each region, with several types prominent in multiple cortical regions. Aggregating across regions, four primary subpopulations were apparent, each distinct in their average response properties. Strikingly, each subpopulation was observed in multiple regions, but subpopulation members from different regions exhibited largely similar response properties.

Strengths:

The work addresses a fundamental question in the field that has not previously been addressed at cellular resolution across such a broad cortical extent. I see this as truly foundational work that will support future investigation of how the rodent brain drives and controls reaching.

The quantification is thoughtful and rigorous. It is great that the authors provide explanation for and intuition behind their response metrics, rather than burying everything in the Methods.

The Discussion and general contextualization of the Results is thorough, thoughtful, and strong. It is great that the authors avoid the common over-interpretation of classical observations regarding cortical organization that are endemic in the field.

All things considered, this is the best paper regarding spatial structure in the motor system I have ever read. The breadth of cellular resolution activity measurement, the rigor of the quantification, and the clear and open-minded interrogation of the data collectively have produced a very special piece of work.

Weaknesses:

There are two important issues left unaddressed that the authors plan to address in their future work. The first is the relation between observed neural activity patterns and movement kinematics, and in particular how much the activity variation across target locations may relate to the kinematic differences across these different conditions, as opposed to true higher-order movement features like reach direction. The second issue is how to interpret the results in relation to existing ideas about behavioral organization in motor/premotor cortex.

Comments on revised version:

The authors have done an excellent job addressing my previous concerns. I have no additional concerns with the manuscript.

Reviewer #2 (Public review):

Summary:

The functional parcellation of cortical areas is a critical question in neuroscience. This is particularly true in frontal areas in mice. While sensory areas are relatively well characterized by their tuning to sensory stimuli, the situation is much less clear for motor areas. This has become even more ambiguous since recent studies using large-scale neuronal recordings consistently report mixed sensory and motor-related activity throughout the brain and motor mapping studies have shown that movements evoked by cortical stimulation are by no means limited to motor areas alone. Here, the authors use a correlation approach combining large-scale functional imaging at cellular-resolution with movement-tracking in mice executing a reaching task. Across multiple recording sessions in the same animals, the authors have imaged a large portion of the sensorimotor cortex at cellular resolution in mice performing a reaching task, recording the activity of nearly 40,000 neurons. By aligning the calcium signal of each neuron to three task events-the Go cue triggering the reach, the onset of paw lift, and the contact between the paw and the target-for different target positions, the authors identified different response patterns distributed differently across cortical areas. They defined a set of features that describe the neurons' response pattern, representing the temporal dynamics and tuning properties for the different target positions. These features were used to construct cortical maps, and the authors show that, interestingly, gradient maps obtained from the first derivative of the feature maps reveal sharp discontinuities at the boundaries between anatomically defined cortical areas. Using dimensionality reduction of the neuronal response features, the authors found that, despite clear differences in their average response properties, individual neurons from the same cortical areas do not form distinct clusters in the reduced-dimensional space. In fact, most areas contain heterogeneous neuronal populations, and most neuronal populations are present in multiple areas, albeit in different proportions. Interestingly, the authors identified four neuronal subpopulations based on the distance between the components of the Gaussian mixture model used to model the distribution of neurons within each area. One of these subpopulations is almost exclusively represented in the anterior M2 cortex, while another is broadly distributed across the different areas.

Strengths:

This article is based on an impressive dataset of nearly 40,000 neurons covering a large portion of the sensorimotor cortex and on innovative analytical approaches. This study is likely the first to clearly demonstrate boundaries between cortical areas defined based on the responses of individual neurons. This innovative approach to functional mapping of cortical areas potentially opens up new perspectives for higher-resolution mapping of frontal cortical areas, using a broader repertoire of sensory and motor evoked responses.

Weaknesses:

One limitation of this study - inherent in most cell imaging studies - is that it only takes into account the activity of neurons in superficial cortical layers. One might think that taking into account neuronal activity across the different layers would allow for an even finer functional cortical segmentation.

Comments on revised version:

The authors have answered all my questions and this new version has largely improved in clarity.

Reviewer #1 (Public review):

Summary:

Simoens and colleagues use a continuous estimation task to disentangle learning rate adjustments on shorter and longer timescales. They show that participants rapidly decrease learning rates within a block of trials in a given "location", but that they also adjust learning rates for the very first trial based on information accrued gradually about the statistics of each location, which can be viewed as a form of metalearning. The authors show that the metalearned learning rates are represented in patterns of neural activity in the orbitofrontal cortex, and that prediction errors are represented in a constellation of brain regions including ventral striatum, where they are modulated by expectations about error magnitude to some degree. The work opens the door to future work focusing on how exactly these signals contribute to adaptive behavior.

Strengths:

The authors build on an interesting task design allowing them to distinguish moment-to-moment adjustments in learning rate from slower adjustments in learning rate corresponding to slowly gained knowledge about the statistics of specific "locations". Behavior and computational modeling clearly demonstrate that individuals adjust to environmental statistics in a sort of metalearning. fMRI data reveal representations of interest including those related to adjusted learning rates and their impact on the degree of prediction error encoding in the striatum.

Weaknesses:

It was nice to see that the authors could distinguish differences between the OFC signals that they observed and those in the visual regions based on changes through the session. However, the linkage between these brain activations and a functional role in generating behavior remains somewhat unclear, opening the door for alternative interpretations.

Comments on revised version.

I appreciate the authors responses and they have largely addressed my concerns. I understand the concerns about power with regard to the individual differences/behavioral analyses included in the rebuttal. However, my personal view, which is perhaps a matter of taste, is that the paper would benefit from a description of these results - along with a clear description of why the authors are hesitant to draw a strong interpretation from the negative result.

Reviewer #2 (Public review):

Summary:

Across two experiments, this work presents a novel spatial predictive inference paradigm that facilitates the investigation of meta-learning across multiple environments with distinct statistics, as well as more local learning from sequences of observations within an environment. The authors present behavioral data indicating that people can indeed learn to distinguish between noise levels and calibrate their learning rates accordingly across environments, even on initial trials when revisiting an environment. They complement their behavioral results with computational modeling, further bolstering claims of both local and global adaptation. Additional fMRI results support the role of OFC in this meta-learning process, with central OFC activity reflecting similarity between environments. This similarity emerges over time with task experience. Holistically, this paradigm and these data add to our understanding of how humans dynamically adapt their behavior on different timescales.

Strengths:

The novel paradigm represents a clever and creative expansion of spatial predictive inference tasks. The cover story was well chosen to facilitate an intuitive understanding of both the differences between environments, and the estimation of the mean within environments.

Additionally, the authors present complementary results from two experiments, which strengthens the behavioral findings. This is especially effective as the initial experiment's results were a bit noisy, and the modifications within the second experiment increased both power and the specificity/accuracy of participant predictions. Taken together, the behavioral results provide convincing evidence that participants did distinguish environments based on their underlying statistics and adapted their initial behavior accordingly.

Beyond this, the combination of behavioral results, computational modeling, and neuroimaging enhances the impact of the work. It paints a fuller picture of whether and how humans meta-learn the global statistics of environments, and this is an important direction for the field of adaptive learning.

Weaknesses:

Throughout much of the paper, the authors refer to the distinctions between environments primarily as differences in "initial learning rates" or "environment-specific learning rates." The optimal initial learning rate did indeed differ across environments -- the result of differences in underlying task statistics. These differences in task statistics result in distinct optimal initial learning rates and also vary with aspects of spatial position (e.g. vertical position in the example figure). The authors convincingly show that OFC activity increasingly reflects these variables throughout task experience. Given that these variables vary together, future work will be needed to distinguish whether particular variables drive these dynamics, or whether together they combine to evoke the representational differences.

The current work is also quite suggestive of meaningful individual differences in both local and global adaptive learning, in line with other prior work on predictive inference. This is perhaps underexplored in this data set, but certainly leaves the topic ripe for follow up going forward.

Finally, more information on all clusters that survived multiple comparisons correction would be useful, even in the absence of a priori hypotheses. For instance, there is commentary in the discussion section on the ACC, but this is not mentioned in the results, and it is unclear whether there were other undescribed clusters that survived correction.

Reviewer #1 (Public review):

Summary:

Cai et al. investigated the role of ripples in the hippocampus and coupled between the hippocampus and the neocortex in visual short-term memory (VSTM) using a similar lures match-to-sample task. The main findings are that hippocampal, but not neocortical ripples, ramp up during the maintenance period, peaking shortly before the memory response is given. This ramping-up effect was stronger for correct compared to incorrect trials. Furthermore, the authors show that stimulus category could be better decoded during coupled hippocampo-neocortical ripples compared to uncoupled ripples. These results provide compelling novel evidence for a role of ripples in supporting human visual short-term memory.

Strengths:

(1) State-of-the-art intracranial EEG in 13 patients during a well-designed visual short-term memory task, with simultaneous hippocampal and neocortical recordings.

(2) Thorough analysis pipeline with validation to detect ripple events, and distinguish them from spurious ripple activity (i.e., as induced by IEDs).

(3) Use of multivariate classifiers to resolve the neural representation of the stimuli.

Weaknesses:

It is difficult to find clear weaknesses in this paper, as the analyses are thorough, the results are clear, and the writing is excellent. However, some more sanity checks on the validity of ripples could have been conducted (i.e., making sure that ripple events have multiple peaks in the unfiltered raw signal at the ripple frequency). Also, the time window for coupled ripples appears to be a bit long, which makes it questionable to what degree these ripples are coupled (i.e., the time window is ~5 times longer than the duration of a ripple event). Lastly, the ramping-up effect could have been more clearly depicted in the figures, but that's a fairly minor point.

Reviewer #2 (Public review):

Summary:

Liu et al. record intracranial EEG from the hippocampus and lateral temporal lobe in thirteen neurosurgical patients while they perform a delayed match-to-sample visual short-term memory task. The central question is whether hippocampal sharp-wave ripples (brief high-frequency oscillations well established in the long-term memory consolidation literature) also contribute to the active maintenance of visual representations over a short delay. The authors report three main findings: hippocampal ripple rates progressively ramp up across the 7-second maintenance period, hippocampal ripples temporally co-occur with ripples in the lateral temporal lobe, and these coupled events coincide with above-chance category-level decoding of the memorized stimulus in the lateral temporal lobe. The findings are interpreted within the dynamic coding framework of working memory, which predicts discrete reactivation bursts rather than sustained firing during maintenance. The question is timely, and the use of intracranial recordings affords a level of temporal and spatial resolution unavailable to non-invasive methods.

Strengths:

The study addresses a genuinely important and underexplored question: whether a neural mechanism best characterized in the context of offline memory consolidation is also engaged during active online maintenance. The use of intracranial recordings in humans is well suited to this question, providing the millisecond temporal resolution and regional specificity needed to detect transient high-frequency events. The dissociation from long-term memory, tested by splitting remembered trials according to whether the item was later recalled in a cued-recall test, directly addresses what would otherwise be a significant confound, and the finding that ripple dynamics during maintenance are unrelated to subsequent long-term memory performance adds specificity to the interpretation. The coupled ripple analysis is methodologically grounded, and the finding that coupled but not isolated ripples coincide with elevated memory decoding is mechanistically informative. The multivariate decoding approach applied to lateral temporal lobe spectral power provides a meaningful index of memory reactivation that goes beyond simple univariate rate measures. The control analysis and the alternative ripple detection method provide useful robustness checks. The public availability of preprocessed data and analysis code on OSF is commendable.

