Reviewer #1 (Public review):

Summary:

The authors integrated bulk proteomics, single-nucleus RNA sequencing, and cellular communication pipelines to map molecular changes in the mouse lumbar spinal cord following endurance training versus acute exhaustive exercise. This kind of data is currently missing in the literature for the healthy spinal cord; therefore, this work represents a useful resource for the community for the investigation of cellular mechanisms of exercise-induced neuroplasticity. The authors found that endurance training elicited robust plastic transcriptional changes in the glia, in genes involved in synaptic modulation, axon development, and intercellular signaling, with cell-specific differences. Acute exhaustive exercise triggered a more nuanced biphasic temporal response in metabolic and synaptic genes, which was different in trained versus sedentary mice. Although cholinergic neurons did not show robust gene expression changes, they were found to be central hubs for communication with glia, suggesting that their cues may act as upstream regulators of glial plasticity.

Strengths:

Nuclei fixation minimized unwanted RNA degradation and tissue processing-driven expression changes. However, in the text, it needs to be acknowledged that the fixation step was performed only after nuclei isolation, and not at the stage of spinal cord tissue collection. The time course study design allowed for the distinction of different temporal gene expression trajectories.

Weaknesses:

No clear indication of the number of biological replicates is given. No validation of the key findings with alternative methods is presented.

Some aspects of data analysis need to be clarified:

(1) Methods

a) Voluntary exercise: the authors should indicate whether the mice were singly housed, and, if not, clarify that the indicated mean km/day is an average of the mice in the cage.

b) The Authors should indicate more precisely which lumbar level of the spinal cord was used and the number of biological replicates.

c) The Authors should indicate the number of highly variable features and PCs (dims) used for Seurat and provide a QC metric table.

(2) Results and Figures

a) Bulk proteomic analysis: The authors used Pval-and not FDR- to assess differentially abundant proteins. Can the author indicate how many proteins passed a more stringent FDR cutoff? For GO analysis: the authors should indicate what background/reference was used.

b) Figure 1B and Figure S1B-C: the differences in total mass and relative lean mass are very subtle, even if statistically significant. This needs to be acknowledged in the relevant sentences.

c) Figure 2 and Figure S2E panels G and H are inverted.

d) Heatmaps in Figures 1F and 2 Figure 2E-F: some of the proteins and genes listed in the text are not present in the heatmaps (TIM22 and FABP4; Smap25 and Slc4a4). Please check the correspondence of the text with the heatmap, and indicate with an arrow the listed proteins and genes.

e) Page 9 "trained mice displayed a modest increase of oligodendrocytes 24h": from the plot, it looks to me like a decrease rather than an increase.

f) Figure 4 depicts expression changes in selected metabolism and synaptic activity-related genes: it would be useful to add a table as a supplementary file with expression data of all the synaptic and metabolic genes in addition to the ones that were selected.

Reviewer #2 (Public review):

Mansingh et al., investigate the impact of voluntary wheel training and acute physical exercise on the transcriptomic and proteomic profile of spinal cord tissues from young adult mice. They first describe the proteomic and transcriptomic differences between sedentary mice and mice provided with running wheels for voluntary exercise. They show that voluntary physical exercise induces changes at a transcriptional level as well as at a proteomic level, with most of these effects restricted to glial cells. They further analyze the putative cell interactions that are induced in the context of physical training and describe the specificity of transcriptional changes in the different cell populations. Using the same multi-omics pipeline, the authors assess dynamic changes in sedentary and trained mice 6 and 24 hours following a bout of physical exercise until exhaustion. Importantly, they demonstrate that the impact of this single bout to exhaustion is modified in mice that have access to running wheels compared with sedentary mice, with a reduced amplitude of the reaction and a faster resolution of changes caused by exercise until exhaustion.

Altogether, this study provides a useful description of the transcriptional changes at play following voluntary physical training and, importantly, uncovers the role of this training in shaping future transcriptomic reactions to a stressful bout of exercise until exhaustion. However, the conclusions of the manuscripts would be strengthened by the clarification of the methods, a better use of the proteomic data regarding the transcriptomic datasets, and a cross-validation of the main claims currently based solely on transcriptomic datasets.

(1) In this study, the housing strategy used is key as it will impact both the proteome and transcriptome of cells in the central nervous system. It can be difficult to measure the running activity of individual mice if they are not housed individually. Yet, individual housing has a major impact on the nervous system and notably on glial cells. Therefore, a better description of the housing strategy for the sedentary and trained group during the 6 weeks of training is required.

(2) In the first part of the paper that uses the results from the first set of multi-omics data, the protocol used is not clear. From Figure 1A, it seems that the mice went through a max performance test before and after the 6-week period in which the two groups had different life experiences (voluntary running versus sedentary). Since in the methods the maximal test protocol is effectively an exercise until exhaustion, it is difficult to understand why the authors defined this first experiment as the one allowing them to test "molecular remodeling in the spinal cord at rest". Also, it is not clear how long after the max performance test the tissues were collected. If indeed the mice went through the max endurance test before tissue collection, it is not a condition at rest, and this first protocol in some way looks like a duplication of a subpart of the second experiment. If mice did not go through this max performance test, it needs to be clarified both in the text and in the figure.

(3) One of the strengths of this study is its multi-omics approach assessing changes at both transcriptomic and proteomic levels. Yet, the use by authors of the proteomic datasets is minimal, and there are no comments on how the proteomic and transcriptomic datasets support each other. Changes at the transcriptional level do not necessarily translate into changes at the protein level. Therefore, it would improve the quality of the study if authors could use the bulk proteomic data in relation to the transcriptomic dataset. The fact that the proteomic datasets do not provide the identity of the cells from which the changes originate should not prevent authors from putting them in perspective with transcriptomic results.

(4) None of the results from the single-nucleus RNA sequencing are cross-validated with, for instance, in situ hybridizations. It would improve the strength of the claim if some findings, in particular regarding the dynamics of the changes 6 vs 24h after exhaustion bout, were cross-validated.

(5) Although the authors note as a limitation that cholinergic neurons were underrepresented in their dataset, since one of the main claims of the manuscript relates to them, it calls for some additional comments on the identity of the cholinergic neurons present in their dataset. There are different populations of spinal cholinergic neurons with very different functions. It would greatly improve the strength of this result if the authors could identify which cholinergic neurons show these changes (or at least which proportion of the different cholinergic population is present in their datasets). For instance, which proportion of cholinergic neurons are expressing classical markers of motor neurons versus markers of cholinergic interneurons (for instance, from the V0c population).

Reviewer #3 (Public review):

Summary:

Mansingh et al. used single-nucleus transcriptional and bulk proteomic profiling to characterize how gene expression changes in the lumbar spinal cord of adult, healthy mice after training (voluntary wheel-running exercise) and acutely after forced treadmill exercise. They found (1) that training was associated with a number of differentially expressed proteins, (2) training was associated with cell-type specific changes in transcription, notably glial cells had the highest numbers of differentially expressed genes, and (3) that trained mice had blunted transcriptional response to an acute exercise bout compared to sedentary mice.

Strengths:

The characterization of the changes to the proteome and the transcriptome associated with exercise will undoubtedly be a useful resource for scientists interested in the effects of exercise on central nervous system gene expression and may inspire mechanistic follow-up studies. The authors nicely use pathway and intercellular communication analyses to distill the complex dataset into key trends.

Weaknesses:

Weaknesses of this paper include two aspects of the analyses that underexplored the rich dataset. The analysis fails to explicitly compare the proteome and transcriptome results. Do the differentially expressed proteins correspond to the differentially expressed genes? If so, in which cell types? If not, why not? Comparison of the GO terms from the proteome dataset and the GSEA terms from the single-nucleus transcriptome dataset suggests that the same gene families were not identified in both data sets. I expect that integrating analyses across these datasets would help make the study truly multi-omic and highlight which expression changes are the most abundant and consistent across approaches. Second, the authors emphasize that related studies do not account for inter-individual variability in both the introduction and discussion. This aspect of the authors' dataset is also underexplored - the transcriptomic data appear to be pooled across animals, and only a single panel shows protein expression from individual animals (Fig. 1F). Is the variability in Figure 1F explainable by the amount of running on the wheel?

Reviewer #1 (Public review):

Summary

This study examines how working memory (WM) influences perceptual decisions, with the aim of distinguishing fast attentional capture-like effects from slower, sustained perceptual biases. The authors use a dual-task design in which a perceptual estimation task is embedded within a WM delay, combined with a time-resolved analysis of mouse tracking reports and hierarchical Bayesian modeling. This approach reveals two temporally distinct signatures of WM-perception interactions within single trials, arguing against a unitary account of WM-driven perceptual bias and instead supporting multiple processes that operate over different timescales.

Strengths

A major strength of the study is its innovative use of a time-resolved mouse trajectory analysis to move beyond endpoint measures and reveal the dynamic evolution of decision biases. By decomposing trajectories into components that are and are not explained by the final response, the authors provide compelling evidence for an early transient deviation and a slower, endpoint-consistent drift. The combination of rigorous experimental design, hierarchical Bayesian modeling, and converging analyses yields compelling support for the central claims and offers a valuable framework for studying top-down influences on perception.

Weaknesses/points requiring clarification:

(1) The primary weakness concerns the clarity of the theoretical framing linking the identified trajectory components specifically to attentional capture and representational (or perceptual) shift. While the manuscript reviews prior work on attentional and perceptual biases, the conceptual transition to the proposed distinction between capture and representational shift would benefit from a stronger connection to the existing literature. Clarifying this relationship would strengthen the interpretation of the results.

(2) The use of the term "continuous" to describe the trajectory analyses may be confusing for readers, as it could be interpreted as referring to a continuous task rather than a time-resolved analysis of movements performed to make a discrete response.

(3) Figures 2 and 7 present posterior distributions of hierarchical Bayesian parameter estimates for endpoint responses in Experiments 1 and 2. However, they do not show how these model estimates relate to the raw behavioral data. Including model fits alongside the observed data would help readers assess the quality of the fits and better evaluate how well the modeling captures the underlying behavioral responses. Similarly, it would be helpful to see individual means in Figure 3a, panel 2, as is done in Figure 4.

Reviewer #2 (Public review):

Summary:

This manuscript investigates the mechanisms by which visual working memory (WM) interacts with perceptual judgements, using continuous mouse-tracking to dissociate putative attentional capture from representational shift. Across two experiments, participants maintained a color in WM while performing an intervening perceptual matching task. Analyses of mouse trajectories revealed bidirectional influences with distinct dynamics of attentional capture and representational shift components. For WM's influence on perceptual judgments, trajectories showed a fast and endpoint-inconsistent deviation (interpreted as attentional capture by WM-matching features), followed by a slower and sustained drift that closely matched the final perceptual bias. In contrast, when perceptual judgments influenced subsequent WM recall, trajectory dynamics were dominated by the sustained drift component, with minimal capture-like deviation. Together, these findings are interpreted as evidence that WM shapes perceptual decisions through at least two temporally distinct processes.