Weaknesses:

(1) Theoretical motivation for examining ripples in visual short-term memory.

A fundamental question that the paper does not adequately address is why hippocampal ripples, a mechanism strongly associated with offline memory consolidation during sleep, where they coordinate the transfer of hippocampal representations to cortex through temporally compressed replay, should be recruited for the online maintenance of visual information over a seconds-long delay. The Introduction acknowledges this gap but does not close it. The dynamic coding framework is used to motivate the ramping-up prediction, but this framework is agnostic about the specific neural mechanism responsible for reactivation bursts. In particular, the literature cited by the authors predicts high-frequency population activity or gamma bursts, but not specifically hippocampal ripples. The reasoning that "ripples share key properties with postulated reactivation bursts" risks being circular: it amounts to saying that ripples could be the relevant mechanism because the relevant mechanism has properties that ripples also have. A stronger theoretical motivation would require either evidence that the replay or reactivation computations that ripples support during offline states are also engaged during active short-term maintenance, or a mechanistic account of how the circuit processes underlying ripple generation are recruited differently across these two contexts.

This concern is compounded by what the authors present as one of their main controls. The finding that ripple dynamics during maintenance are not associated with subsequent long-term memory performance is treated as a reassurance that the observed effects are specific to short-term memory. But if ripples are canonically a long-term memory consolidation mechanism, the observation that they are engaged by a short-term memory task while appearing disengaged from concurrent long-term memory encoding is itself a finding that demands explanation. Resolving this tension is important for the paper's contribution to be correctly interpreted by the field.

(2) Ripple detection and specificity.

Even granting that ripples could in principle contribute to short-term memory maintenance, the study does not establish that the detected events are physiological sharp-wave ripples rather than broadband high-frequency activity. The detection band (70-180 Hz) substantially overlaps with the high-gamma range, which is a well-established proxy for local neural population activity and coding, and is broader than the 80-120 Hz band used by several of the cited papers, including Vaz et al. (2019), Ngo et al. (2020), Chen et al. (2021), Staresina et al. (2023), and Kunz et al. (2024). Without demonstrating that detected events have the hallmark features of physiological sharp-wave ripples, a clear narrowband spectral peak, and characteristic waveform morphology, it is difficult to conclude that the observed effects reflect a ripple-specific mechanism rather than a more general high-frequency population activity phenomenon. The reported mean rate of 0.29 Hz is somewhat higher than rates reported in some recent work, such as Chen et al. (2021, ref 74) and Kunz et al. (2024, ref 15). It is worth noting that van Schalkwijk and Helfrich (2026, Nature Communications) demonstrated that a large proportion of awake ripple detections in the human medial temporal lobe reflect false positives arising from aperiodic 1/f noise, with task-related modulations of this noise floor producing spurious detections. The authors present an 80-120 Hz control analysis as a robustness check, but this inverts the appropriate logic: if 80-120 Hz is the more validated band, as the cited literature suggests, it should serve as the primary analysis rather than a supplementary one.

(3) Internal inconsistency with the dynamic coding framework.

The authors invoke the dynamic coding framework, which predicts that reactivation bursts should ramp up toward the end of the retention interval in the region where memory representations are actively maintained. The hippocampal ramping-up result is presented as confirming this prediction. However, the lateral temporal lobe, the region where above-chance category decoding is found and memory reactivation is attributed, shows no corresponding ramp-up. The authors acknowledge this asymmetry but do not offer a mechanistically satisfying explanation, and the suggestion that the effect might exist in unsampled subregions cannot be evaluated with the current data. This leaves the framework's core prediction unconfirmed in the region that is claimed to maintain the representations.

(4) Coupled ripples, directionality of hippocampal-lateral temporal coupling, and the ramping-up paradox.

The conclusion that coupled hippocampal-lateral temporal ripples coordinate memory reactivation creates a logical tension that the paper does not resolve. If hippocampal ripples drive lateral temporal reactivation only when co-occurring with lateral temporal ripples, and hippocampal ripples ramp up in a memory-predictive fashion, then the absence of lateral temporal ripple ramping up implies that the hippocampal ramp-up is not primarily expressed through the coupled ripple mechanism, undermining the coherence of the two main findings. The coupled ripple analysis further quantifies only temporal co-occurrence and provides no evidence about the direction of influence. Without demonstrating that hippocampal ripples systematically precede lateral temporal ripples (i.e., the expected signature of hippocampus-to-cortex information flow), the central claim that hippocampal ripples drive lateral temporal reactivation remains an interpretive assumption. Directly testing whether lateral temporal ripples specifically coupled to hippocampal ripples show a ramping temporal profile during maintenance (even if overall lateral temporal ripple rates do not) is necessary to establish whether the lateral temporal lobe engages in hippocampally-gated reactivation bursts in the manner the framework predicts. Additionally, reporting the distribution of peak lags between hippocampal and lateral temporal ripple peaks, and testing whether hippocampal ripples systematically precede lateral temporal ripples, is similarly necessary to support the directional interpretation.

(5) Trial-level analysis clarity.

The paper reports that ripples occurred in 54%, 79%, and 27% of trials during encoding, maintenance, and retrieval, respectively, but does not state whether subsequent analyses were conducted on trials thresholded by ripple occurrence. Given that occurrence rates vary substantially across stages and conditions, this inclusion criterion has implications for interpreting rate differences and should be stated explicitly.

(6) Statistical model specification.

The methods describe the ramping-up analysis using both a "logistic" link function and a "Poisson link function" in different places, with the dependent variable described inconsistently as ripple occurrence and ripple count. These are not equivalent, and the distinction matters for interpreting the reported coefficients. Additionally, the regional dissociation in Figure 3 appears to be assessed by fitting separate models to each region and comparing results informally. This does not constitute a direct test of whether slopes differ between regions and risks the well-known error of inferring a difference based on one p-value being significant while another is not. A direct region × time interaction test would more cleanly support the claimed dissociation.

Reviewer #3 (Public review):

Summary:

Liu, He, et al. present results suggesting hippocampal ripples support short-term working memory. The basic finding that hippocampal ripples increase during a 7s working memory maintenance period is intriguing and previously not shown as far as I know, but a lack of control analyses within the task, across brain regions, or as compared to alternative oscillatory signals makes the overall evidence weak. The author needs to more thoroughly evidence this signal via several analyses (suggested below) to strengthen their finding. The paper moves on to a hippocampal-cortical ripple coupling analysis that needs further methodological details and corrected statistics to make a meaningful contribution. As is, the ripple coupling results don't seem to necessarily relate to the hippocampal ripples found in the maintenance period, making the manuscript somewhat incoherent and of low impact in its current form.

Major issues:

(1) The framing sets up "visual short term memory" (VSTM) and "long term memory" (LTM) as two different things. A long line of research with humans possessing MTL/hippocampus damage shows the hippocampal memory system contributes to working memory only when the task is difficult enough to warrant its recruitment (see Hannula et al. 2006 J. of Neuroscience, Pertzov et al. 2013 Brain, or particularly Jeneson et al. 2012 Learning & Memory and J. of Neuroscience). This theory therefore, suggests that the hippocampus contributes to working memory via LTM mechanisms, as opposed to it possessing two different roles (VSTM and LTM). While the authors might disagree with this framing, at a minimum, they should describe this line of work. As is, it's difficult to know how their task fits into this literature since it's a cross between a pattern separation probe (identify repeats from lures), working memory (7 s delays), and subsequent cued associate recognition. Addressing why they used this combination of task features would help frame its place in the literature.

(2) The basic idea of looking for hippocampal ripples as a marker for working memory maintenance is new, with no prior literature (that I know of in rodents or in the handful of human intracranial ripple papers) to build on. That said, I suspect hippocampal ripples act as a proxy for hippocampal activation, providing a possible explanation for the hippocampal ripple increase shown during the Maintenance period. The effect they show is well supported by the mixed effects modeling (MEM), making it a potentially meaningful finding, but considering the novelty, it's rather important that control analyses rule out alternative possibilities. I suggest two important ones and a third related to the lack of parametric manipulations in the next paragraph. First, the authors frame the paper by suggesting hippocampal ripples share features with beta/gamma burst theories of working memory maintenance. In that case, the obvious question is why use a ripple detector instead of measuring gamma (or beta) activity as in this previous work? Some work has suggested hippocampal ripples act differently than high-frequency activity (see Sakon et al. 2024 J. of Neuroscience), so an analysis contrasting ripples and gamma seems rather important. Second, and relatedly, the authors only compare the hippocampus and lateral temporal cortex (LTC), likely because these tend to be sites with strong coverage in epilepsy cases. That's ok, but typically there is also reasonable coverage in other MTL areas like entorhinal cortex and amygdala, which would serve as important controls to show what they're measuring likely relates to sharp-wave ripples (a hippocampal phenomenon) and not something more generic like gamma or HFA (as shown in Sakon et al. 2024, Howard et al. 2003 Cerebral Cortex, Axmacher et al. 2007 reference 26, Meltzer et al. 2008 Cerebral Cortex, etc.).

(3) Related to the last point, since there are no parametric manipulations (e.g., different delay durations, different set sizes, varying lure difficulties) there's no way to assess increased hippocampal ripples with stronger loads, which would be important for determining the hippocampal dependence of their task in the first place. Do the authors have any justification for this task as an assessment of hippocampal working memory? I could imagine using a top vs. bottom tercile of lure discrimination difficulty (as assessed across all participants or control non-patients) to compare hippocampal activity. But only after the first trial, each pair is used since only then would the patient have awareness of the difficulty of the upcoming comparison. Or maybe something could be done by comparing VSTM performance by splitting patients based on how they performed at the LTM test.

(4) Also related to the VSTM vs. LTM framing, the authors use an "LTM" cued category recognition task--presumably done at the end of the repeat/lure recognition task--as a way to argue that the hippocampal ripple effects they see relate to VSTM and not LTM. The LTM task is disappointingly underdescribed, where even in the methods (lines 588-592) I cannot figure out when this task was probed, how many trials were done in comparison to the VSTM task, etc. Considering they use the LTM task to support their VSTM interpretation, it's rather crucial to understand precisely what they did. As is, the comparison they do present relies on a statistical error, where they compare p-values (n.b. https://www.nature.com/articles/nn.2886) instead of performing a direct interaction test (lines 177-180). Specifically, if they want to say their signal relates more to VSTM subsequent memory rather than LTM subsequent memory, they need to run a model of the form: ripple_rates ~ remembered + test_type + remembered*test_type (where test_type is either their VSTM or LTM task).

(5) As noted, the increase in hippocampal ripples during maintenance seems substantial, and the MEM confirms a significant increase over time. That said, the presentation of the data is atypical, with an example raster from one channel followed by average time courses of ALL participants below it. Why not show full raster plots for all participants? Ripples are so sparse that all the data in the task can be visualized in a single raster easily. A swarm plot indicating inter-patient variability in the maintenance signal also seems crucial. As is, there is no way to assess how much of the signal depends on a small subset of channels or patients.

(6) To compare ripple rates across task phases, they average over the bounds of each phase (lines 657-660) and input these into their MEMs. This approach makes sense for quantifying what we see in the ripple plots (Figure 2), except for Encoding, where they average over the entire 3 s window, even though there is clear tuning only from ~0-1 s. Using the tuned region and not the entire window is standard and would be more appropriate for the comparisons to maintenance, retrieval, etc (e.g., line 147-148 doesn't check out when looking at the figure), otherwise you are averaging over a seeming ripple inhibition from 1-2 s. They perform a cluster-based permutation test as is, so that a window or something a bit wider would be appropriate.

(7) The authors pivot to a hippocampal-cortical ripple coupling analysis to build the argument that the hippocampal ripples shown in Figure 2 support memory maintenance in the cortex. They use a window of -500 to 500 ms from hippocampal ripples to assess coupling. This is quite wide, since it doesn't seem plausible that a cortical ripple 500 ms from a hippocampal ripple means they synchronize. They cite two papers to justify the analysis, both of which use {plus minus}500 ms windows, but for spindle-ripple coupling, not ripple-ripple, so are miscited. Later in the paper, they switch to {plus minus}50 ms for another coupling analysis, raising the question of why they used {plus minus}500 ms in the previous analysis to begin with. If they want to claim cortical ripples are tuned by hippocampal ripples all the way up to 500 ms away, they should show the rasters (as in Figure 4a) and timecourse ripple rates, but going beyond {plus minus}500 ms to show that ripples in the {plus minus}50-500 ms range are above, say 500-1000 ms to justify their window selection. I will point out that there IS previous work that used {plus minus}500 ms to measure cortical-cortical ripple coupling (Dickey et al 2022 PNAS, which should be cited regardless, as I believe the first hippocampal-cortical ripple paper showing memory effects), although the figures in that paper suggest anything beyond {plus minus}250 ms returns to baseline (see Figure 2A-B).

(8) Lines 239 to 243 comparing p-values instead of an interaction test.

(9) I don't understand what "Further analysis based on the identified cluster" means (line 271). I see in Figure 5c that their broadband classifier identified a window of optimal decoding, but did they use only activity in this cluster to train the subsequent classifier (Figure 5d)? If so, this is not described in the methods. And if it is done that way, I don't think the logic makes sense. As mentioned in comment 6, the ripples during encoding tune to 0-1s after image presentation. So it doesn't make sense to use a 1.85-2.25 s window for ripple-locked decoding-they should just be using the 0-1 s window (or whatever their cluster-based permutation test shows in Figure 2b). Otherwise, it would appear they are studying two different phenomena.

(10) As is, the results in Figure 5d need to be redone. First, the results described on lines 271-275 once again suffer from comparing p-values. They need to run an interaction model if they want to claim Maintenance shows stronger ripple-locked decoding than Encoding (it almost certainly will not, since Encoding appears to show some evidence of decoding (p=0.118)). Second, even if they do change the framing to say Encoding and Maintenance show significant decoding, is it meaningful if Retrieval fails to? If you cannot decode the same information at the time of retrieval as is theoretically being held in working memory during the delay, the coupled ripple reactivation story wouldn't appear to make sense. They do show significant Retrieval decoding in Figure 5a-b, but since I don't really understand how they settled on the "identified cluster" in Figure 5c, I'm not sure what to make of the difference between these decoders.

(11) Finally, as mentioned in the summary, the analyses in Figures 2-3 seem disjointed from those in Figures 4-5. Part of this has to do with the switch to a broadband classifier, then a switch back to coupled ripples, and then, as I already mentioned, decoding results with time windows that don't align with the hippocampal ripple effects they showed earlier. Further, since the main point of Figures 2-3 is to establish a ramp in hippocampal ripples across maintenance, shouldn't they be trying to show how the decoding changes over the course of the Maintenance period? It would also help the interpretation of Figure 5 to see how the coupled ripples change over time in Figure 4 (as they showed them in Figure 2).

Minor issues:

(1) Instead of citing a software package like Emmeans, the statistical test being performed should be explained.

(2) Decoding % accuracy in the heatmaps in Figure 5 and supplementary would be more intuitive, particularly since Figure 5b uses accuracy anyway.

(3) Figure 2b is misleading with an unnecessary change in the y-axis for retrieval.

(4) In Figure 2d, a significant cluster is mentioned, but not drawn onto the figure as in Figure 2b.

Reviewer #1 (Public review):

Summary:

This study combines representational similarity analysis (RSA) with 7T layer-specific fMRI and EEG to examine how neural representations in specific cortical layers of EVC and LOC correspond to the temporal dynamics of visual processing. The authors interpret these correspondences as reflecting feedforward and feedback processes, based on their relative timing and their similarity to representations in different layers of a deep neural network (DNN).

Strengths:

The combination of RSA with laminar fMRI is a promising approach for dissociating the functional roles and dynamics of different cortical layers within the same functional region, and it holds considerable potential for elucidating computational mechanisms both within and between levels of the visual hierarchy. However, several issues should be addressed before the authors' conclusions can be fully supported.

Weaknesses:

(1) The authors report that the representation in the LOC superficial layer resembles EEG-derived neural representations at ~400 ms post-stimulus, and that this similarity is best explained by representations in the higher layers of the DNN. From these two observations, they conclude that activity in the LOC superficial layer is driven by feedback signals. However, neither line of evidence directly dissociates feedforward from feedback contributions.

Specifically, late-stage representations in LOC could instead reflect the outcome of local recurrent computation, given that the superficial layer also serves as an output layer of the local cortical circuit. Moreover, the correlation with the DNN peaks at higher layers rather than being dominated by them, and feature tuning in higher DNN layers does not necessarily map onto higher-order cortical regions such as PFC.

While a feedback contribution to the LOC superficial layer is consistent with theoretical predictions and known cortical anatomy, the current evidence is indirect. I would recommend that the authors either tone down this conclusion or, at a minimum, explicitly clarify the strength and limitations of the evidence in the Discussion.

(2) I could not find information regarding the fMRI slice orientation or whether temporal regions beyond LOC were covered. The reported FOV (192 × 192 mm) seems quite large if only EVC and LOC were targeted. Did the authors acquire data from other object-selective regions in the temporal cortex, and if so, did they analyze these?

It would strengthen the feedback interpretation considerably if the RDM of the LOC superficial layer could be shown to resemble RDMs from more anterior temporal regions, which would be consistent with feedback originating from higher-order object-processing areas.

(3) Related to the previous point, LOC is a relatively large region, and based on the figures, it appears that the LOC ROI may contain two subregions. It would be helpful for the authors to show the location and extent of the LOC ROI in example participants.

If the ROI does indeed span two subregions, do these subregions share the same laminar profile and temporal dynamics?

(4) The authors report no feedback-related information in EVC, which contrasts with a number of prior fMRI studies that have demonstrated object-related feedback signals in EVC. One plausible explanation for this discrepancy is task relevance: in the present study, participants performed only a fixation color-change task, whereas in previous work they were required to attend to object features or identity (e.g., Morgan et al., 2019, J Neurosci; Kok et al., 2016, Curr Biol; Mohsenzadeh et al., 2018, eLife; Hou et al., 2026, eLife). Task demands on object processing may substantially modulate the strength of feedback signals to EVC, and this possibility warrants discussion.

(5) A substantial body of work has used specialized paradigms to dissociate feedforward and feedback signals in EVC (e.g., Williams et al., 2008, Nat Neurosci; Fan et al., 2016, PNAS; Hou et al., 2026, eLife). These studies are directly relevant to the current work but are not cited.

(6) Multidimensional scaling (MDS) visualizations of the RDMs (as in, e.g., Mohsenzadeh et al., 2018) are not included in the manuscript. These visualizations are important for interpreting the representational format across different layers of LOC and EVC, and I would encourage the authors to include them.

Reviewer #2 (Public review):

Summary:

Carricarte and colleagues set out to identify and functionally characterize feedforward (FF) and feedback (FB) information flow during object perception in humans, a question that has been difficult to address non-invasively because FF and FB signals overlap rapidly in time and across regions. The authors capitalize on the canonical cortical microcircuit-FF terminations primarily in middle layers, FB terminations primarily in superficial and deep layers, to spatially separate these signals using sub-millimeter (0.9 mm isotropic) GE-BOLD fMRI at 7T in early visual cortex (EVC) and lateral occipital complex (LOC). They combine these layer-resolved fMRI patterns with millisecond-resolution EEG (from a previously published dataset using the same 24 images) via representational similarity analysis-based EEG-fMRI fusion, and use a Vision Transformer (DeiT) trained on ImageNet to characterize the feature complexity of the resulting spatiotemporal signatures.

The authors first review their approach at the macroscale, replicating the expected EVC-then-LOC temporal hierarchy and the EVC-low/LOC-high feature complexity gradient. They then apply the same framework at the mesoscale of cortical layers, reporting: (a) early middle-layer signals in both EVC (~100 ms) and LOC (~160 ms) consistent with FF processing, (b) a later superficial-layer signal in LOC (~400 ms) interpreted as FB; (c) a layer-uniform feature-complexity profile in EVC (peaking at low-mid DNN layers across all depths); and (d) a feature-complexity dissociation in LOC, where middle-layer signals correspond to mid-to-high DNN layers and superficial-layer signals to high DNN layers. They argue that this complexity shift, combined with the timing difference, indicates interareal FB into LOC.

Strengths:

(1) The combination of layer-fMRI at 7T, EEG, and DNN-based representational analysis is well motivated through RSA. Each modality compensates for a known limitation of the others (fMRI: poor temporal resolution; EEG: poor spatial resolution; DNN: surrogate for representational format), and the RSA framework provides a principled common currency. Relatedly, the two-step macroscale-then-mesoscale design, in which the macroscale fusion replicates established findings before the same approach is applied at the layer level, is a sound and welcome scientific strategy that strengthens confidence in the combined-modality inferences.

(2) The authors include multiple complementary controls: partialing out lower layers to mitigate vascular draining, voxel-count matching across layers, an alternative DNN (AlexNet), an alternative time-window definition based on between-layer differences, and time-resolved commonality analyses. The convergence across these analyses is reassuring.

(3) Methodological transparency: The authors are forthright about partial-volume effects, foveal-confluence aggregation, and the indirect nature of the temporal estimates derived from EEG-fMRI fusion.

Weaknesses:

The central interpretive claim-that the late (~400 ms), superficial-layer LOC signal indexes interareal feedback that increases representational complexity-is intriguing, but in my view it is not yet fully supported by the evidence presented based on the following context.

(1) Eye movements as a possible confound for late signals. Stimuli were presented for 1 second, and fixation was enforced only behaviorally via a color-change task on a central cross. No eye-tracking is reported for either the fMRI or EEG datasets. While this approach is not uncommon, the absence of gaze monitoring introduces ambiguity when the goal is to decouple feedforward and feedback contributions at fine temporal resolution in EEG recordings. Under these conditions, multiple image-driven saccades within a trial are plausible, and saccade patterns are likely to be systematically image-specific, given the small (n = 24) and heterogeneous naturalistic stimulus set. Critically, the temporal window over which RDM correlations are interpreted as feedback coincides with the period during which observers typically make 2-4 fixations (average fixation durations of ~250-330 ms; Rayner, 1998; Henderson, 2003), meaning the late EEG-fMRI fusion peaks fall in a window where image-locked saccadic activity and successive foveation-driven feedforward responses would be expected to accumulate. Late peaks could therefore reflect cumulative feedforward responses across successive foveations rather than top-down feedback. The manuscript would be strengthened by providing eye-tracking data (if available), control analyses leveraging post-hoc indicators, or a discussion citing prior evidence that EEG/fMRI response profiles in this paradigm are robust to such eye movements.