Strengths:

I find the paradigm to be cleverly designed and the analyses rigorous. A major strength of this work is the use of continuous mouse-tracking and time-resolved analyses to dissociate transient influences from sustained biases within single trials. The trajectory decomposition provides an elegant way to separate early deviations from later drift, which would be difficult to achieve using traditional measures that only measure the final recall. I find the observation particularly compelling that trajectories initially deviate toward WM-matching information and then correct back toward the task-relevant target, highlighting the dynamic interplay between transient priority signals and the final decision.

Weaknesses:

(1) The early curvature in the mouse trajectory, inconsistent with the endpoint, is interpreted as fast attentional capture. However, this signal may also reflect competition among multiple responses driven simultaneously by the WM representation and the perceptual matching item. While the current interpretation is plausible, it would be helpful if the authors could more clearly articulate why this component should be solely interpreted as attentional capture rather than early response competition.

(2) The mouse trajectories show a clear correction back toward the target later in the movement, particularly when the cursor enters the color wheel (Figure 3a), where the correction appears most pronounced. I wonder how this corrective phase should be interpreted. For example, does this correction reflect disengagement from an initial WM-driven priority signal, increasing influence of task demands and sensory evidence, or some other control process?

Relatedly, movement onset latency modulated the overall AUC but did not influence the final perceptual error. I wonder whether the time courses of the capture and shift components (as revealed by the destination-vector transformation) differ between early-onset and late-onset trials, and if so, when those differences emerge. Explicitly showing these comparisons would help further clarify how early capture is corrected while the endpoint bias remains stable. It may also be informative to include representative raw trajectory paths for early- and late-onset trials, as Figure 3a is currently the only figure showing raw trajectories, whereas most subsequent results are derived measures.

(3) The contrast in destination-vector dynamics between the perceptual matching response and the WM recall response (Figure 8) is interesting. For the representational shift component, the effect appears to increase sharply after movement onset. Conceptually, one might expect the shift in WM representation to have already occurred following perceptual judgment, rather than emerging during the response itself. It would be helpful if the authors could clarify why the shift is expressed primarily during the movement phase. Additionally, although weak, there appears to be a small capture-like deviation in the WM recall trajectories. Was this effect statistically significant? It may be informative to apply the same cluster-based permutation analysis directly comparing the capture effects against zero, in addition to the paired comparisons currently reported.

Reviewer #1 (Public review):

Summary:

Zeng et al. characterized the dynamic brain states that emerged during episodic encoding and the reactivation of these states during the offline rest period in children aged 8-13. In the study, participants encoded scene images during fMRI and later performed a memory recognition test. The authors adopted the BSDS approach and identified four states during encoding, including an "active-encoding" state. The occupancy rate of, and the state transition rates towards, this active-encoding state positively predicted memory accuracy across participants. The authors then decoded the brain states during pre- and post-encoding rests with the model trained on the encoding data to examine state reactivation. They found that the state temporal profile and transition structure shifted from encoding to post-encoding rest. They also showed that the mean lifetime and stability (measured with self-transition probability) of the "default-mode" state during post-encoding rest predict memory performance.

Strengths:

How brain dynamics during encoding and offline rest support long-term memory remains understudied, particularly in children. Thus, this study addresses an important question in the field. The authors implemented an advanced computational framework to identify latent brain states during encoding and carefully characterized their spatiotemporal features. The study also showed evidence for the behavioral relevance of these states, providing valuable insights into the link between state dynamics and successful encoding and consolidation.

Weaknesses:

(1) If applicable, please provide information on the decoding performance of states during pre- and post-encoding rests. The Methods noted that the authors applied a threshold of 0.1 z-scored likelihood, and based on Figure S2, it seems like most TRs were assigned a reinstated state during post-encoding rest. It would be useful to know, for the decodable TRs, how strong the evidence was in favor of one state over others. Further, was decoding performance better during post- vs. pre- encoding rest? This is critical for establishing that these states were indeed "reinstated" during rest. The authors showed individual-specific correlations between encoding and post-encoding state distribution, which is an important validation of the method, but this result alone is not sufficient to suggest that the states during encoding were the ones that occurred during rest. The authors found that the state dynamics vary substantially between encoding and rest, and it would be helpful to clarify whether these differences might be related to decoding performance. I am also curious whether, if the authors apply the BSDS approach to independently identify brain states during rest periods (instead of using the trained model from encoding), they find similar states during rest as those that emerged during encoding?

(2) During post-encoding rest, the intermediate activation state (S1) became the dominant state. Overall, the paper did not focus too much on this state. For example, when examining the relationship between state transitions and memory performance, the authors also did not include this state as a part of the analyses presented in the paper (lines 203-211). Could the author report more information about this state and/or discuss how this state might be relevant to memory formation and consolidation?

(3) Two outcome measures from the BSDS model were the occupancy rate and the mean lifetime. The authors found a significant association with behavior and occupancy rate in some analyses, and mean lifetime in others. The paper would benefit from a stronger theoretical framing explaining how and why these two different measures provide distinct information about the brain dynamics, which will help clarify the interpretation of results when association with behavior was specific to one measure.

(4) For performance on a memory recognition test, d' is a more common metric in the literature as it isolates the memory signal for the old items from response bias. According to Methods (line 451), the authors have computed a different metric as their primary behavioral measure (hits + correction rejections - misses - false alarms). Please provide a rationale for choosing this measure instead. Have the authors considered computing d' as well and examining brain-behavior relationships using d'?

(5) While this study examined brain state dynamics in children, there was no adult sample to compare with. Therefore, it is hard to conclude whether the findings are specific to children (or developing brains). It would be helpful to discuss this point in the paper.

Reviewer #2 (Public review):

This paper investigates the latent dynamic brain states that emerge during memory encoding and predict later memory performance in children (N = 24, ages: 8 -13 years). A novel computational approach (Bayesian Switching Dynamic Systems, BSDS) discovers latent brain states from fMRI data in an unsupervised and parameter-free manner that is agnostic to external stimuli, resulting in 4 states: an active-encoding state, a default-mode state, an inactive state, and an intermediate state. The key finding is that the percentage of time occupied in the active-encoding state (characterized by greater activity in hippocampal, visual, and frontoparietal regions), as well as greater transitions to this state, predicts memory accuracy. Memory accuracy was also predicted by the mean lifetime and transitions to the default-mode state (characterized by greater activity in medial prefrontal cortex and posterior cingulate cortex) during post-encoding rest. Together, the results provide insights into dynamic interactions between brain regions that may be optimal for encoding novel information and consolidating memories for long-term retention.

The approach is interesting and important for our understanding of neural mechanisms of memory during development, as we know less about dynamic interactions between memory systems in development.

Moreover, the novel methodology may be broadly useful beyond the questions addressed in this study. The manuscript is well-written and concise. Nonetheless, there are several areas for improvement:

(1) The study focuses on middle childhood, but there is a lack of engagement in the Introduction or Discussion about what is known about memory development and the brain during this period. Many of the brain regions examined in this study, particularly frontoparietal regions, undergo developmental changes that could influence their involvement in memory encoding and consolidation. The paper would be strengthened by more directly linking the findings to what is already known about episodic memory development and the brain.

(2) A more thorough overview of the BSDS algorithm is needed, since this is likely a novel method for most readers. Although many of the nitty-gritty details can be referenced in prior work, it was unclear from the main text if the BSDS algorithm discovered latent states based on activation patterns, functional connectivity, or both. Figure 1F is not very informative (and is missing labels).

(3) A further confusion about the BSDS algorithm was whether it necessarily had to work on the rest data. Figure 4A suggests that each TR was assigned one of the four states based on the maximum win from the log-likelihood estimation. Without more details about how this algorithm was applied to the rest data, it is difficult to evaluate the claim on page 14 about the spontaneous emergence of the states at rest.

(4) Although the BSDS algorithm was validated in prior simulations and task-based fMRI using sustained block designs in adults, it is unclear whether it is appropriate for the kind of event-related design used in the current study. Figure 1G shows very rapid state changes, which is quantified in the low mean lifetime of the states (between 1-3 TRs on average) in Figure 4C. On the one hand, it is a strength of the algorithm that it is not necessarily tied to external stimuli. On the other hand, it would be helpful to see simulations validating that rapid transitions between states in fMRI data are meaningful and not due to noise.

(5) The Methods section mentions that participants actively imagined themselves within the encoded scenes and were instructed to memorize the images for a later test during the post-encoding rest scan. This detail needs to be included in the main text and incorporated into the interpretation of the findings, as there are likely mechanistic differences between spontaneous memory replay/reinstatement vs. active rehearsal.

(6) Information about the general linear model used to discover the 16 ROIs that showed a subsequent memory effect are missing, such as: covariates in the model (motion, etc.), group analysis approach (parametric or nonparametric), whether and how multiple-comparisons correction was performed, if clusters were overlapping at all or distinct, if the total number of clusters was 16 or if this was only a subset of regions that showed the effect.

Reviewer #3 (Public review):

Summary:

This paper uses a novel method to look at how stable brain states and the transitions between them promote memory formation during encoding and post-encoding rest in children. I think the paper has some weaknesses (detailed below) that mean that the authors fall short of achieving their aims. Although the paper has an interesting methodological approach, the authors need better logic, and are potentially "double dipping" in their results - meaning their logic is circular. I think the method that they are using could be useful to the broader neuroimaging community, although they need to make this argument clearer in the paper.

Strengths:

The paper is interesting in that they use a novel method to look at brain state dynamics and how they might support memory.

Weaknesses:

The paper has several weaknesses:

(1) The authors use children as their study subjects but fail to reconcile why children are used, if the same phenomena are expected to be seen in adults (or only children), and if and how their findings change with age across an age range that ranges from middle childhood into early adolescence. They need to include more consideration for the development of their subject population. The authors should make it clear why and how memory was tested in children and not adults. Are adults and children expected to encode and consolidate in a similar manner to children? Do the findings here also apply to adults? Do the findings here also apply to adults? How was the age range of 8-13-year-old children selected? Why didn't the authors look at change with age? Does memory performance change with age? Do the BSDS dynamics change with age in the authors' sample?