(2) Decoding accuracy along the visual hierarchy raises questions about whether LOC is adequately engaged. Pairwise decoding accuracy is substantially higher in EVC than in LOC (Figure 1D), and the noise ceiling for LOC RDMs is markedly lower than for EVC across all layers (Supplementary Figure 4D-F). This pattern inverts the canonical hierarchical gradient of progressively stronger object decoding along the ventral visual stream, as well as the analogous gradient observed in DNN late layers that underlies the commonality analyses. As written, it is unclear how the manuscript reconciles this with its emphasis on LOC's role in higher-order, feedback-modulated representations with greater tolerance or increased complexity--unless decoding accuracies should be understood as image-level discrimination rather than at the level of object-category discrimination. A parsimonious alternative is that the 24-image set is too small or too coarse to reveal category-level representations in LOC robustly, such that LOC RDMs may be driven by lower-level or background/contextual variance and noise. This concern has direct bearing on the mesoscale commonality analyses supporting the "feedback transmits high-complexity features" conclusion. I would encourage the authors to (a) report split-half reliability of LOC RDMs alongside the commonality analyses, and either (b) acknowledge that the feature-complexity inferences are conditional on LOC RDMs faithfully capturing object structure rather than residual contextual/low-level variance, or (c) discuss how replication with a richer stimulus set might bear on the feedback-content interpretation.

(3) The interareal feedback interpretation could be more robustly defended against intra-areal alternatives. In EVC, the authors carefully consider non-feedback explanations for layer-specific dynamics, including lateral connections modulating gain and superficial GE-BOLD bias, and conclude these are sufficient. The same skepticism is not extended to LOC, where the corresponding superficial-layer signal is interpreted as interareal feedback, with speculative sourcing to DLPFC. Slow (unmyelinated) horizontal/lateral propagation in superficial cortical layers (e.g., Davis et al., 2024) can, in principle, produce delayed superficial-layer signals on the timescale observed here without any interareal contribution. This asymmetry is compounded by the treatment of the absence of sustained EVC activity following the middle-layer peak, which is dismissed as a "limitation of the spatial and temporal sensitivity of our measurements" (lines 388-390). If feedback to EVC truly cannot be resolved with this method, the corresponding feedback claim in LOC-imaged with the same protocol warrants comparable caution. The manuscript would benefit from either presenting positive evidence that distinguishes interareal feedback from intra-areal recurrence (e.g., frequency-band signatures, source-resolved EEG, or coupling with frontal regions), or qualifying the conclusion to "delayed superficial-layer activity consistent with either interareal feedback or intra-areal recurrence."

(4) The predictive coding framing is invoked but not well-grounded. The Discussion (lines 349-357) includes a theoretical implication of predictive coding. Predictive coding makes content-specific claims-feedback carries predictions, feedforward carries error signals relative to those predictions, and dissociating these requires manipulations of expectation, congruence, or predictability, none of which are present in the current design. The observed layer-wise timing differences do not bear evidence for rejecting non-predictive accounts. I would suggest either removing this framing or explicitly noting that the present data neither support nor refute predictive coding.

Reviewer #3 (Public review):

Summary.

Carricarte and colleagues use 0.9mm 7T fMRI in EVC and LOC, fused with previously collected EEG using the same stimulus set, in order to dissect feedforward and feedback contributions to human object processing through their layer-specific termination patterns. They report a feedforward signal in middle layers of EVC (~100ms) and LOC (~160ms), and a later signal in superficial LOC (~400ms) that they interpret as interareal feedback. Using commonality analysis with a Vision Transformer, they argue that this late signal carries higher-complexity features than the earlier signal, and conclude that feedback actively increases representational complexity in LOC.

Strengths.

The empirical work is methodologically ambitious. Sub-millimeter 7T coverage of both EVC and LOC, combined with layer-resolved EEG-fMRI fusion, represents a substantial technical achievement. The authors first reproduce established macroscale EEG-fMRI fusion patterns at 7T before extending the approach to the layer level. The figures throughout are beautifully designed and convey complex analyses with clarity. The empirical core of the paper - that LOC contains layer-distinct dynamics at distinct times, with the late signal carrying representational structure that differs in some way from the early signal - is supported by the data, though with caveats imposed by the LOC noise ceiling.

Weaknesses.

The authors' interpretation of these data (interareal feedback that reflects feature-complexity, related to the functional role of these signals) is not adequately supported and requires either reframing or substantial additional evidence.

Feedback vs. recurrence. The late superficial-LOC signal is interpreted as interareal feedback, but the data are equally consistent with within-area recurrence, lateral connections, or sustained feedforward dynamics. A reader expecting evidence of higher-area signals returning to early-time middle layers - a signature of interareal feedback - finds none in either region.

"Functional role" overclaim. The paper repeatedly claims to characterize the "functional role" of feedforward and feedback, but contains no behavioral linkage, no perturbation, and no analysis relating signals to perceptual outcomes; the fMRI task is explicitly orthogonal to object processing. What is demonstrated is spatiotemporal dynamics and representational format - both valuable, neither equivalent to functional role.

DNN analysis. The DNN analyses use several non-standard modeling choices that introduce more uncertainty than clarity. In the main analyses, the authors only use four sampling points from a single model (DeiT-small): transformer blocks 1, 7, and 12, plus the classification head. Then, the authors make their headline claims about complexity by comparing block 12 and the classification head; within the model, this is a distinction between an embedding layer and a supervised category readout, not a feature-complexity gradient. As such, the author's interpretation conflates semantic layers with representational "complexity." A more convincing use of this modeling strategy would be to demonstrate these effects in multiple models that might disentangle these factors-e.g., supervised (ResNet/ViT), self-supervised (DINOv2), and vision-language (CLIP) models-then to visualize these brain-model relationships across all layers. Alternatively, there are many suitable model-free analyses that could demonstrate the unique representational information within LOC without introducing any model-related concerns.

Reliability of LOC layer-resolved RDMs. The lower-bound noise ceiling for LOC mesoscale RDMs is approximately 0.05 across layers, with deep-LOC reliability essentially at zero. The central layer-resolved dissociation rests on RDMs that individual subjects barely reproduce; consequently, the deep LOC layer is dropped from the commonality analysis (Figure 4C shows only middle/superficial layers, while Figure 4B shows all three for EVC) because the data cannot support it. This is not damning, but it is consequential, and not sufficiently addressed in the manuscript.

Reviewer #1 (Public review):

Summary:

Hüppe and colleagues characterized the network of neurons in the central nervous system of Antarctic krill that contained pigment-dispersing hormone (PDH), an important output factor in the circadian clock of insects. These neurons in the brain are putative clock neurons since a subset also expressed the clock genes period and cryptochrome 2. As one of the ocean's major contributors to biomass, krill is an ecologically important marine species that experiences challenging daily and seasonal environmental fluctuations in its high-latitude habitat. A comprehensive study of krill's internal clock may help to understand the extent of its resilience to the rapidly changing climate.

The authors used antibody staining against PDH across the whole central nervous system and additional in situ hybridization for cry2 and per mRNA, with a focus on the supraesophageal ganglion. There, they identified the major neuropils in the eye stalks and central brain of Antarctic krill. The resulting staining pattern aligns with the identified circadian clock network in insects and PDH-expressing networks in other crustaceans, making these neurons highly likely candidates for krill clock neurons.

Strengths:

(1) This study provides the first clues about the circadian clock architecture in a non-model organism in chronobiology, Antarctic krill, with a clear 3D reconstruction of the putative clock network.

(2) The authors effectively place their results within the extensive body of literature on arthropod circadian clock networks to argue that the neurons they describe are likely the circadian clock in krill.

Weaknesses:

(1) The data presented here are not sufficient to support the claim that the described network is the circadian clock because functional evidence is missing.

(2) Additionally, the study falls short of identifying any elements of the positive limb of the canonical circadian clock transcriptional-translational feedback loop, e.g., clk or cyc, in the PDH-expressing neurons.

(3) No sample sizes are reported, making it difficult for readers to assess the generalizability of the presented data.

Reviewer #2 (Public review):

Summary:

This study advances our understanding of the neuronal basis of the circadian clock in pancrustaceans. It extends our knowledge on the pigment-dispersing hormone system and provides links to information on the expression of core clock components, cryptochrome 2, and period. The data are sound and well-documented.

Comments:

The neuronal components of the arthropod circadian clock system have been analysed extensively in insects. Much less information on this system is available on malacostraca crustacea crustaceans. However, considering that malacostracan crustaceans and insects go back to a common pancrustacean ancestor and considering that we know that the brain architecture in these two groups shares many commonalities (see, e. g., extensive reviews by N. J. Strausfeld), we have to expect that crustaceans and insects share many of the characteristics of the circadian system. This is the case, e. g., for the network of pigment-dispersing hormone-positive neurons. The authors cite these studies, although late in the paper (discussion, line 339ff), and I suggest to move this info into the introduction: "339 ff: The arborization pattern of the PDH-network has been described in various malacostracan crustaceans, including Carcinus maenas (Alexander et al., 2020; Mangerich & Keller, 1988; Mangerich et al., 1987), Cancer productus (Hsu et al., 2008), Orconectes limosus (de Kleijn et al., 1993; Mangerich & Keller, 1988; Mangerich et al., 1987), Homarus americanus (Harzsch etal., 2009), Cherax destructor, Procambarus clarkii (Sullivan et al., 2009), and Procambarus virginalis (Luna et al., 2010)."

The strength of this paper is that it extends our knowledge on the PDH system and brings together neuroanatomical information on PDH-positive neurons with information on the expression of core clock components, cryptochrome 2, and period. That way, it advances our understanding of the neuronal basis of the circadian clock in pancrustaceans. The data are sound and well documented, and the authors are to be applauded for the superb dissection presented in Figure 1.

Below, please find some essential suggestions on how to further improve the paper.

(1) Framing of the study:

I know that krill is a key element of the Southern Ocean's food webs, but my sense is that discussing the current findings in a context of resilience of this species to global ocean change means largely overselling this study:

- Lines 47, 48: "and the resilience of this key species in a rapidly changing Southern Ocean."

- Lines 70 ff: "Hence, understanding the mechanisms of adaptation, including biological clocks, is crucial for predicting how species, populations, and whole ecosystems will respond to climate change."

- 154 ff: "The Southern Ocean environment experiences rapid change (Abram et al., 2025; Meredith et al., 2019; Thomalla et al., 2023). To assess krill's resilience to environmental changes, understanding the mechanisms that govern daily and seasonal timing in krill is essential."

- 325 ff: "The rhythmic adaptation of krill to its high-latitude environment is key to its success in the Southern Ocean, which in turn represents a cornerstone for the well-being of the whole krill centred ecosystem. To predict krill's resilience to rapid environmental changes, it is essential to understand the mechanisms that govern daily and seasonal timing in krill."

- 597 ff: "A detailed mechanistic understanding of the flexibility of clock-based processes is therefore essential to predict krill resilience in a changing Southern Ocean."

My understanding is that duration of day length is one of the most predictable environmental drivers, and - despite the seasonal changes of day length - nevertheless a very stable one compared to fluctuations of environmental drivers such as temperature or salinity (see, e.g. this recent review on environmental driver fluctuations on nervous system functioning in crustaceans: Stein W, Harzsch S (2021) The Neurobiology of Ocean Change - insights from decapod crustaceans. Zoology: 125887. https://www.sciencedirect.com/science/article/pii/S094420062030146X).

I do not see how global ocean change may significantly change day length, and what this study has to do with understanding this species' resilience against ocean change. I suggest that you explain in more detail why the light day length will change in the future or strongly tone this aspect. Statements such as Line 76 ff: "Due to their disproportionate importance for ecosystem function, understanding the resilience of ecological key species is essential in assessing the fate of ecosystems in the future." are completely out of focus here and, again, trying to oversell the current study.

(2) Uncited essential studies of crustacean neuroanatomy, missing connection to contemporary crustacean neurobiology:

- Line 157: "despite the ecological importance of E. superba, only very little is known about its neurobiology".

- Line 329: "However, so far, little was known about the neurobiology of krill in general."

I agree that this species' brain is understudied, but this makes it even more important to cite the little information that IS available. Please consider this essential reading for any crustacean neurobiologist: "Sandeman, D.C., Scholtz, G., Sandeman, R.E., 1993. Brain evolution in decapod crustacea. J. Exp. Zool. 265, 112-133." to find information on the basic brain anatomy in E. superba.

The manuscript in many places seems to reinvent the wheel and raises the impression that our knowledge of crustacean brain morphology is close to zero. The authors in places seem to operate in a vacuum, and I find it disturbing that in a study on the crustacean brain, very few references are provided to studies on crustacean brain anatomy, such as the following essential book chapter: "Schmidt, M., 2016. Malacostraca. In: Schmidt-Rhaesa, A., Harzsch, S., Purschke, G. (Eds.), Structure & Evolution of Invertebrate Nervous Systems. Oxford University Press, Oxford, pp. 529-582. https://www.researchgate.net/publication/315366157"

In terms of brain anatomy, I would like to know if the authors have a hypothesis on whether and how their target species' brain structure may be similar or different to the brains of other "shrimps" as described, e. g., in the following studies. If so, please elaborate in the introduction:

Krieger J, Hörnig MK, Sandeman RE, Sandeman DC, Harzsch S (2020), Masters of communication: The brain of the banded cleaner shrimp Stenopus hispidus (Olivier, 1811) with an emphasis on sensory processing areas. Journal of Comparative Neurology 528(9): 1561-1587.

Meth R, Wittfoth C, Harzsch S (2017) Brain architecture of the Pacific White Shrimp Penaeus vannamei Boone, 1931 (Malacostraca, Dendrobranchiata): correspondence of brain structure and sensory input? Cell and Tissue Research 369(2): 255-271.

(3) Lacking rigor and command of crustacean brain nomenclature

I suggest that for their brain nomenclature, the authors should rigorously stick to that laid out by Sandeman et al. 1992 (not yet cited in the ms): Sandeman, D.C., Sandeman, R.E., Derby, C.D., Schmidt, M., 1992. Morphology of the brain of crayfish, crabs, and spiny lobsters: a common nomenclature for homologous structures. Biol. Bull. 183, 304-326.

More specifically, in lines 41, 163, 199, 204, 207, and throughout the paper, the authors use the terms "Optic lobes" or "optic lobe neuropils". To the best of my knowledge, "optic lobe" is not a term used in crustacean neuroanatomy at all (as opposed to insects). Lamina, medulla, and lobula are collectively referred to as "visual neuropils" (see Krieger, J., Hörnig, M. K., Sandeman, R. E., Sandeman, D. C., & Harzsch, S. (2020). Masters of communication: The brain of the banded cleaner shrimp Stenopus hispidus (Olivier, 1811) with an emphasis on sensory processing areas. Journal of Comparative Neurology, 528(9), 1561-1587. https://doi.org/10.1002/CNE.24831). The medulla terminalis and mushroom bodies are referred to as "lateral protocerebrum". All afore-mentioned neuropils are summarized as "eyestalk neuropils" (compare nomenclature in Schmidt 2016 as referenced above).

Line 170, 172, 175 ff, and Figure 1. "abdomen", "abdominal ganglia": Contra the book chapter by Siegel 2016 "Introducing Antarctic Krill Euphausia superba Dana, 1850", his Fig. 1.2, the "tail" of crustaceans in most books on crustacean anatomy is not called "abdomen" but instead "pleon"; hence the name "pleopods" for the appendages of the pleon (instead of "abdomipods"). What is more, I suggest using the terms "pleon ganglia" instead of "abdominal ganglia", following the terminology suggested in "Harzsch S, Sandeman D, Chaigneau J (2012) Morphology and development of the central nervous system. In: Forest J and von Vaupel Klein JC (Eds.). Treatise on Zoology - Anatomy, Taxonomy, Biology. The Crustacea Vol. 3. Brill, Leiden pp. 9-236."

Line 174: "thoracic ganglia". In Figure 1, there is a labelling mistake as these ganglia are named "thoracaic ganglia".

Line 176, and throughout the paper: "supraesophageal ganglion". Following the standard nomenclature for crustaceans (see, e. g., Schmidt, M., 2016. Malacostraca. In: Schmidt-Rhaesa, A., Harzsch, S., Purschke, G. (Eds.), Structure & Evolution of Invertebrate Nervous Systems. Oxford University Press, Oxford, pp. 529-582. https://www.researchgate.net/publication/315366157", this structure (as in insects) is typically called a "brain". For terminology, also consult the following nomenclature paper: "Richter, S., Loesel, R., Purschke, G., Schmidt-Rhaesa, A., Scholtz, G., Stach, T., Vogt, L., Wanninger, A., Brenneis, G., Döring, C., Faller, S., Fritsch, M., Grobe, P., Heuer, C. M., Kaul, S., Møller, O. S., Müller, C. H. G., Rieger, V., Rothe, B. H., Stegner, M., Harzsch, S. (2010). Invertebrate neurophylogeny: Suggested terms and definitions for a neuroanatomical glossary. Frontiers in Zoology, 7. https://doi.org/10.1186/1742-9994-7-29".

Line 212, and throughout the paper - hemielliposoid body: please refer to Harzsch Krieger 2011 and the numerous references to studies by Strausfeld cited therein in crustaceans. Strausfeld has provided compelling evidence that the crustacean hemiellipsoid body is equivalent to the insect mushroom body, so this term should be replaced. Harzsch, S., & Krieger, J. (2021). Genealogical relationships of mushroom bodies, hemiellipsoid bodies, and their afferent pathways in the brains of Pancrustacea: Recent progress and open questions. Arthropod Structure & Development, 65, 101100. HYPERLINK "https://doi.org/10.1016/J.ASD.2021.101100" https://doi.org/10.1016/J.ASD.2021.101100.

Legend, figure 2, and others, and throughout the paper: "The olfactory neuropiles comprise the lateral antennal neuropile (LAN, ochre), the olfactory lobes (OL, yellow), and the antennal neuropile (AnN, green)." This is a strange terminological mix that you should urgently revise according to the standard terminology by Sandeman et al. 1992 (as referenced above). The LAN is the lateral antenna 1 neuropil. The AnN is the antenna 2 neuropil. The AnN is NOT deutocerebral but tritocerebral.

Reviewer #1 (Public review):

Summary:

In this manuscript, Scheib et al. identify distinct calcium dynamics in the somata and tuft dendrites of layer 5 pyramidal cells in mice performing a licking task. Animals are trained to lick water ports on the left or right following an acoustic cue, and can adjust their targeting when the ports are displaced. For tongue premotor cortical neurons projecting to the ventromedial thalamus, calcium transients in tuft dendrites are tightly locked to the direction-instructive cue, while somatic calcium signals are more broadly dispersed and more frequently synchronized with tongue motion and port contact. Finally, when the targets are shifted, tufts exhibit a sparse but large corrective signal on an improperly-targeted first lick, and the changes in population activity in the tufts and somata differ after adaptation to the new port locations.

Strengths:

In my opinion, this is a very strong manuscript which reports several novel and significant observations, contains high-quality data and (for the most part) reasonable analyses, and is clear and well-written. Most prior studies of cortical sensorimotor processing have measured the output of neurons using extracellular recording - an approach which obscures potentially important signaling differences between neuronal compartments. This study leverages cutting-edge imaging techniques in mice to document large, time-dependent differences between calcium signals at cortical somata and tuft dendrites. This phenomenon could have major implications at the cellular level for synaptic plasticity, and at the systems and behavioral levels for motor adaptation. As described below, I have only one major technical concern (which should be addressable with additional analysis), along with several relatively minor suggestions for improving the manuscript.

Weaknesses:

At a conceptual level, the authors may wish to elaborate a bit on what sensorimotor computation they think the circuit is implementing, and how their results help explain this implementation. Several possibilities are raised: tuft activation could "prime" the pyramidal cells in advance of movement initiation (line 319ff), or could track errors to engage plasticity (line 351ff) and solve the credit assignment problem (line 362ff). It might be helpful to make one of these proposals more concrete with a computational model, but this is not strictly necessary.

My only major technical concern relates to the analyses in Figures 4F-H, 5G-I, and 6H-K (c.f. equations 2-5). Typically, one identifies population-level factors by projecting neural activity onto fixed dimensions of interest; this makes it possible to see how activity evolves over time along interpretable coordinates. Here, however, the coding directions are redefined at each time point, so the "choice" activity at time t is actually a different signal from the "choice" activity at t+1. This procedure is a bit like comparing the activity of one neuron at one time point with the activity of a different neuron at a later time point. It also makes the physiological interpretation more complicated: if the dimensions are fixed, one can see how a downstream neuron could "read out" the signal by computing a weighted sum of the activity of upstream neurons, but it is harder to see how this could happen if the weights are always rotating.

A few comments on the behavioral task and results. After the port shift, the error rate is quite high, and doesn't diminish much between the early and late epochs (approximately 42% and 38% error rate, respectively; Figure 1I). That is, mice do not seem to fully master the task. Clearly, animals do alter their aim, but even this does not seem to change much between early and late periods (Figure 1J). I recommend that the authors show the behavioral data at a finer level of granularity (e.g., by plotting the change in exit trajectory on all individual trials across sessions, with a loess fit) to allow an assessment of the adaptation rate and when adaptation saturates. It would also be more conventional to refer to the behavioral changes as "motor adaptation," instead of "skill learning." (The latter would be appropriate if the port offset were randomized across trials, and animals received two separate cues for direction and offset, but I suspect this task would be too difficult for mice to learn.)

This is perhaps a semantic point, but it might not be entirely accurate to refer to the activity evoked by the directional cue as "sensory." Typically, a "sensory" response should encode some feature of a stimulus - in this case, the frequency of a tone. Here, it seems likely that the cue-aligned activity reflects the instructed lick direction, rather than the auditory information per se. (Presumably, these premotor neurons do not have well-behaved auditory tuning curves.) By comparison, in macaques performing center-out reach tasks, activity in dorsal premotor cortex rapidly ramps up following a visual cue instructing the direction of an upcoming reach, but one usually wouldn't refer to this activity as "visual" or "sensory" (though this is sometimes done). I suggest the authors either use "Instruction" or similar (e.g., in Figure 4F), or clarify in the text whether they think the activity is a genuine auditory response or something else.

Reviewer #2 (Public review):

Summary:

The authors set out to compare functional encoding in the tuft dendrites and somata of a specific cortical cell type during motor planning and learning.

Strengths:

The investigation of a specific projection type (L5 ET) is a strength that aids reproducibility and interpretation. The elegant approach to increasing the depth of field of dendritic imaging is another strength. The data analyses are largely clear in their methods, scope, and interpretation. The writing is extremely clear and appropriately referenced, with an excellent Introduction, in particular.

Weaknesses:

It is not obvious whether the selected labeling strategy avoids labeling Layer 6 CT neurons, which would contaminate dendritic recordings. The images provided suggest enrichment in L5, but a discussion of this important potential caveat is warranted, especially since within-cell comparisons of apical dendrites to somata were not performed.