(2) The authors look for brain state dynamics within a preselected set of ROIs that are selected because they display a subsequent memory effect. This is problematic because the state that is most associated with subsequent memory (S3, or State 3) is also the one that shows most activity in these regions (that have already been a priori selected due to displaying a subsequent memory effect). This logic is circular. It would be helpful if they could look at brain state dynamics in a more ROI agnostic whole brain approach so that we can learn something beyond what a subsequent memory analysis tells us. I think the authors are "double dipping" in that they selected regions for further analysis based on a subsequent memory association (remembered > forgotten contrast) and then found states within those regions showing a subsequent memory effect to further analyze for being associated with subsequent memory. Would it be possible instead to do a whole-brain analysis (something a bit more agnostic to findings) using the BSDS framework, and then, from a whole-brain perspective, look for particular brain states associated with subsequent memory? As it stands, it looks like S3 (state 3) has greater overall activation in all brain regions associated with subsequent memory, so it makes sense that this brain state is also most associated with subsequent memory. The BSDS analysis is therefore not adding anything new beyond what the authors find with the simple subsequent memory contrast that they show in Figure 1C. This particularly effects the following findings: (a) active-encoding state occupancy rate correlated positively with memory accuracy, (b) transitions to the active-encoding state were beneficial / Conversely, transitions toward the inactive state (S4) were detrimental, with incoming transitions showing negative correlations with memory accuracy / The active-encoding state serves as a "hub" configuration that facilitates memory formation, while pathways leading to this state enhance performance and transitions away from it impair encoding.

(3) The task used to test memory in children seems strange. Why should children remember arbitrary scenes? How this was chosen for encoding needs to be made clear. There needs to be more description of the memory task and why it was chosen. Why was scene encoding chosen? What does scene encoding have to do with the stated goal of (a) "Understanding how children's brains form lasting memories", (b) "optimizing education" and (c) "identifying learning disabilities"? What was the design of the recognition memory test? How many novel scenes were included in the test, and how were they chosen? How close were the "new" images to previously seen "old" images? Was this varied parametrically (i.e., was the similarity between new and old images assessed and quantified?)

(4) They ultimately found four brain states during encoding. It would be helpful if they could make the logic and foundation for arriving at this number clear.

(5) There is already extant work on whether brain states during post-encoding rest predict memory outcomes. This work needs to be cited and referred to. The present manuscript needs to be better situated within prior work. The authors should look at the work by Alexa Tompary and Lila Davachi. They have already addressed many of the questions that the authors seek to answer. The authors should read their papers (and the papers they cite and that cite them) and then situate their work within the prior literature.

More minor weaknesses:

(1) The authors should back up the claim that "successful episodic memory formation critically depends on the temporal coordination between these systems. Brain regions must coordinate their activity through dynamic functional interactions, rapidly reconfiguring their activity and connectivity patterns in response to changing cognitive demands and stimulus characteristics." Do they have any specific evidence supporting this claim?

(2) These claims seem overstated: "this work has broad implications for understanding memory function in children, for developing educational interventions that enhance memory formation, and enabling early identification of children at risk for learning disabilities." Can the authors add citations that would support these claims, or if not, remove them?

Reviewer #1 (Public review):

This is a high-quality and extensive study that reveals differences in the self-assembly properties of the full set of 109 human death fold domains (DFDs). Distributed amphifluoric FRET (DAmFRET) is a powerful tool that is applied here for a comprehensive examination of the self-assembly behaviour of the DFDs, in non-seeded and seeded contexts, and allows comparison of the nature and extent of self-assembly. The work reveals the nature of the barriers to nucleation in the transition from low to high AmFRET. Alongside analysis of the saturation concentration and protein concentration in the absence of seed, the work demonstrates that the subset of proteins that exhibit discontinuous transitions to higher-order assemblies are expressed more abundantly than DFDs that exhibit continuous transitions. The experiments probing the ~20% of DFDs that exhibit discontinuous transition to polymeric form suggest that they populate a metastable, supersaturated form, in the absence of cognate signal. This is suggestive of a high intrinsic barrier to nucleation.

The differences in self-assembly behaviour are significant and highlight mechanistic differences across this large family of signalling adapter domains, with identification of a small number of key supersaturated adapters, which exhibit higher centrality within networks, and can amplify signals and transduce them to effectors as required. The description of some supersaturated DFD adaptors as long-term, high-energy storage forms or phase change adaptors is attractive and is a framework that addresses many of the requirements for on-demand signaling and amplification in innate immunity. The identification of only a small number of key adaptors and high specificity suggests a mechanism for insulation of pathways from each other and minimisation of aberrant lethal consequences.

An optogenetic approach is applied to initiate self-assembly of CASP1 and CASP9 DFDs, as a model for apoptosome initiation in these two DFDs with differing continuous or discontinuous assembly properties. This comparison reveals clear differences in the stability and reversibility of the assemblies, supporting the authors' hypothesis that supersaturation-mediated DFD assembly underlies signal amplification in at least some of the DFDs. The study also reveals interesting correlations between supersaturation of DFD adapters in short- and long-lived cells, suggestive of a relationship between mechanism of assembly and cellular context. Additionally, the interactions are almost all homomeric or limited to members of the same DFD subfamily or interaction network and examination of bacterial proteins from innate immunity operons suggest that their polymerisation could be driven by similar mechanisms. Future detailed studies that probe the roles and activities of DFDs identified with continuous or discontinuous barriers to nucleation, through mutational analysis, in chimeric proteins and with high resolution studies of the assemblies, can build on this methodology and database.

The Discussion effectively places this work in the context of innate immunity effectors and adapters, explains and provides a justification of the phase change material analogy, and contrasts this mechanism with phase separation. The breadth and depth of the experimental investigations allow a new view of the role of nucleation barriers and supersaturation in DFD assembly and innate immunity pathways.

Reviewer #2 (Public review):

This work studies the self-association behavior of 109 human Death Fold Domains (DFD) in eukaryotic cells and its connection to their function in innate immune signalosomes.

Using an amphifluoric FRET (DAmFRET) method previously developed by the authors, self-association is monitored as a function of protein concentration by Förster Resonance Energy Transfer in the cell.

Several DFDs are found to be in a supersaturable state and are considered energy reservoirs necessary for signal amplification.

The revised manuscript addresses most of the original concerns, resulting in a significant improvement.

The following observations are made:

(1) A group of DFDs shows a bimodal FRET distribution of no FRET and high FRET values at low and high protein concentration, which indicates a nucleation barrier. This conclusion is corroborated by the modification from a discontinuous to a continuous FRET transition by expressing a structural template or seed. The authors find that DFDs displaying discontinuous FRET behavior are supersaturated, and those that retain their discontinuous behavior in the context of the full-length protein correspond to protein adaptors of innate immune signalosomes.

(2) The authors indicate that the adaptors of inflammatory signalosomes act as energy reservoirs for signal amplification. This is not demonstrated, but it is assumed that the energy stored in the supersaturated state is released upon polymerization.

(3) This work also includes evidence showing that nonsupersaturable and supersaturable constructs of caspase-9 form puncta that dissolve or persist, respectively, upon apoptosome stimulation. The supersaturable construct also induces massive cell death, in contrast to the nonsupersaturable form. Although not demonstrated, these results could be related to the level of signal amplification.

(4) The cell's lifespan depends on the supersaturation levels of certain DFDs.

(5) Polymerization nucleated by interaction between DFDs from different pathways (different signalosomes) is rare.

(6) The study demonstrates the presence of nucleation barriers, inferred from supersaturable conditions, in the adaptor orthologs of zebrafish (Danio rerio) and the model sponge Amphimedon queenslandica, which indicates that this characteristic is conserved.

Reviewer #1 (Public review):

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

Comments on revised version:

The authors satisfactorily addressed my comments, even though the precise mechanism by which Mettl5 regulates translation of clock genes remains to be firmly demonstrated.

Reviewer #3 (Public review):

Xiaoyu Wu and colleagues examined a potential role in sleep of a Drosophila ribosomal RNA methyltransferase, mettl5. Based on sleep defects reported in CRISPR generated mutants, the authors performed both RNA-seq and Ribo-seq analyses of head tissue from mutants and compared to control animals collected at the same time point. A major conclusion was that the mutant showed altered expression of circadian clock genes, and that the altered expression of the period gene in particular accounted for the sleep defect reported in the mettl5 mutant. In this revision, the authors have added a more thorough analysis of clock gene expression and show that PER protein levels are increased relative to wild type animals a specific times of day, indicating increased stability of the protein. Given that PER inhibits its own transcription, the per RNA is low in the mutants. Efforts toward a more detailed understanding of how clock gene expression was altered in the mutants, as well as other clarification of sleep phenotypes throughout is appreciated. As noted above, a strength of this work is its relevance to a human developmental disorder as well as the transcriptomic and ribosomal profiling of the mutant. However, there still remain some minor weaknesses in the manuscript. This reviewer is not in agreement with the interpretation of the epigenetic experiments. Specifically, co-expression of Clk[jrk] or per[01] with the mettl5 mutant recovered the nighttime sleep phenotype, but was additive to the daytime sleep phenotype such that double mutants showed higher sleep. This effect should be acknowledged and discussed. Overall, this is an interesting paper that indicates a molecular link between mettl5 and the circadian clock in regulation of sleep.

Reviewer #1 (Public review):

Summary:

The authors report intracranial EEG findings from 12 epilepsy patients performing an associative recognition memory task under the influence of scopolamine. They show that scopolamine administered before encoding disrupts hippocampal theta phenomena and reduces memory performance, and that scopolamine administered after encoding but before retrieval impairs hippocampal theta phenomena (theta power, theta phase reset) and neural reinstatement but does not impair memory performance. This is an important study with exciting, novel results and translational implications. The manuscript is well written, the analyses are thorough and comprehensive, and the results seem robust.

Strengths:

- Very rare experimental design (intracranial neural recordings in humans coupled with pharmacological intervention);

- Extensive analysis of different theta phenomena;

- Well-established task with different conditions for familarity versus recollection;

- Clear presentation of findings;

- Translational implications for diseases with cholinergic dysfuction (e.g., AD);

- Findings challenge existing memory models and the discussion presents interesting novel ideas.

Reviewer #2 (Public review):

Summary:

In this study, performed in human patients, the authors aimed at dissecting out the role of cholinergic modulation in different types of memory (recollection-based vs familiarity and novelty-based) and during different memory phases (encoding and retrieval). Moreover, their goal was to obtain the electrophysiological signature of cholinergic modulation on network activity of the hippocampus and the entorhinal cortex.

Strengths:

Authors combined cognitive tasks and intracranial EEG recordings in neurosurgical epilepsy patients. The study confirms previous evidence regarding the deleterious effects of scopolamine, a muscarinic acetylcholine receptor antagonist, on memory performance when administered prior the encoding phase of the task. During both encoding and retrieval phases scopolamine disrupts the power of theta oscillations in terms of amplitude and phase synchronization. These results raise the question on the role of theta oscillations during retrieval and the meaning of scopolamine effect on retrieval-associated theta rhythm without cognitive changes. The authors clearly discussed this issue in the discussion session.