The application of DeepInterpolation to dendritic data appears to be novel, and little detail or vetting is provided. The reader is left guessing: Was the model retrained or fine-tuned on dendritic data? How does the denoising affect the resulting segmentation and activity traces? Is denoising necessary for this workflow?

The activity patterns of the recorded cells appear to lack the characteristic ramping during the delay epoch previously reported in both calcium imaging and electrophysiology studies. Given that a major contribution to the significance of the work is to constrain models of ALM function, a discussion of how the data aligns with previous measurements in the same circuit would improve the work.

It would be very informative to compare differences in signals between dendrites and somata of the same cells. Consistently tracing dendrites to their respective somata would assuage worries of potential contamination from dendrites of deeper cells and enable more direct comparisons of signal transformations between dendrites and somata. It would be good to understand the relationship between dendritic calcium signals and backpropagating action potentials in this task. The authors detect less frequent calcium events in tufts versus somata; is this due to selective backpropagation of action potentials? The dynamics of this process were recently investigated by Adam Cohen's group in vivo and in vitro, and measurements in the present settings could be compared to such work.

The Coding Direction analyses presented in this work, while consistent with previous literature on population codes in ALM, are at odds with the nature of the measurements here. The changes in representation that occur between the dendrites and soma of an individual cell are probably best thought of in terms of the dynamics of signals themselves within individual neurons, rather than in the information encoded across a population.

This work is largely observational, describing signals that might reflect computational transformations and/or instruct plasticity, but those possibilities have not yet been deeply investigated. The manuscript does a good job of laying out these as future directions.

Reviewer #3 (Public review):

Summary:

This article by Scheib et al. investigates how layer 5 extratelencephalic (ET) neurons in the frontal cortex encode sensorimotor information during motor learning, focusing on differences between their apical tuft dendrites and somas. The authors alternated recordings among these ET neuronal compartments in the mouse anterior lateral motor cortex (ALM) during a cued directional licking task with a target port shift. They found that while tuft dendrites predominantly encode sensory cues, with a subset selectively active during corrective actions, somatic activity was more strongly associated with action timing. Additionally, learning induced divergent plasticity: tuft dendrites increased their selectivity but decreased response gain, maintaining stable net selectivity, whereas somas showed increased net selectivity early in learning. Together, these findings reveal distinct sensorimotor representations and learning-related plasticity in dendritic and somatic compartments, providing insight into how compartment-specific activity in the frontal cortex may contribute to motor skill acquisition.

Strengths:

The authors developed an innovative imaging approach and a comprehensive data analysis pipeline to address a knowledge gap in the literature. By alternating imaging of dendritic tufts and somas in the same animals, they compare compartment-specific activity during motor learning and identify distinct encoding of task variables and learning-related plasticity across these compartments. Interestingly, a subset of dendritic tufts shows activity associated with corrective actions. The findings are discussed in the context of current theories of dendritic computation, credit assignment, and motor learning, providing a useful foundation for future mechanistic studies.

Weaknesses:

No major weaknesses were identified.

Reviewer #1 (Public review):

Summary:

The non-social task was a classic risky decision-making task with a binary choice between an option with a sure gain and a risky option with a probabilistic gain or loss. In the social task, the sure option was an individual gain (as in the non-social option) and the probabilities in the risky option, which were shown to participants, were framed as probabilities of other previous participants (i.e., "partners") to cooperate or not; a probabilistic gain (when the partner cooperated) also led to a gain of the partner, while a probabilistic loss meant that the partner would receive the amount lost by the participant. This loss was framed as "betrayal." The authors show differences in how probabilities and amounts (of gains/losses) affected choices, RTs, and ERPs (P3 and LPP).

Strengths:

Since participants faced decisions with the same individual payoffs in a non-social and a social condition, this setup made it possible to use identical standard analyses for choices, RTs, and ERPS as well as (almost) identical economic models for the two conditions.

Weaknesses:

(1) The task does not include many components that are usually considered central for cooperation or "betrayal" and this is not discussed appropriately. At the same time, the "emotional aspects" of the operationalized "betrayal" are not directly assessed.

a) The standard economic game for cooperation is the prisoner's dilemma, in which participants make independent choices at the same time without getting any explicit information on the cooperation probability of their partner before they make their decisions. Furthermore, most of the time the interactions are repeated. Actually, the trust game as one other frequently used economic game, also includes a back and forth of transfers between the partners. So, here, I am not so convinced by the operationalization of a low cooperation probability, which is shown before the decision, as "betrayal." The authors should motivate and explain their rationale more clearly in reference to such other tasks.

b) The setup of the task, especially the fake interaction with the fake partners, should be made clearer in the main text (before reporting the results). I would argue for including the task picture in the main text.

c) In general, I am in favour of taking participants' choice behaviour as the main outcome measure. But given the strong implications of "emotional costs" made by the authors, I would have expected some ratings of "betrayal" on a trial-by-trial basis. I would at least include this as a shortcoming.

d) Also, given the framing of the study, I would have expected some exploratory analyses regarding individual differences with respect to, e.g., social value orientation, etc. I would at least include this as an outlook.

(2) The standard statistical analyses could be improved.

a) It is good that the authors have rather long sections using standard regression analyses. But they are a bit lengthy, and the modelling should be more prominent.

b) In a couple of places, the authors say something like "this is significant, but that is not." Here, it has been made very clear that the interaction term needs to be looked at. As far as I can see, this has not always been done.

c) For this binary choice, the difference in expected value (EV) between the sure and the risky options is one crucial comparison. But the authors never take that into account. This difference does not depend on the amount, which the authors dub "principal." That is, the sure option simply has an EV of x, i.e., the amount. The risky option has the EV = p2x + (1-p)0.5x, with p being the probability of gain/cooperation. That is, the two options have the same EV at p=1/3, independent of x. This should be made clear.

d) Relatedly, RTs should depend on the differences in EV (and not so much on p or on x per se). This can be seen by the more or less quadratic relationship between p and RTs (Fig 1A), with a peak around a p of 1/3.

e) RTs are often log-transformed. It should be briefly mentioned why this was not done here.

(3) The modelling evidence is relatively weak. This is my main point.

a) (Cumulative) prospect theory should be introduced.

b) The models seem overly complicated with many free parameters. I would have expected some simpler versions and more comparisons between models that differ in just one parameter.

- e.g., it is really nice that the authors used a probability weighting function. BTW: Please describe this more clearly in the introduction and in the results. But for this limited range of probabilities, this might be too much.

- e.g., why directly assume two different exponents in the utility function for gains and losses, and in addition a loss aversion parameter lambda? Only lambda would be a better starting point here.

c) The differences in AIC (Figure 2A) seem rather minuscule, and the distribution of winning models is not very peaked. I am not convinced that Model 3 is the winning model.

d) Crucially, and related to the previous points, judging from Fig 2C, the "betrayal" parameter kappa seems to be zero for about half of the participants. The authors should look into this.

- Would a model just like model 3 but without kappa (i.e., kappa set to zero) perform better? Is this just model 2?

- How is kappa set in the non-social condition?

- This massive skew, to say the least, is never discussed.

- A correlation is definitely not warranted.

(4) The ERP results seem to me rather superficial. But I am not an EEG expert.

a) The authors do not seem to look at the outcome phase, which could be interesting for differences in reward/loss processing in the two task versions.

b) Again, differences in EV seem to be more important from a conceptual point than probabilities or amounts; see my comment 2d.

c) Also, the authors report ERPs for the two task types separately but do not seem to run proper comparisons between them, see my comment 2b.

(5) Preregistration: It should be made very clear early on that this study was not preregistered.

(6) Quality checks: The authors should check if some participants are outliers in terms of the number of missed trials, always choosing the same option, etc. It is notoriously difficult to find good post hoc reasons for excluding participants (one reason why replications and preregistrations are important). In any case, the data quality should be checked and described a bit more.

Reviewer #2 (Public review):

Summary:

This paper investigates risk and cooperation decisions by integrating computational modeling with event-related potential (ERP) measures. Participants completed two tasks involving financial risk and cooperation under possible betrayal. The comparison between social and non-social decision-making is interesting and potentially valuable. However, the conceptual framing, theoretical grounding, and modeling rationale require substantial clarification.

Strengths:

(1) The paper introduces comparable tasks to probe social vs. non-social decision making.

(2) The authors use a model to identify a psychological distinction and test its validity using neural data.

Weaknesses:

(1) Conceptual framing and theoretical clarity

The primary theoretical contribution of the paper is currently unclear. Specifically, it is not clear what key difference the authors hypothesize between risk and cooperation conditions. This distinction should be grounded in prior literature.

The manuscript states: "Indeed, mutual cooperation maximizes social welfare, whereas betrayal benefits the trustee but comes at the trustor's expense in the Trust Game (Joyce et al., 1995)." However, the authors do not discuss the substantial literature on the Trust Game, which is used here but not explicitly acknowledged.

• The original Trust Game framework and behavior in one-shot settings (e.g., Berg et al., 1995).

• The persistence of cooperation even when defection is economically optimal (e.g., Berg et al., 1995; Fehr & Fischbacher, 2003).

• The influence of trustworthiness of the partner on cooperation decisions has been previously studied (Ma et al., 2022).

• Differences between social and non-social decision-making contexts have also been reported with matched tasks (Liu et al., 2024).

(2) Distinction between constructs (risk, loss aversion, betrayal aversion)

The introduction introduces multiple related constructs-risk aversion, loss aversion, and betrayal aversion-but does not clearly differentiate them. A theoretically grounded distinction is needed.

In particular:

• The manuscript introduces multiple related constructs, or maybe the terms are used interchangeably? The distinction between risk aversion, loss aversion, defection aversion, and betrayal aversion should be clearly defined.

• Betrayal aversion versus loss aversion is introduced but not clearly differentiated. Importantly, it should be clarified that this distinction is not experimentally manipulated but instead inferred through computational modeling. This point is currently not made explicit, which leads to confusion in the introduction

• The computational model should be introduced clearly in the introduction. Without explaining how these constructs are operationalized in the model, the framework is difficult to follow.<br /> The statement "In the risk task, losses were solely impersonal" is also unclear. It seems the authors may mean "personal or non-social" rather than "impersonal" as rewards are always personally relevant.

(3) Hypotheses and preregistration

The manuscript would benefit from more theoretical rationale for hypotheses. For example:

• What is the basis for hypothesizing that financial loss aversion and betrayal aversion independently affect cooperation choices?

• Why should these constructs be separable and modeled independently?

• Additionally, the absence of preregistration is a limitation that should be acknowledged even more.

• Given the flexibility of the modeling approach and number of parameters, this is particularly important.

• For instance, the rationale for focusing on decision times is also not clearly explained and should be better motivated.

(4) Computational modeling

There are several concerns regarding the modeling approach:

• The choice of model comparison metric should be justified. Why is AIC used rather than BIC, which penalizes model complexity more strongly? This is particularly relevant given the inclusion of additional parameters to capture processes not directly measured by the task.

• Full model recovery analyses are missing. A full model recovery is necessary to demonstrate that competing models produce distinguishable behavioral patterns. This needs to be shown in order to justify the specificity of the winning model

• How correlated are the parameters across participants, particularly loss and betrayal parameters?

• More broadly, it is unclear how well loss aversion and betrayal aversion can be differentiated based on behavior alone. If these constructs are separable, they should predict distinct aspects of behavior.