A major point is the finding that scopolamine-mediated effect is selective for recollection-based memory and not for familiarity- and novelty-based memory.

The methodology used is powerful and the data underwent a detailed and rigorous analysis.

Reviewer #1 (Public review):

Summary:

An interesting manuscript from the Carrington lab is presented investigating the behavior of single vs double GPI-anchored nutrient receptors in bloodstream form (BSF) T. brucei. These include the transferrin receptor (TfR), the HpHb receptor (HpHbR), and the factor H receptor (FHR). The central question is why these critical proteins are not targeted by host acquired immunity. It has generally been thought that they are sequestered in the flagellar pocket (FP), where they are subject to rapid endocytosis - any Ab:receptor complexes would be rapidly removed from the cell surface. This manuscript challenges that assumption by showing that these receptors can be found all over the outer cell body and flagella surfaces - if one looks in an appropriate manner (rapid direct fixation in culture media).

Strengths and weaknesses:

(1) The presence of a second ESAG6 gene in the BES7 expression site was noted in the previous review. This is now noted and discussed appropriately in the current version.

(2) Surface binding studies: The ability of cells to bind tagged-Tf while in complete media was challenged and it was suggested that classic competition studies be performed to validate saturable ligand binding. This has been done now and the results confirm that this is so. A reasonable discussion of the results is presented.

(3) Variable TfR expression in different BESs: The claim that specific ES environment is the dominant factor controlling TfR expression levels was challenged in that the presented results could be due to technical issues. RNA seq has now been performed confirming that the differences in TfR abundance is indeed directly related to mRNA levels

(4) Surface immuno-localization of receptors: In regard to the novel immunofluorescence (direct fixation) methodology used to demonstrate TfR on the cell surface the authors were asked of they had attempted more traditional methods that involve centrifugation/washing. These data are now provided (Fig S5) and do indicate that centrifugation does reduce signal, likely due to shedding and/or internalization during the procedure. Nevertheless, significant signal is present after centrifugation leaving the issue of why others have never detected significant surface TfR.

These responses address all the major concerns with the original submission and a greatly improved manuscript is now submitted.

Reviewer #2 (Public review):

The revised data support the conclusion that methodological differences can influence apparent receptor localization. However, key claims regarding functional surface engagement of TfR and hydrodynamic clearance remain based largely on indirect evidence and model-based interpretation. These conclusions should therefore be phrased more cautiously.

I thank the authors for their careful rebuttal and the additional experiments included in the revised manuscript. The new fixation comparisons and transferrin competition assays substantially strengthen the technical basis of the study and address several of the original concerns.

However, some conclusions remain more inferential than directly supported by the data. While the fixation and washing controls demonstrate that methodology influences apparent TfR localisation, they do not directly establish that previous protocols quantitatively redistribute surface TfR into the flagellar pocket. Statements implying such redistribution should therefore be phrased more cautiously.

Similarly, the added transferrin binding controls argue against non-specific interactions, but functional engagement of surface-exposed TfR in intact bloodstream-form parasites remains supported mainly by indirect evidence. The proposed explanation involving rapid on/off rates and newly arriving receptors is plausible but should be more clearly identified as an inference.

Reviewer #1 (Public review):

Summary:

This study examined the functional organization of the mouse posterior parietal cortex (PPC) using meso-scale two-photon calcium imaging during visually-guided and history-guided tasks. The researchers found distinct functional modules within the medial PPC: area A, which integrates somatosensory and choice information, and area AM, which integrates visual and choice information. Area A also showed a robust representation of choice history and posture. The study further revealed distinct patterns of inter-area correlations for A and AM, suggesting different roles in cortical communication. These findings shed light on the functional architecture of the mouse PPC and its involvement in various sensorimotor and cognitive functions.

Strengths:

Overall, I find this manuscript excellent. It is very clearly written and built up logically. The subject is important, and the data supports the conclusions without overstating implications. Where the manuscript shines the most is the exceptionally thorough analysis of the data. The authors set a high bar for identifying the boundaries of the PPC subareas, where they combine both somatosensory and visual intrinsic imaging. There are many things to compliment the authors on, but one thing that should be applauded in particular is the analysis of the body movements of the mice in the tube. Anyone working with head-fixed mice knows that mice don't sit still but that almost invariable remains unanalyzed. Here the authors show that this indeed explained some of the variance in the data.

Comments on revisions:

I only had minor comments on the first version of the manuscript and these concerns were fully addressed after revision.

Reviewer #2 (Public review):

Summary:

The posterior parietal cortex (PPC) has been identified as an integrator of multiple sensory streams and guides decision making. Hira et al observe that dissection of the functional specialization of PPC subregions requires simultaneous measurement of neuronal activity throughout these areas. To this end, they use widefield calcium imaging to capture the activity of thousands of neurons across the PPC and surrounding areas. They begin by delineating the boundaries between the primary sensory and higher visual areas using intrinsic imaging and validate their mapping using calcium imaging. They then conduct imaging during a visually guided task to identify neurons that respond selectively to visual stimuli or choice. They find that vision and choice neurons intermingle primarily in the anterior medial (AM) area, and that AM uniquely encodes information regarding both the visual stimulus and the previous choice, positioning AM as the main site of integration of behavioral and visual information for this task.

Strengths:

There is an enormous amount of data and results reveal very interesting relationships between stimulus and choice coding across areas and how network dynamics relate to task coding.

Weaknesses:

The enormity of the data and the complexity of the analysis makes the manuscript hard to follow. Sometimes it reads like a laundry list of results as opposed a cohesive story.

Comments on revisions:

The authors have addressed our concerns.

Reviewer #3 (Public review):

Summary:

This work from Hira et al leverages mesoscopic 2-photon imaging to study large neural populations in different higher visual areas, in particular areas A and AM of the parietal cortex. The focus of the study is to obtain a better understanding of the representation of different task-related parameters, such as choice formation and short-term history, as well as visual responses in large neural populations across different cortical regions to obtain a better understanding of the functional specialization of neural populations in each region as well as the interaction of neural populations across regions. The authors image a large number of neurons in animals that either perform a visual discrimination or a history-dependent task to test how task demands affect neural responses and population dynamics. Furthermore, by including a behavioral perturbation of animal posture they aim to dissociate the neural representation of history signals from body posture. Lastly, they relate their functional findings to anatomical data from the Allen connectivity atlas and show a strong relation of functional correlations on anatomical connectivity patterns.

Strengths:

Overall, the study is very well done and tackles a problem that should be of high interest to the field by aiming to obtain a better understanding of the function and spatial structure of different regions in the parietal cortex. The experimental approach and analyses are sound and of high quality and the main conclusions are well supported by the results. Aside from the detailed analyses, a particular strength is the additional experimental perturbation of posture to isolate history-related activity which supports the conclusion that both posture and history signals are represented in different neurons within the same region.

Weaknesses:

The work does not focus on functional overlap at the single-cell level but on the spatial distribution of functional classes across areas. A minor weakness is therefore that it does not explicitly address how the finding of functional clusters relate to established notions of mixed selectivity within PPC.

Reviewer #2 (Public review):

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

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

In the revised version, the authors perform experiments with ASM KO cells to provide genetic evidence of the role for ASM in S. aureus entry through lysosomal modulation. The key additional experiment is the phenotype of reduced bacterial uptake in low serum, but not in high serum conditions. The authors suggest this could be due to the SM from serum itself affecting the entry. While this explanation is plausible, prolonged exposure of cells to low serum is well documented to alter several cellular functions, particularly in the context of this manuscript, lysosomal positioning, exocytosis and Ca2+ signaling. A better control here could be WT cells grown in low serum. If SM in serum can interfere, why do they see such pronounced phenotype on bacterial entry in WT cells upon chemical inhibition?

While the authors argue a role for undetectable nano-scale Cer platforms on the cell surface caused by ASM activity, results do not rule out a SM independent role in the cellular uptake phenotype of ASM inhibitors.

The authors have attempted to address many of the points raised in the previous revision. While the new data presented provide partial evidence, the reliance on chemical inhibitors and lack of clear results directly documenting release of lysosomal Ca2+, or single bacterial tracking, or clear distinction between ASM dependent and independent processes dampen the enthusiasm.

I acknowledge the author's argument of different ASM inhibitors showing similar phenotypes across different assays as pointing to a role for ASM, but the lack of phenotype in ASM KO cells is concerning. The author's argument that altered lipid composition in ASM KO cells could be overcoming the ASM-mediated infection effects by other ASM-independent mechanisms is speculative, as they acknowledge, and moderates the importance of ASM-dependent pathway. The SM accumulation in ASM KO cells does not distinguish between localized alterations within the cells. If this pathway can be compensated, how central is it likely to be ?

The authors allude to lower phagosomal escape rate in ASM KO cells compared to inhibitor treatment, which appears to contradict the notion of uptake and intracellular trafficking phenotype being tightly linked. As they point out, these results might be hard to interpret. Could an inducible KD system recapitulate (some of) the phenotype of inhibitor treatment? If S. aureus does not escape phagosome in macrophages, could it provide a system to potentially decouple the uptake and intracellular trafficking effects by ASM (or its inhibitor treatment) ?

The role of ASM on cell surface remains unclear. The hypothesis proposed by the authors that the localized generation of Cer on the surface by released ASM leads to generation of Cer-enriched platforms could be plausible, but is not backed by data, technical challenges to visualize these platforms notwithstanding. These results do not rule out possible SM independent effects of ASM on the cell surface, if indeed the role of ASM is confirmed by controlled genetic depletion studies.

The reviewer acknowledges technical challenges in directly visualizing lysosomal Ca2+ using the methods outlined. Genetically encoded lysosomal Ca2+ sensor such as Gcamp3-ML1 might provide better ways to directly visualize this during inhibitor treatment, or S. aureus infection.

Reviewer #1 (Public review):

Summary:

The authors report the structure of the human CTF18-RFC complex bound to PCNA. Similar structures (and more) have been reported by the O'Donnell and Li labs. This study should add to our understanding of CTF18-RFC in DNA replication and clamp loaders in general. However, there are numerous major issues that I recommend the authors fix.

Strengths:

The structures reported are strong and useful for comparison with other clamp loader structures that have been reported lately.

Reviewer #2 (Public review):

Summary

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

Strength & Weakness

Their overall analysis is of high quality, and they identified, among other things, a human-specific beta-hairpin in Ctf18 that flexible tethers Ctf18 to Rfc2-5. Indeed, deletion of the beta-hairpin resulted in reduced complex stability and a reduction in the rate of primer extension assay with Pol ε. Moreover, the authors identify that the Ctf18 ATP-binding domain assumes a more flexible organisation.

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

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

Reviewer #3 (Public review):

Summary:

CTF18-RFC is an alternative eukaryotic PCNA sliding clamp loader which is thought to specialize in loading PCNA on the leading strand. Eukaryotic clamp loaders (RFC complexes) have an interchangeable large subunit which is responsible for their specialized functions. The authors show that the CTF18 large subunit has several features responsible for its weaker PCNA loading activity, and that the resulting weakened stability of the complex is compensated by a novel beta hairpin backside hook. The authors show this hook is required for the optimal stability and activity of the complex.

Relevance:

The structural findings are important for understanding RFC enzymology and novel ways that the widespread class of AAA ATPases can be adapted to specialized functions. A better understanding of CTF18-RFC function will also provide clarity into aspects of DNA replication, cohesion establishment and the DNA damage response.

Strengths:

The cryo-EM structures are of high quality enabling accurate modelling of the complex and providing a strong basis for analyzing differences and similarities with other RFC complexes. They use complementary pre-steady state FRET and polymerase primer extension assays to investigate the role of a unique structural element in CTF18.

Weaknesses:

The manuscript would have benefited from a more detailed biochemical analysis using mutagenesis and assays to tease apart the functional relevance of the many differences with the canonical RFC complex.

Overall appraisal:

Overall, the work presented here is solid and important. The data is sufficient to support the stated conclusions.

Reviewer #1 (Public review):

General assessment of the work

In this manuscript, Mohr and Kelly show that the C1 component of the human VEP is correlated with binary choices in a contrast discrimination task, even when the stimulus is kept constant and confounding variables are considered in the analysis. They interpret this as evidence for the role V1 plays during perceptual decision formation. Choice-related signals in single sensory cells are enlightening because they speak to the spatial (and temporal) scale of the brain computations underlying perceptual decision making. However, similar signals in aggregate measures of neural activity offer a less direct window and thus less insight into these computations. The authors do a good job justifying their focus on the C1 component and illustrating how it may behave under different simulated scenarios. The results are interesting, although it is difficult to specify which reasonable hypothesis is exactly ruled out by these results. One interpretation is that V1 activity directly guides perceptual decisions in this task. Alternatively, higher-level areas may do this, provided that their activity largely reflects their V1-inputs. This certainly seems possible in a simple task like this.

Summary of substantive concerns

I have no substantive concerns about the revised version of the paper.

Reviewer #2 (Public review):

Summary:

Mohr and Kelly report a high-density EEG study in healthy human volunteers in which they test whether correlations between neural activity in primary visual cortex and choice behavior can be measured non-invasively. Participants performed a contrast discrimination task on large arrays of Gabor gratings presented in the upper left and lower right quadrants of the visual field. The results indicate that single-trial amplitudes of C1, the earliest cortical component of the visual evoked potential in humans, predict forced-choice behavior over and beyond other behavioral and electrophysiological choice-related signals. These results constitute an important advance for our understanding of the nature and flexibility of early visual processing.

Strengths:

The findings suggest a previously unsuspected role for aggregate early visual cortex activity in shaping behavioral choices.

The authors extend well-established methods for assessing covariation between neural signals and behavioral output to non-invasive EEG recordings.

The effects of initial afferent information in primary visual cortex on choice behavior is carefully assessed by accounting for a wide range of potential behavioral and electrophysiological confounds.

Caveats and limitations are transparently addressed and discussed.

Weaknesses:

Due to the inherent limitations of scalp-recorded visual evoked potentials, the results cannot be directly compared to invasive recordings in animal models.

Reviewer #1 (Public review):

Summary:

The existence of VERT regions is well supported, but the number of regions called as ISCs may be inflated by permissive thresholds (e.g., AEI {greater than or equal to} 0.8 or {less than or equal to} 0.2 in a single clone). This risks conflating transient stochastic differences with stable ISCs. Similarly, the claim of cell-type specificity is not convincingly demonstrated given the small sample size (n=4) and strong batch confounding between lymphoblastoid and cartilage progenitors. While syntenic VERT regions across mouse and human are intriguing, they complicate interpretation of strong clustering by cell type. Sampling depth may also have exaggerated allelic imbalance calls.

The proposed role of ISCs in haploinsufficiency is conceptually interesting but remains speculative; developmental stochasticity and founder population size may play larger roles than replication timing. The claim that autosomal inactivation is mechanistically distinct from XCI, however, is reasonable and supported.

Some conclusions should be more explicitly qualified as preliminary. Cell-type specificity and mitotic stability both require stronger evidence; the latter is inferred indirectly from clonal expansion rather than shown directly, and orthogonal experiments (e.g., allele-specific ChIP-seq, DNA methylation) would be required. Estimated genomic coverage of ISCs should also be re-evaluated, as single-clone observations may inflate counts.

Replication is limited. Hierarchical clustering is confounded by batch and based on presence/absence calls that lack quantitative resolution. More robust approaches would include using magnitude of imbalance, annotating VERTs by genomic location, applying stricter thresholds for replication timing, and benchmarking AEI distributions against the X chromosome. These are realistic re-analyses requiring no new data and could be completed in ~1 month.

Methods are generally well described and reproducible. Figures and text would benefit from improved clarity: axis labels are missing in places (e.g., Fig. 1c, Fig. 2g), legends should explain chromosome arm colors, and cluttered figures such as Fig. 1j could be re-visualized for interpretability. Gene set enrichment analysis should be restricted to avoid inflated significance from overly broad categories. A useful citation for XCI timing (pmid=39420003) could be added to strengthen background.

Significance:

Conceptually, this work introduces ISC-like phenomena in human and mouse progenitor lines, coupling allelic expression imbalance with replication timing. Technically, it combines allele-specific RNA-seq with Repli-seq in genotyped, clonal, single-cell-derived lines. Clinically, it suggests an alternative model for haploinsufficiency, relevant to dosage-sensitive diseases where stochastic transcriptional delays could shape penetrance.

The study builds on prior work in allelic exclusion (e.g., HLA, olfactory receptors) and random monoallelic expression, generalizing these phenomena into ISC/vert frameworks and proposing mitotic stability of allele choice. By extending beyond expression to replication timing, the authors suggest a broader paradigm for epigenetic regulation at autosomal loci.

The paper will be of interest to epigeneticists studying XCI, allelic exclusion, and monoallelic expression; to developmental biologists examining replication timing and differentiation; and to clinicians concerned with dosage-sensitive and haploinsufficient disorders.

Reviewer #2 (Public review):

Summary:

- This is a complicated research topic that touches on a few sub-fields of biology, and thus to make the paper more approachable I would recommend a careful edit of the text for clarity and precision of language.<br /> - Authors point out that this is a decades-old field; it would make sense to use terminology established within the field rather than inventing their own. Allelic imbalance has been referred to as AI, MAE (monoallelic expression), RMAE (random monoallelic expression) etc. The paper whose mouse data the authors make use of uses Asynchronous Stochastic Replication Timing (ASRT) instead of VERT to refer to the same phenomenon. Creating unnecessary jargon makes the paper more difficult to read and adds needless complexity to an already complex field.<br /> - Methods do not provide sufficient detail to fully evaluate or reproduce these experiments.<br /> - It is helpful to show representative loci as the authors do in Fig 1F and G and Fig 2, but these panels are very densely rendered and thus difficult to process visually - even the cartoon version (1D) is thick with overlapping lines. The point that allelic imbalance is enriched in VERTs would be enhanced if the authors could present the allelic ratio for all genes found in all VERTs, demonstrating how replication timing on either chromosome affects the allelic ratio.<br /> - The authors make the important point that VERTs are unlikely to be shared among different cell types and tissues (Fig 1i) but then find an enrichment for neuronal and immune genes in VERT regions identified in ACPs. It follows that these same genes are unlikely to be in such regions in the tissues where they are relevant. Some of the GO terms presented are too broad to suggest any biological significance to the result, even if there is statistical significance (for example, the top term for LCL clones 'Cytoplasm' is associated with 12,000 genes, and the second term for mouse clones 'Membrane' is associated with 10,000). It would be helpful to focus on GO terms lower in the GO hierarchy.<br /> - Figure 3 highlights the association of related gene clusters with VERTs but the VERTs are assigned based on variable replication timing in just 1 or 2 clones. This is an interesting observation, but to make the point that "VERT regions frequently coincide with gene clusters in the human genome" there needs to be a systematic assessment of replication timing at all gene clusters across all clones, and a statistical test for significance.<br /> - It is an interesting hypothesis that VERTs are conserved between species at synentic loci. If such regions are really conserved, one would expect that replication timing at these sites would be consistently asynchronous. However, the data presented shows that in human clones these VERTs can be specific to an individual donor (as in 5A) or an individual clone (as in 5H).<br /> - Again, the finding that VERTs coincide with neurodevelopmental disease genes in immune and cartilage cells is at odds with the previous statements and data about the tissue specificity of VERTs. In order to support the claim that neurodevelopmental disease associated genes reside in asynchronously replicating regions, and are thus more prone to allelic imbalance, the authors would need to demonstrate this phenomenon in neuronal cells.

Significance:

The authors pair analysis of replication timing and allele-specific expression in clonal populations of primary human cells. They combine these data with previously published data on clones from transformed human cell lines. They identify a number of genomic regions that display asynchronous replication timing in at least one clone and correlate these regions with allele-specific expression of genes within them. They also observe that several interesting gene sets, including genes that are associated with human diseases, map to asynchronously replicating regions. This is a good experimental approach that builds on already published data demonstrating the connection between allelic imbalance and replication timing. However, the authors consistently lean on thin evidence (i.e. a single clone) within a modestly sized dataset (4 clones from 2 donors each) to propose a new model for haploinsufficiency in human disease. The consistent focus on limited elements in the data and perhaps an overreach in the interpretation makes it difficult to appreciate what is in fact a very good experiment.

Reviewer #1 (Public review):

Summary:

This manuscript by Kolb and Hasseman et al. introduces a significantly improved GABA sensor, building on the pioneering work of the Janelia team. Given GABA's role as the main inhibitory neurotransmitter and the historical lack of effective optical tools for real-time in vivo GABA dynamics, this development is particularly impactful. The new sensor boasts an enhanced signal-to-noise ratio (SNR) and appropriate kinetics for detecting GABA dynamics in both in vitro and in vivo settings. The study is well-presented, with convincing and high-quality data, making this tool a valuable asset for future research into GABAergic signaling.