(5) ERP analyses

The ERP results (e.g., P300 and LPP) seem to suggest that betrayal aversion is relevant in both time periods and similarly.

• Do neural signals differentially reflect betrayal aversion versus loss aversion earlier and later on?

• Are there significant interaction effects between betrayal and loss aversion for each ERP component?

Reviewer #3 (Public review):

Summary:

In this study, the authors aim to address two questions. First, do people avoid cooperation primarily because of betrayal aversion beyond loss aversion? Second, can the effects of betrayal aversion and loss aversion be dissociated at the behavioral and neural levels? To address these questions, the authors compared individuals' choices of taking risks in a nonsocial risk task with those in a social cooperation task, with the two tasks matched in success probability and principal amount. They fitted computational models that include betrayal-aversion and loss-aversion terms and related the model parameters to ERP measures. Based on these analyses, the authors concluded that betrayal aversion has a stronger effect on cooperation than loss aversion and that betrayal is encoded earlier than loss in the brain. This is an important research question, and the attempt to combine computational modeling with ERP analysis is valuable. However, the current data analyses may not be able to support all the conclusions the authors made. For instance, the claims concerning the dissociation between betrayal aversion and loss aversion are not yet sufficiently supported by the evidence.

Strengths:

(1) The research question is theoretically important. Distinguishing betrayal aversion from loss aversion is important for research on trust, cooperation, and risky decision-making.

(2) The approach of integrating behavioral measures, self-report ratings, computational modeling, and ERP data is valuable and gives the study significance.

(3) The behavioral findings are broadly consistent. Participants reported stronger emotional responses in the cooperation task and were less willing to accept risk in the cooperation condition. These findings are generally in line with previous work on betrayal aversion and provide a reasonable manipulation check for the contrast between social and nonsocial risk.

Weaknesses:

(1) The manuscript states that the two tasks are matched in probability and principal amount, but the cooperation task additionally introduces partner outcomes, betrayal, and prosocial components. The Methods section states that, in the cooperation task, if both players cooperate, the principal is doubled and then split equally; if the partner betrays, half of the participant's principal is transferred to the partner. The model also includes an expected-other-reward term, namely, V_other=ω[p⋅2X+(1-p)⋅1.5X]. This raises an interpretive concern: if the two tasks differ not only in whether the source of uncertainty is social, but also in partner outcome, intentionality, and potential inequity structure, then the fitted "betrayal aversion" parameter may in fact reflect multiple motives rather than betrayal aversion alone. In the current experimental design, the "betrayal aversion" parameter may not be uniquely interpretable as a pure betrayal-specific construct, and the current evidence is insufficient to support such a specific interpretation.

(2) Participants were informed that the cooperation probabilities were derived from previous real participants, whereas in fact these probabilities were randomly generated. In addition, six participants explicitly expressed doubts about the authenticity of the social interaction, yet the authors retained these participants with only the brief statement that this "did not affect the results." For such a critical manipulation, this explanation is too brief. I recommend that the authors report robustness analyses excluding skeptical participants. Since six participants reportedly doubted the authenticity of the social interaction, and some participants also performed poorly on the catch trials, it would be important to show whether the main behavioral, modeling, and ERP findings remain after excluding these participants. This is especially important because the manuscript's central interpretation depends on the assumption that the cooperation task was genuinely experienced as social.

(3) The descriptions of the sample size are inconsistent across sections. The Participants section states that, after excluding one participant for misunderstanding the instructions, the final sample consisted of 49 participants; however, the behavioral results section later states that only 42 participants were included in the final analyses due to recording problems. This discrepancy is important because readers need to know clearly which sample was used for the behavioral analyses, which for the model fitting, and which for the ERP analyses; whether these analyses were conducted on the same participants; and whether the exclusion criteria were consistent across analyses. The manuscript needs a more transparent description of sample size and exclusion criteria.

(4) The authors need to do more thorough analyses to validate their models. In addition to AIC and parameter recovery, I would encourage the authors to include other model comparison metrics where possible, such as BIC and exceedance probability, as well as model-recovery analyses. The authors should also do model-based simulation analyses to show that the winning model can capture the contextual effects observed in real data.

(5) The authors should explain the rationales for the choice of ERP time windows and component selection in more detail. The current ERP analyses are time-locked to principal onset, and P3/LPP are extracted from fixed time windows. The authors should explain why this is the most appropriate time-locking point for examining betrayal- and loss-related computations, and why alternative time-locking points, such as probability-cue onset or other key task events, were not used. More importantly, the time windows of P3 and LPP are defined arbitrarily in the current analyses. The authors need to apply a more principled approach to define ERP components. It looks like the P3 and LPP are from the same ERP component in Figure 3.

(6) The manuscript has several internal inconsistencies in terminology, figure references, and result descriptions. These issues weaken the clarity of the arguments and reduce the readability of the manuscript.

(7) The authors partially achieved their aims. The study does provide evidence that social risk and nonsocial risk are not treated equivalently, and it also offers a computational framework that is informative for the field. This is an important topic, and the overall approach is promising.

Reviewer #1 (Public review):

Summary:

In this manuscript, Demeshkina and Ferré-D'Amaré showed that extrachromosomal circular DNA (eccDNA) and chromatin-associated proteins are present in stress granules, based on proteomic and sequencing analyses. Using HCR-FISH combined with imaging, the authors showed the colocalization of eccDNA with stress granule proteins. Furthermore, they found that CRISPR machinery targeting the eccDNA component of stress granules disrupts stress granule assembly, and that this effect is largely independent of Cas9 endonuclease activity. Notably, expression of cytoplasmic chromatin factors restores stress granule formation in the presence of CRISPR machinery in yeasts. This also rescues the growth defect caused by hypoxic stress, which correlates with impaired stress granule formation. Together, this manuscript provides insight into the presence of eccDNA in cytoplasmic membraneless organelles, specifically stress granules, and suggests a functional role for eccDNA within these structures under stress conditions.

Strengths:

The authors used a panel of ribonucleases to demonstrate that stress granule cores isolated from yeast and HEK293 cells are resistant to plasmid-safe DNase, an enzyme that does not degrade circular double-stranded DNA. To further support the presence of extrachromosomal circular DNA (eccDNA) in stress granules, they performed Circle-Seq on stress granule cores. The gel electrophoresis and sequencing experiments complement each other well, providing consistent evidence for eccDNA within these granules. Overall, this study provides insight into potential cytoplasmic roles for eccDNA, an area that remains largely unexplored.

Weaknesses:

(1) Figure 1F suggests that stress granule cores are susceptible to DNase I but not to plasmid-safe DNase (psDNase). However, its smearing pattern in the psDNase condition appears similar to that in the DNase I treatment shown in Figure 1E, although psDNase produces more discrete bands. The authors should comment on these differences between Figures 1E and 1F, or consider revising Figure 1F to improve consistency with Figures 1E and 1D.

(2) The authors should clearly define "colocalization". Does it refer to complete spatial overlap between two signals (i.e., VCP and T30), or partial overlap (i.e., AHNAK DNA and G3BP)? Figure 3 and the associated text are descriptive. Quantitative analysis would strengthen the conclusions. For example, the authors could analyze the fraction of molecules localized to stress granules or provide Pearson's correlation coefficient or similar measurements.

(3) The authors used a CRISPR-based approach to target the Ty1 LTR retrotransposon, an abundant stress granule eccDNA, and they observed a loss of stress granule formation. However, this phenotype may be specific to Ty1 eccDNA rather than representative of all eccDNA species present in granules. In particular, the title "Cytoplasmic circular DNA is a key constituent of stress granules" implies a broader role. To support this claim, the authors should consider approaches that more globally deplete eccDNA rather than targeting a single eccDNA.

(4) The authors should provide additional experimental evidence to support the claim that eccDNA is packaged in a chromatin-like state. The rescue of stress granule formation by ectopic expression of modified chromatin-associated proteins (CHD1NES and GCN5NES) following CRISPR treatment does not necessarily demonstrate that eccDNA is packaged like chromatin under basal conditions.

Reviewer #2 (Public review):

Summary:

The authors report the presence of extrachromosomal circular DNAs (eccDNAs) within the core of stress granules purified from both yeast and mammalian cells.

Strengths:

This study is important for understanding the molecular mechanisms underlying stress granules containing eccDNAs and is likely to have a major impact on future research. A major strength of the study is the extensive experimental validation performed in yeast cells. In particular, cytoplasmic CRISPR-mediated targeting of eccDNAs suppresses stress granule formation and impairs recovery from hypoxic stress in yeast cells.

Weaknesses:

The conclusions would be further strengthened by validating the functional findings in an additional model system, such as mammalian cells.

Comments:

(1) Section: "Stress granule cores contain eccDNA"

a) The presence of eccDNAs would be more convincingly demonstrated using an orthogonal validation approach, such as DNA FISH targeting MYC and Centromere 8 (CEN8) on metaphase spreads from HEK293T cells (as performed in PMID: 34819668).

b) The study would also benefit from assessing the presence of eccDNAs in the extracellular medium. For example, DNA could be extracted from conditioned media and analyzed by PCR using primers spanning eccDNA breakpoint junctions (as performed in PMID: 40074906; PMID: 36123406).

(2) Section: "eccDNA-CRISPR abrogates stress granules"

These findings should be further validated under additional stress conditions, such as drug-induced stress (like methotrexate) or nutrient deprivation in the cell medium.<br /> In addition, the same set of experiments should be performed in HEK293T cells to support the broader relevance of the observations.

Reviewer #1 (Public review):

In this manuscript, the authors study optimal chemotactic navigation of bacteria in disordered environments. Most previous work has studied bacterial chemotaxis in free liquid, but navigation in obstructed environments is gaining more attention. Here, the authors first used the classic swim plate assay to select E. coli for chemotaxis in soft agar at two agar concentrations. In the higher concentration, they observed that the population's migration speed increased and the mean run duration decreased over selection cycles. Importantly, the growth rate did not change, so the change in migration speed was due to improved chemotaxis. Then, using a strain in which they could control the mean run duration with an inducible promoter, they measured population migration speed as a function of mean run duration, observing a peak. In liquid, theory predicts a peak when the run duration is comparable to the time scale of rotational diffusion. Here, the peak is at a much shorter run duration, and the optimal run duration decreased with agar concentration. A key feature in previous studies of bacterial motion in obstructed environments has been the dynamics of cell trapping and escape via tumbling. By directly visualizing the flagella in single cells, the authors found that the majority of trap events in semisolid agar did not end with a tumble. This is important because it means that the peak in the migration speed has a different origin from the peak typically seen in the diffusion coefficient, which is due to a balance between longer runs and less time spent trapped. Instead, using a minimal theoretical model, the authors argue that the peak in the migration speed is due to a balance between longer runs, which improve chemotaxis, and having those runs terminate with a tumble rather than a trap event, because runs that end with trapping do not result in up-gradient bias. Qualitatively similar behavior is seen in simulations of a more complex model of chemotaxis.

Overall, we find the results to be significant and the evidence to be strong. We have some comments, which the authors need to address to improve/clarify their work:

(1) The authors' model predicts that, because cells spontaneously escape traps without tumbling, the diffusion coefficient should depend monotonically on mean run length even though the chemotaxis coefficient is non-monotonic. It would strengthen the paper if the authors could show this to be true in experiments. Part of the reason for this comment is that the flagella labeling experiments were done in agar that was rapidly cooled in a freezer and then thawed, whereas the migration experiments were performed in agar cooled at room temperature. Our (anecdotal) understanding is that the cooling rate dramatically affects the properties of the agar mesh. Verifying that diffusivity is monotonic in mean run length would therefore show that cells' spontaneous escape from traps is not an artifact of the cooling protocol.