Strengths:

The core strength of this work lies in its significant advancement of GABA sensing technology. The authors have successfully developed a sensor with higher SNR and suitable kinetics, enabling the detection of GABA dynamics both in vitro and in vivo. This addresses a critical gap in neuroscience research, offering a much-needed optical tool for understanding the most important inhibitory neurotransmitter. The clear representation of the work and the convincing, high-quality data further bolster the manuscript's strengths, indicating the sensor's reliability and potential utility. We anticipate this tool will be invaluable for further investigation of GABAergic signaling.

Weaknesses:

Despite the notable progress, a key limitation is that the current generation of GABA sensors, including the one presented here, still exhibits inferior performance compared to state-of-the-art glutamate sensors. While this work is a substantial leap forward, it highlights that further improvements in GABA sensor would still be highly beneficial for the field to match the capabilities seen with glutamate sensors.

Reviewer #1 (Public review):

Summary:

BK channels are widely distributed and involved in many physiological functions. They have also proven a highly useful tool for studying general allosteric mechanisms for gating and modulation by auxiliary subunits. Tetrameric BK channels are assembled from four separate alpha subunits which would be identical for homozygous alleles and of potentially five different combinations for heterozygous alleles Geng et al . (2023), (https://doi.org/10.1085/jgp.202213302). Construction of BK channels with concatenated subunits in order to strictly control heteromeric subunit composition had not yet been used because the N-terminus in BK channels is extracellular whereas the C-terminus is intracellular. In this new work, Chen, Li, and Yan devise clever methods to construct and assemble BK channels of known subunit composition, as well as to fix the number of γ1 axillary subunits per channel. With their novel molecular approaches, Chen, Li and Yan report that a single γ1 axillary subunit is sufficient to fully modulate a BK channel, that the deep conducting pore mutation L312A exhibited a graded effect on gating with each addition mutated subunit replacing a WT subunit in the channel adding an additional incremental left shift in activation, and that the V288A mutation at the selectivity filter must be present on all four alpha subunits in order to induce channel inactivation. Chen, Li, and Yan have been successful in introducing new molecular tools to generate BK channels of known stoichiometry and subunit composition. They validate their methods and provide three different examples of stoichiometric modulation by LRRC26, the selectivity filter, and the pore.

Strengths:

Powerful new molecular tools for study of channel gating are developed and validated in the study.

Weaknesses:

One example each of auxiliary, deep pore, and selectivity filter allosteric actions are presented, but this is sufficient for the purposes of the paper to establish their methods and present specific examples of applicability.

Reviewer #2 (Public review):

Summary:

This manuscript describes novel BK channel concatemers as a tool to study the stoichiometry of gamma subunit and mutations in modulation of the channel. Taking the advantage of modular design of BK channel alpha subunit the authors connected S1-S6/1st RCK as two- and four-subunit concatemers and coexpressed with S0-RCK2 to form normal function channels. These concatemers avoided the difficulty that the extracellular N-terminus of S0 was unable to connect with the cytosolic C-terminus of the alpha or gamma subunit, allowing a single gamma subunit to be connected to the concatemers. The concatemers also helped reveal the required stoichiometry of mutant BK subunits in modulating channel function. These include L312A in the deep pore region that altered channel function additively with each additional subunit harboring the mutation, and V288A at the selectivity filter that altered channel function cooperatively only when all four subunits being mutated. These results demonstrate that the concatemers are robust and effective in studying BK channel function and molecular mechanisms related to stoichiometry. The different requirement of the gamma subunit and the mutations stoichiometry for altering channel function is interesting, revealing fundamental mechanisms of how different motifs of the channel protein control function.

Strengths:

The manuscript presents well designed experiments with high quality data, which convincingly demonstrate the BK channel concatemers and their utility. The results are clearly written.

Weaknesses:

This reviewer did not identify any major concerns with the manuscript.

Editors' note: We thank you for addressing some of the concerns, adding clarifications and more complete discussions, including further details about experimental protocols. The revised version is significantly improved. Some concerns linger that the biophysical/structural mechanisms underlying the observed phenotypes remain unclear and in some ways are phenomenological. However, the current study is more about the methodology and the mechanisms underlying the stoichiometry dependent effects are perhaps left for a separate study, with more detailed exploration. Congratulations for the excellent work.

Reviewer #1 (Public review):

Summary

The manuscript by Ma et al. provides robust and novel evidence that the noctuid moth Spodoptera frugiperda (Fall Armyworm) possesses a complex compass mechanism for seasonal migration that integrates visual horizon cues with Earth's magnetic field (likely its horizontal component). This is an important and timely study: apart from the Bogong moth, no other nocturnal Lepidoptera has yet been shown to rely on such a dual-compass system. The research therefore expands our understanding of magnetic orientation in insects with both theoretical (evolution and sensory biology) and applied (agricultural pest management, a new model of magnetoreception) significance.

The study uses state-of-the-art methods and presents convincing behavioural evidence for a multimodal compass. It also establishes the Fall Armyworm as a tractable new insect model for exploring the sensory mechanisms of magnetoreception, given the experimental challenges of working with migratory birds. Overall, the experiments are well designed, the analyses are appropriate, and the conclusions are generally well supported by the data.

Strengths

• Novelty and significance: First strong demonstration of a magnetic-visual compass in a globally relevant migratory moth species, extending previous findings from the Bogong moth and opening new research avenues in comparative magnetoreception.

• Methodological robustness: Use of validated and sophisticated behavioural paradigms and magnetic manipulations consistent with best practices in the field. The use of 5 min bins to study a dynamic nature of magnetic compass which is anchored to a visual cue but updated with latency of several minutes is an important finding and a new methodological aspect in insect orientation studies.

• Clarity of experimental logic: The cue-conflict and visual cue manipulations are conceptually sound and capable of addressing clear mechanistic questions.

• Ecological and applied relevance: Results have implications for understanding migration in an invasive agricultural pest with expanding global range.

• Potential model system: Provides a new, experimentally accessible species for dissecting the sensory and neural bases of magnetic orientation.

Weaknesses

Overall, this is a strong study, and the authors have completed an excellent major revision that has undoubtedly addressed most major and minor issues. The remaining points below are minor recommendations, and I acknowledge that differences in opinion are always possible:

(1) Structure and Presentation of Results

• I recommend reordering the visual-cue experiments to progress from simpler conditions (no cues) to more complex ones (cue-conflict). This would improve narrative logic and accessibility for non-specialist readers. The authors have chosen not to implement this suggestion, which I respect, but my recommendation stands.

(2) Ecological Interpretation

• The authors should expand their discussion on how the highly simplified, static cue setup translates to natural migratory conditions, where landmarks are dynamic, transient, or absent. Specifically, further consideration is needed on how the compass might function when landmarks shift position, become obscured, or are replaced by celestial cues. Additionally, the discussion would benefit from a more consolidated section with concrete suggestions for future experiments involving transient, multiple, or more naturalistic visual cues.

This point was addressed partially in one paragraph of the Discussion, which reads as follows:

"In nature, they are likely to encounter a range of luminance-gradient visual cues, including relatively stable celestial cues as well as transient or shifting local features encountered en route. Although such natural cues differ from our simplified laboratory stimulus, they may represent intermittently sampled visual inputs that can be optimally integrated with magnetic information, with the congruency between visual and magnetic cues likely playing a key role in maintaining a stable compass response. Whether the cues are static or changing, brief periods without them may still allow the subsequent recovery of a stable long-distance orientation strategy. Determining which types of natural visual cues support the magnetic-visual compass, and how they interact with magnetic information, including how their momentary alignment or angular relationship is integrated and how such visual cue-magnetic field interactions may require time to influence orientation, together with elucidating the genetic and ecological bases of multimodal orientation, will be important objectives for future research."

While this paragraph is informative, the wording remains lengthy, somewhat unclear, and vague. Shorter, clearer statements would improve readability and impact. For example:

• How could moths maintain direction during periods when only the magnetic field is present and visual landmarks are absent?

• Could celestial cues (e.g., stars) compensate, and what happens if these are also obscured?

• What role does saliency play when multiple visual landmarks are present simultaneously?

• How might a complex skyline without salient landmarks affect orientation?

Including simple, concise sentences that pose concrete open questions and suggest experimental designs would strengthen the discussion without creating space issues. In my view, a comprehensive discussion of how the simplified, static cue setup relates to natural migratory conditions-where landmarks are dynamic, transient, or absent-would add significant value to the paper.

(3) Methodological Details and Reproducibility

• The lack of luminance level measurements should be explicitly highlighted.

• The authors chose not to adjust figure legends by replacing "magnetic South" with "magnetic North." While I believe this would be more conventional and preferable, this is ultimately a minor stylistic issue.

(4) Conceptual Framing and Discussion

• Although the authors made a good attempt to explain the limitations of using an artificial visual cue, I believe there is room for a more explicit argument. For example, it could be stated clearly that this species is unlikely to encounter a situation in nature where a single, highly salient landmark coincides with its migratory direction. Therefore, how these findings translate to real migratory contexts remains an open question. A sentence or two making this point directly would strengthen the discussion.

(5) Technical and Open-Science Points

• Sharing the R code openly (e.g., via GitHub) should be seriously considered. The code does not need to be perfectly formatted, but making it available would be highly beneficial from an open-science perspective.

Reviewer #2 (Public review):

Summary:

The work titled "Geomagnetic and visual cues guide seasonal migratory orientation in the nocturnal fall armyworm, the world's most invasive insect" provided experimental evidence on how geomagnetic and visual cues are integrated, and visual cues are indispensable for magnetic orientation in the nocturnal fall armyworm.

Strengths:

It has been demonstrated that the Australian Bogon moth could integrate global stellar cues with the geomagnetic field for long distance navigation. However, data are lacking for other insects. This study suggested that the integration of geomagnetic and visual cues may represent a conserved navigational mechanism broadly employed across migratory insects.

Weaknesses:

The visual cues used in the indoor experimental system designed by the authors may have some limitations in ecological relevance. The author may need more explanations on this experimental system.

In the revised manuscript, the authors have added explanations in the discussion section. I am fine with the revision.

Reviewer #1 (Public review):

Summary:

Laaker et al. investigate 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.

Weaknesses:

(1) In Figure 1, the manuscript would be strengthened by quantification of CSF1R-GFP+ and CD11c-eYFP+ cells in PDPN+LYVE1- versus PDPN+LYVE1+ regions in both control and EAE mice. This would demonstrate selective accumulation or retention of myeloid cells at the cribiform plate niche.

(2) While the PostContact-seq strategy is innovative (Figure 3), additional justification is needed to demonstrate that tissue dissociation did not artificially disrupt PDPN-myeloid contacts. The relatively small proportion of live PDPN-rich doublets (~2.5% total aggregates and ~18% PDPN+ within total aggregates) raises questions about representativeness compared with in situ observations. The authors should also more explicitly elaborate on why PostContact-seq was favored over alternative approaches such as PIC-seq.

(3) The authors stated that results regarding cell-cell interactions were integrated across four intercellular communication methodologies (Figure 4B), but this integration is not clearly described in either the Results or Method sections. This needs clarification. Moreover, the interaction analysis in Figure 4B seems to rely on TALKIEN, which does not incorporate prior ligand-receptor knowledge. Given the availability of widely used tools, such as CellChat and NicheNet, the authors may consider cross-referencing their findings.

(4) Given the increase in CCR2+ cells in PDPN+ regions (Figure S4), a pseudotime trajectory analysis may be valuable to test whether CCR2+ monocytes preferentially differentiate into CHI3L3+ immunosuppressive macrophages, PD-1+ DCs, or other myeloid subsets in post-contact versus no contact.

(5) Validation of immunosuppressive signatures in macrophages (Fig. 4G-H) using the same FACS-based post-contact versus no-contact sorting strategy (as in Figure 3A) would strengthen the conclusions.

(6) The identity of CD45IV+ cells in contact with PDPN+ cells is unclear (Figure 6B-C). The authors should provide a gating strategy demonstrating that these cells are CD11b+CD11c+ DCs within the PDPN+ doublet population, and ideally show whether these dying cells are PD-1+. Furthermore, co-labeling in tissue sections for PD-1, cleaved caspase-3, and CD11c-eYP would provide important spatial validation of flow cytometry findings (Figure 6E).

(7) In Figures 1F-H, the authors should comment on the morphological differences of CD11c+ cells in the olfactory bulb versus those infiltrating the cribriform plate.

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 the 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 is 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's currently unclear how the sorted populations reflect in vivo interactions or a propensity to form aggregates during ex vivo processing. The authors address both podoplanin-expressing cells as stromal cells and as lymphatic endothelial cells, but at times it's unclear which of these two populations is being analyzed and which is the most relevant. While novel observations, most of these findings are descriptive and lack functional correlates, and in places, the potential implications could use further discussion.

Reviewer #1 (Public review):

Summary:

This is an important study that employs high-throughput single-cell imaging to directly investigate the relationship between topologically associating domain (TAD) boundaries and gene regulation. The authors rigorously test the prevailing model that TAD boundaries functionally regulate gene activity by modulating chromatin interactions. Their core finding is that, under their specific experimental conditions, the physical distance between TAD boundaries shows no consistent correlation with the transcriptional bursting activity of a gene within the TAD. However, the authors' leap from this specific observation to the broad conclusion that "TAD boundary architecture and gene activity are uncoupled" risks conceptual overgeneralization and may lead to misinterpretation, as it seemingly contradicts substantial prior evidence supporting the regulatory role of TAD structures.

Strengths:

The major strength of this work lies in its innovative high-throughput, multi-colour imaging platform, which enables the simultaneous detection of spatial distances between specific DNA elements (TAD boundaries) and transcriptional activity at the same genomic locus in single cells and single alleles. The high-throughput nature makes the results convincing. A second key strength is the incorporation of perturbations, including global transcriptional inhibition, cell-type comparison, and degradation of key architectural proteins (CTCF, cohesin). This provides a comprehensive methodological framework to examine the relationship between boundary proximity and gene activity from multiple angles under defined conditions.

Weaknesses:

(1) Conceptual framing and interpretation:

The central conclusion may require more precise framing to avoid potential overreach. The authors' interpretation equating "physical distance between TAD boundaries" with overall "TAD boundary architecture," and "transcriptional bursting events" with broader "gene activity," could benefit from clarification. This framing may not fully capture the temporal dynamics of transcription or the regulatory complexity within TADs. Furthermore, the broad conclusion of an uncoupled relationship appears to challenge extensive prior evidence from perturbation studies showing that disrupting TAD boundaries can alter gene expression. The authors' own observation of reduced gene activity upon RAD21 degradation suggests that global TAD disruption can affect transcription. A more precise and limited conclusion, acknowledging that their data demonstrate a lack of detectable correlation between boundary distance and bursting activity in their system, would be more accurate and help reconcile these findings with the existing literature.

(2) Technical methods and data presentation:

(2.1) Accuracy and dimensionality of distance measurements: The manuscript does not clearly state whether distances are measured in 2D or 3D, nor does it sufficiently address precision limits. The stated Z-step size (1 µm) may be inadequate for accurately measuring sub-micron chromatin distances in 3D.

(2.2) Probe design and systematic error: The genomic coverage size of the BAC probes used for DNA FISH is not explicitly stated. Large probe coverage could inherently blur the precise spatial location of adjacent DNA loci. The reported average distance (~300 nm) may be influenced by the physical size of the probes, as well as systematic expansion or distortion introduced by sample fixation and FISH processing. Although such technical limitations are currently unavoidable, the authors should clarify how these factors might affect their ability to detect subtle distance changes.

(2.3) Data Visualization: The manuscript would benefit from including representative, zoomed-in regions of interest from the raw imaging data. This would allow readers to visually assess measured distance differences against background noise.

(2.4) Potential impact of resolution limits: In Figure 5, the micro-C data reveal a clear difference in interaction patterns inside versus outside the VARS2 locus TAD, yet the imaging data show no corresponding distance difference. This strongly suggests that the current imaging system, limited by optical resolution, probe size, and localisation accuracy, may be unable to resolve finer-scale spatial reorganizations associated with specific chromatin conformations (e.g., enhancer-promoter loops). The authors should explicitly discuss that their conclusion of "no coupling observed" may be constrained by the resolution and sensitivity of their method and does not preclude the possibility of detecting such associations with higher-precision measurements or in live-cell dynamics.

In summary, this study provides a valuable single-cell perspective. However, the authors should more cautiously define the scope of their findings in the manuscript and provide a more balanced discussion situating their work within the broader field.

Reviewer #2 (Public review):

Summary:

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

Strengths:

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

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

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

Weaknesses:

In untreated cells, the distribution of distance measurements between boundary probes is exceptionally narrow. While depletion of RAD21 clearly demonstrates an ability to detect changes in this distribution, this tight baseline distribution may limit sensitivity to more subtle changes (like those one might expect from transcriptional influences). In addition, the correlation analysis is asymmetric, primarily stratifying by transcriptional status and then comparing boundary distances. Given the central claim that boundary architecture does not influence gene activity, the analysis should be done from the opposite perspective (stratifying by boundary distance).

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

On a related note, this approach primarily tests the role of boundary interactions rather than domain organization as a whole, and it should be acknowledged that internal domain structures are not directly assessed.

The comparison to work in other organisms (particularly the comparisons made to Drosophila) should be handled with care. The mechanisms underlying domain formation differ substantially across these systems, particularly regarding the differences in CTCF's role.

Reviewer #1 (Public review):

Summary:

The ubiquitin kinase PINK1 accumulates on damaged mitochondria to signal the initiation of mitophagy. While we know what PINK1 looks like when it is stabilised on damaged mitochondria, not much is known about how it gets there. In this study, Okatsu et al. solve a cryoEM structure of partially folded PINK1 in complex with its chaperones HSP90 and CDC37 to a resolution of 3.08 Å. This structure captures PINK1 in a state whereby the C-lobe of its kinase domain is folded, while the N-lobe remains unfolded and stabilised by an HSP90 dimer. According to the authors' model, their structure represents cytosolic PINK1 on its way to the mitochondria. This structure also demonstrates how PINK1 is folded in a step-wise mechanism and proposes a role for residues that are mutated in Parkinson's disease.

Strengths:

PINK1 is known to be a client of the HSP90 chaperone system. Here, Okatsu et al. present a solid structural dataset showing how PINK1 interacts with HSP90 and CDC37, and they describe key residues and motifs predicted to facilitate the interactions between PINK1 and the chaperones. Notably, two key residues within interacting regions on PINK1 are also mutated in Parkinson's disease. The structure by Okatsu et al. is in line with another recently published structure of the same complex (Tian et al. Nat Comms, 2025), which appears very similar, further supporting the findings. Together, these two studies represent the first observations of cytosolic PINK1 in a semi-folded state, which provides a novel insight into PINK1 at an earlier stage within the signalling cascade.

Weaknesses:

This paper is not the first to describe the structure of the PINK1-HPS90-CDC37 complex. A study by Tian et al. was published in early December 2025 in Nature Communications, reporting a 2.84 Å structure of PINK1-HSP90-CDC37, as well as a structure of PINK1 with HSP90 and another HSP90 co-chaperone, FKBP51. It would be important to acknowledge this comparable study and to discuss how the structure in this study compares with the Tian et al. structures and whether it reveals any additional information.

Although they make claims about the functional relevance of PINK1-interacting residues, the study by Okatsu et al. does not include any biochemical or functional validation of the structure. To support their claims, the authors should test the PINK1-HSP90-CDC37 interaction using their recombinant proteins for mutants of the conserved hydrophobic PINK1 residues in the PINK1 c-lobe, H352, L353, H360, I382, D384, as well as the PINK1 HPNI motif, especially the PD mutation H271Q. The PINK1 PD mutation L347P, which interacts with the CDC37 HPNI moti,f is also worth testing.

A major question that arises from this work is whether the PINK1-HSP90-CDC37 complex is newly translated PINK1 on its way to mitochondria (as suggested by the authors) or PINK1 that has already entered mitochondria, been cleaved and then retrotranslocated. This latter scenario is the favoured model proposed by Tian et al. (Nat Comms) based on their biochemical experiments. The discrepancies between the two models should at least be discussed, and the authors should also attempt to demonstrate experimentally whether their model is correct. This question is important to address because it would allow this structural information to be placed in the greater context of PINK1 signalling.

It is also unclear what the consequences are of disrupted PINK1-HSP90-CDC37 interactions on the PINK1 signalling process more broadly - does PINK1 accumulate in the cytosol? Is there less of it? Can it still be degraded via the N-end rule? What happens during mitophagy? Perhaps some of these questions can be answered with cell-based studies using a selection of the PINK1 mutants mentioned above that disrupt the PINK1-HSP90-CDC37 complex formation.