(2) Two agar densities were used in their study (0.2%, 0.3%). As shown in Figure 1, while cells in the 0.3% agar showed significant improvements during the directed evolutionary experiments, the cells in 0.2% agar didn't. Correspondingly, the evolved average run time did not show significant changes in the 0.2% agar, but it decreased in the 0.3% agar. What is the reason for this difference? Does it mean the cells are already optimized for the 0.2% agar medium?

(3) Related to the previous comment, the comparison between Figure 1 and Figure 2 should be made clearer. In Figure 2, a peak performance at an intermediate run time is shown, with the optimal run time decreasing with the agar density. Qualitatively, this result, i.e., the existence of the peak performance, gives the evolution experiments shown in Figure 1 a nice explanation. However, quantitatively, the run times shown in Figures 1 and 2 are quite different. For example, for the 0.3% agar case, the change of run time decreases from ~0.6sec. in cycle-1 to ~0.4sec in cycle-40. However, in Figure 2, the optimal run time is ~0.9sec., which means that the migration speed would decrease if the run time is decreased from 0.6sec to 0.4sec. We understand this may only be considered as a qualitative result. However, it does raise the question of what the molecular mechanisms are that drive the directed evolution, which the authors should address.

(4) In Figure 3B, the distributions of speed in different media (liquid versus agar) for cells with bundled and split flagella are shown. While the distribution for the bundled flagella shows nicely the emergence of the trapped state (peak near zero speed), the distribution for the split flagella shows a significant shift of the distribution. Does this mean the agar medium also changes the tumble state significantly? In fact, we are puzzled by the observation that in bulk liquid, the run speed distribution for cells with split flagella seems to be quite similar to that of cells with bundled flagella, which might indicate problems in determining run speed.

(5) Finally, none of the points plotted have error bars. Error bars would allow the readers to evaluate i) whether the changes in mean run speed during selection are significantly resolved and ii) whether the peaks in the migration speeds are significantly resolved.

Reviewer #2 (Public review):

Summary:

The manuscript by Bai and colleagues investigates how Escherichia coli navigates and explores agar gels through chemotaxis and what parameters of bacterial swimming are tuned under selection pressure for rapid migration (i.e., reaching the edge of the agar plate quickly). Prior studies have examined related questions to a substantial degree. Examples include "Migration of Chemotactic Bacteria in Soft Agar: Role of Gel Concentration" (https://pmc.ncbi.nlm.nih.gov/articles/PMC3145277) and numerous other studies in this area (e.g., "Migration of bacteria in semi-solid agar" https://www.pnas.org/doi/10.1073/pnas.86.18.6973). From such studies has emerged the paradigm/model that reorientation (i.e., tumbling) is essential when bacteria navigate agar, which is considered a model for "complex" environments, because run-only bacteria become trapped in the agar matrix and are unable to migrate far. This new manuscript provides some evidence that this paradigm may be overly simplified or incomplete. As I understand it, the authors propose that migration is influenced to a greater extent by bias in the chemotactic run, where runs up attractant gradients are longer. The authors incorporate these data into a new model for chemotactic navigation and claim that this work establishes a general principle for how bacteria optimize active transport through complex environments.

I will first note to the editor and authors that I am not qualified to assess the detailed mathematics of the model, and my review therefore focuses on the biology and phenotypes described. Nevertheless, in my view, this manuscript, in its current form, has several important limitations. For each point, I provide suggestions for additional experiments that could strengthen the rigor of the work and clarify the claims.

Strengths:

A strength of this work is the use of microscopy and automated methods to characterize an extremely large number of bacterial cells, which strengthens the authors' claims. However, substantially greater detail on these approaches is needed for the analysis to be reproducible and to allow verification that the analyses were performed correctly.

Weaknesses:

Major concerns

(1) Claims are overly broad, and the experimental system is too artificial to support general conclusions about bacteria, chemotaxis, or evolution.

E. coli MG1655 is a longstanding model organism in the chemotaxis field, and agar chemotaxis assays are also widely used. However, the authors make very broad claims about how phenotypic changes observed during selection in 0.2% or 0.3% agar relate to bacterial chemotaxis and evolution more generally. In essence, the experimental foundation on which the authors build a complex theoretical framework is limited to a domesticated laboratory strain of E. coli and a highly artificial environment consisting of agar in a Petri dish. Although E. coli is well studied, its motility and taxis behaviors are not necessarily representative of bacteria across nature. In addition, natural environments are dynamic, and bacteria rarely experience stable gradients for extended periods, such as the 24-hour time-frame used here. The authors have also only focused on responses to attractant gradients with undefined complex growth media, and not assessed if this is also true for repellent gradients. This is important to consider because E. coli also generates repellent gradients (indole) that are not considered here. E. coli also generates AI-2, sensed as an attractant, that would be an opposing force for migration. For these reasons, it is not clear that the data and theory presented here generalize to diverse bacterial species, to natural environments, or to chemotaxis broadly.

The authors should acknowledge that further work is needed to generalise their findings by testing additional organisms, such as non-laboratory E. coli isolates, other enteric bacteria, and species with fundamentally different motility systems (e.g., Campylobacter jejuni). Further work could also expand beyond agar by examining chemotaxis in a biological matrix such as mucin, as well as testing responses to defined attractants and repellents.

(2) No genetic component is identified, so claims about evolution are not supported.

Evolution requires heritable genetic changes that produce phenotypes advantageous under a given selection pressure. The authors state that bacteria were selected for rapid migration and that this selection produced progressively more efficient migrators. However, no sequencing analyses of the evolved isolates were performed, no genetic changes were identified, and no mechanism underlying this phenotypic shift was described. Without identifying genetic alterations, they cannot substantiate the claim that evolution occurred. Whole-genome sequencing of the evolved isolates is necessary to determine whether specific mutations underlie the observed phenotypes.

(3) The predictive power of the model is not tested.

The authors develop a model with post-dictive capability, meaning the model reproduces behaviors similar to those observed in the data used to construct it. However, the manuscript does not demonstrate that the model has predictive power. Demonstrating predictive performance would substantially increase the value of the model. For example, the authors could perform an additional round of selection and predict the resulting bacterial behavior under a condition not used during model construction (such as a different agar concentration or predicting the behavior of different bacteria). Otherwise, the authors should tone down the claims.

(4) Limited novelty and impact of the environmental difference studied.

A central point of the manuscript is the difference between evolution in 0.2% versus 0.3% agar and how this difference relates to the proposed model. However, this represents a relatively minor change in the environment experienced by the bacteria. Developing an extensive theoretical framework and proposing that bacterial evolution is highly sensitive to these parameters based on this narrow experimental system may be premature. This would be addressed by the suggested broadening of experiments described above.

(5) The manuscript is too brief, and some data and methods are insufficiently described, particularly related to the machine learning analysis.

The manuscript addresses a complex topic, yet the main text, methods, and figures are very brief, which need not be the case. As a result, it is often difficult to understand exactly what was done and how the data support the authors' claims. More detailed descriptions of the experimental approaches and analyses are necessary.

One example is the machine learning approach used for cell tracking. This method is only briefly described, and no validation data are presented that would allow readers to evaluate whether the approach performs accurately. If the method is robust, it would be a powerful analytical tool, but the current description does not provide sufficient information to evaluate the reliability of the results. This issue is particularly important because the authors conclude that tumbles account for less than 3% of escape events, which contrasts with previous paradigms. Automated tracking methods can be susceptible to artifacts, and therefore, rigorous validation of the tracking pipeline, supported by appropriate figures and benchmark data, is essential.

Reviewer #3 (Public review):

The manuscript by Bai et al presents a study of the effect of trapping on the efficiency of chemotactic spreading. While the overall impression of the study is positive, there are multiple drawbacks that accumulate and together make the statement of the paper not fully justifiable. Below, I provide some detailed comments in chronological order, and indicate those of particular importance.

(1) On the first page of the Introduction, the authors use the following wording: "...how bacteria optimise their intrinsic motility parameters to maximise navigation efficiency". However, it is not shown or known whether they do. In the experiments, the authors fetch the bacteria at the far front and artificially select the ones with shorter run times. The ones at the front could be the effect of heterogeneity of the population rather than an adaptation. Moreover, the authors claim that the selective pressure is via trapping. But this can be due to a multitude of other factors that change with agar concentration, availability of nutrients, osmotic properties of water, etc.

(2) At the beginning of the results section, the authors claim that for both agar concentrations, they observe a progressive increase in chemotactic navigation. I do not see how the data for 0.2 % agar would correspond to that. Migration speed remains flat.

(3) (Important). The authors claim that the mean run speed remained constant. But this is definitely not true, as seen in the plots. The speed of modernity is increasing for both agar conditions. And here it is important to note that the chemotactic drift velocity is proportional to the square of run speed (which is not the case for the formulas in this paper, see comment below). Thus, even smaller changes in v_0 can result in a significant increase in the drift velocity.

(4) (Important). Tumble bias is also significantly increasing in 0.3 agar concentration. While it is not clear from the paper what exactly the tumble bias is, if it is related to the persistence of the turning angle, this also has a linear effect on the chemotactic drift velocity.

(5) (Important). When performing aTc dependence testing, the authors didn't report how other observables of swimming behaviour are changing.

(6) (Very important). I'm not sure that by interfering with Che-Z expression, one does not affect the whole chemotactic circuit, for example, by changing G (in terms of the model) and thus the optimality occurs not due to the agar concentration/traps but due to the perturbations in the circuit. Also, the effect of different % seems to be much more minor compared to the overall induced changes in spreading speed.

(7) (Very important). I was very confused by the statement of the authors about only 3% of traps being exited due to tumble. I don't think this is possible (in a way consistent with the suggested model). Mean free run times (Figure 1C) go down to 0.4 s. Duration of tumbles is 0.3s (Figure S2c), but the duration of traps is longer than tumbles (and a bit shorter than runs). So how can it be that a running cell gets into a trap and only in 3% cases it experiences a tumble? What would be the distribution of run durations if one combines pre-trap+trap_time+post_trap run time - would they still have a mean below 1s?? It really looks like the authors are not able to detect tumbles when bacteria are trapped. Or is there an active mechanism suppressing tumbles when in the trap?

(8) It is not clear what it means that post-tumble angles were uniformly distributed. Does this refer to only trap-associated tumbles? It is known that in the freely swimming e.coli the tumbling angles are not isotropic but have a preference for the forward direction. Is it different in agar conditions?

(9) (Very important) The authors assume an oversimplified model for the chemotactic drift based on biased random walks. As a result, the answer for chemotactic drift velocity has a wrong scaling with run speed. In the linear theory of chemotaxis by de Gennes, the scaling is v_0^2, while the authors use a linear relationship. Thus, the assumption of the simplified model is incorrect. The exact effect of the traps (where no tumbling is happening, and the directional memory is conserved) needs to be properly calculated, for example, in the same de Gennes framework. And I can't say what the result would be from the top of my head because the calculation is, in fact, not too trivial. Thus, the model used is oversimplified, and thus the fact that it shows a non-monotonous relationship with tau_f is of little predictive power.

Taken together, you see that all the key points that are used in the chain of the argument about the optimality are not rock solid and allow for alternative explanations. I think all those either need to be tested explicitly or at least clearly discussed, and the respective conclusions of the paper need to be rephrased. In my view, this work needs major revision.