Reviewer #2 (Public review):

Summary:

Okatsu et al report the cryoEM structure of the PINK1-HSP90-CDC37 complex at 3.08A. To do so, they mutated the PARL cleavage site (F104M) and removed the N-terminal 103 a.a. The construct was co-expressed with HSP90beta and CDC37 in insect cells, as performed previously for other kinase-HSP90-CDC37 complexes (e.g. Raf1). Molybdate was added to prevent cycling between open and closed HSP90 conformations. The initial characterization by single particle cryoEM reveals two HSP90 conformations: closed with CDC37 dissociated, and open with the CTD of HSP90 separated. Thus, the authors crosslinked the complex, which yielded a more homogenous closed structure with clearly visible density for HSP90, CDC37, and PINK1. The structure shows an immature or partially folded kinase domain conformation for PINK1, with the C-lobe bound to HSP90 and the N-lobe unfolded. The C-lobe binds to HSP90 via the HPNI motif in CDC37, which mimics the HPNI motif found in the N-lobe of kinases, and which is conserved across kinases. The main novelty here is the interaction between the C-terminal extension (CTE) of PINK1, which must adopt another conformation than in the folded state, which would otherwise clash with HSP90. The interaction with the CTE is notably mediated by the flexible charged linker (FCL) of HSP90, which is partially disordered. In this conformation, HSP90 would clash with TOM20 binding.

Strengths:

Overall, this is well-executed structural biology work, which brings insight into the elements required to fold PINK1. The protein engineering used in this study is of great value and will help others in the field explore the function of PINK1 folding. Understanding the mode of activation of PINK1 is important, and this work brings forward hypotheses that are worthy of testing.

Weaknesses:

In the absence of functional assays, the study does not bring much novelty or biological insights. Furthermore, there are already several structures of HSP90-CDC37 bound to partially folded kinases, and a simple superposition of these structures on the model of HsPINK1 allows similar conclusions to be drawn, i.e. that it would bind a folded C-lobe and unfolded N-lobe. Furthermore, a very similar structure of PINK1 bound to HSP90-CDC37 (and FKBP5) was published in Nature Communications in December 2025 by another group. The main novelty from this work (and the paper published in December) is that the CTE adopts a different conformation compared to the mature form, but the implications of this are not explored. Furthermore, the authors propose that HSP90 would compete with TOM20, but what dictates the outcome of this competition? More importantly, how do these results help understand how PINK1 become active? Again, this is not explored.

Reviewer #1 (Public review):

Summary:

This manuscript by Ghosh and colleagues investigates the transcriptional changes within the oligodendrocyte lineage that contribute to age-related declines in oligodendrocyte differentiation and myelination. Combining bulk RNA-Seq on acutely purified oligodendrocyte lineage cells with bioinformatic approaches, the authors identify groups of genes that show different patterns of dynamic regulation during differentiation (which they term "switch" genes, or "switches"). A subset of these switch genes is differentially regulated with age. The authors identify two transcription factors, Bcl11a and Foxm1, that are downregulated during differentiation, have predicted binding site enrichment at other switch genes, and are downregulated in aged OPCs. Functionally testing Bcl11a, the authors show that Bcl11a knockdown inhibits the differentiation of young OPCs in culture, whereas overexpression promotes the differentiation of aged OPCs. Viral expression of Bcl11a in Sox10-expressing cells accelerates the formation of Plp1+ oligodendrocytes in aged rodents following lysolecithin induced demyelination.

Strengths:

The work is clearly presented and addresses an important biological problem. The bioinformatic approaches used in the manuscript are powerful, and the identification of Bcl11a as a modulator of oligodendrocyte differentiation is a novel finding. The combined in vitro and in vivo approaches to assess the function of Bcl11a in oligodendrocyte differentiation are a substantial strength of the work.

Weaknesses:

Although the PCA plots show distinct and reproducible global gene expression differences between the different isolated cell populations, the authors do not present a figure showing expression levels of typical stage-specific markers (e.g., Pdgfra, Pcdh15, C1ql1 for OPCs, Bcas1, Enpp6, Gpr17 for preOLs, Mobp, Mog, etc. for OLs) or confirm the absence of markers of other lineages (astrocytes, neurons, microglia, etc.). This makes it difficult to evaluate the success of their cell isolation strategy at different ages without reanalyzing the raw data. In addition, other publicly available datasets (e.g., the Barres lab bulk RNA-Seq datasets from PMID 25186741 or the Castelo-Branco lab single cell datasets from PMID 27284195) do not show downregulation of Bcl11a during OL differentiation as is described here - this apparent discrepancy is not discussed.

Reviewer #2 (Public review):

Aging poses a significant challenge to the regenerative capacity of oligodendrocyte precursor cells (OPCs) to differentiate and myelinate neuronal axons. Myelin abnormalities accumulate with age, and it is likely that the ability of OPCs to differentiate into myelinating oligodendrocytes becomes progressively impaired during aging, leading to inefficient turnover of damaged myelin and oligodendrocytes, as well as reduced adaptive myelination. Understanding the molecular mechanisms underlying the compromised capacity of aged OPCs is therefore critical for addressing age-related white matter decline.

This study aims to decipher the intrinsic molecular changes that occur in aged OPCs. By profiling differentially expressed transcription factors (TFs) between young and aged OPCs, and by employing a novel bioinformatic tool to identify key TFs that undergo dynamic changes across distinct stages of OPC differentiation, the authors identify Bcl11a as a potential regulator. Bcl11a is highly expressed in young OPCs but markedly reduced in aged cells. Functional experiments further demonstrate that while Bcl11a does not affect OPC proliferation, it significantly promotes the differentiation of aged OPCs. Importantly, this effect is also observed in vivo following demyelinating injury in aged mice.

While the study provides compelling evidence that BCL11A represents a limiting factor for OPC differentiation during ageing, the downstream targets and molecular mechanisms through which BCL11A exerts its effects are not directly addressed. As such, the work should be interpreted primarily as identifying a key regulatory node rather than a fully defined molecular pathway.

Overall, this study offers valuable insights into the age-related loss of regenerative capacity in the central nervous system and introduces a computational framework that may be broadly useful for investigating dynamic gene regulation in other biological contexts.

Major Points:

(1) MACS mouse anti-A2B5 microbeads are not OPC-specific and may also label astrocyte precursor cells or immature astrocytes. How do the authors justify this caveat? Could some of the claimed "OPC-specific" switch genes in fact be enriched in astrocyte lineage cells?

(2) Overall, Figures 1 and 2 are not very informative in terms of biological insight. The authors should provide more detail in the main figures regarding the enriched gene sets associated with each of the Type 1-4 switch categories. For example, summarizing the top Gene Ontology terms for each switch type would greatly enhance interpretability.

(3) A similar issue applies to Figure 3. The authors should explicitly specify the transcription factors in the main figure, particularly the 27 TFs identified through the ENCODE/ReMap2 analysis.

(4) Have the authors validated Bcl11a expression across different CNS cell types and between young and aged conditions using independent methods such as qPCR, immunofluorescence, or western blotting?

(5) Regarding OPC aging, an open question is whether the reduced differentiation capacity of aged OPCs is an intrinsic property of the cells themselves or whether it results from prolonged exposure to an aging environment that induces non-cell-autonomous epigenetic or genetic changes, thereby rendering OPCs less efficient at differentiating. It would be helpful if the authors could expand on this point in the Discussion, with reference to relevant previous studies and experimental evidence.

(6) Do the authors observe a change in the number or density of OPCs between young and aged mice?

(7) The in vivo characterization of Bcl11a overexpression using the AAV-based approach appears incomplete. Do aged mice overexpressing Bcl11a in Sox10⁺ cells exhibit reduced age-related myelin degeneration under baseline conditions? In the LPC model, do the authors observe differences in lesion size and/or remyelination efficiency?

(8) Are the authors presenting gSWITCH for the first time in this manuscript? Given that the gSWITCH framework is novel and central to the study, its conceptual contribution could be emphasized more strongly. A brief comparison with existing trajectory- or pattern-based methods-ideally in the main text around Figure 1-would help readers better appreciate its novelty.

(9) The evolutionary analysis also appears somewhat disconnected from the rest of the study. Could the authors leverage available public datasets to test whether a similar Bcl11a expression trajectory is observed in human oligodendrocyte lineage cells?

Reviewer #2 (Public review):

Summary:

This paper formulates an individual-based model to understand the evolution of division of labor in vertebrates. The model considers a population subdivided in groups, each group has a single asexually-reproducing breeder, other group members (subordinates) can perform two types of tasks called "work" or "defense", individuals have different ages, individuals can disperse between groups, each individual has a dominance rank that increases with age, and upon death of the breeder a new breeder is chosen among group members depending on their dominance. "Workers" pay a reproduction cost by having their dominance decreased, and "defenders" pay a survival cost. Every group member receives a survival benefit with increasing group size. There are 6 genetic traits, each controlled by a single locus, that control propensities to help and disperse, and how task choice and dispersal relate to dominance. To study the effect of group augmentation without kin selection, the authors cross-foster individuals to eliminate relatedness. The paper allows for the evolution of the 6 genetic traits under some different parameter values to study the conditions under which division of labour evolves, defined as the occurrence of different subordinates performing "work" and "defense" tasks. The authors envision the model as one of vertebrate division of labor.

The main conclusion of the paper is that group augmentation is the primary factor causing the evolution of vertebrate division of labor, rather than kin selection. This conclusion is drawn because, for the parameter values considered, when the benefit of group augmentation is set to zero, no division of labor evolves and all subordinates perform "work" tasks but no "defense" tasks.

Strengths:

The model incorporates various biologically realistic details, including the possibility to evolve age polytheism where individuals switch from "work" to "defence" tasks as they age or vice versa, as well as the possibility of comparing the action of group augmentation alone with that of kin selection alone.

Weaknesses from the previous round of review::

The model and its analysis are limited, which in my view makes the results insufficient to reach the main conclusion that group augmentation and not kin selection is the primary cause of the evolution of vertebrate division of labour. There are several reasons.

First, although the main claim that group augmentation drives the evolution of division of labour in vertebrates, the model is rather conceptual in that it doesn't use quantitative empirical data that applies to all/most vertebrates and vertebrates only. So, I think the approach has a conceptual reach rather than being able to achieve such conclusion about a real taxon.

Second, I think that the model strongly restricts the possibility that kin selection is relevant. The two tasks considered essentially differ only by whether they are costly for reproduction or survival. "Work" tasks are those costly for reproduction and "defense" tasks are those costly for survival. The two tasks provide the same benefits for reproduction (eqs. 4, 5) and survival (through group augmentation, eq. 3.1). So, whether one, the other, or both helper types evolve presumably only depends on which task is less costly, not really on which benefits it provides. As the two tasks give the same benefits, there is no possibility that the two tasks act synergistically, where performing one task increases a benefit (e.g., increasing someone's survival) that is going to be compounded by someone else performing the other task (e.g., increasing that someone's reproduction). So, there is very little scope for kin selection to cause the evolution of labour in this model. Note synergy between tasks is not something unusual in division of labour models, but is in fact a basic element in them, so excluding it from the start in the model and then making general claims about division of labour is unwarranted. In their reply, the authors point out that they only consider fertility benefits as this, according to them, is what happens in cooperative breeders with alloparental care; however, alloparental care entails that workers can increase other's survival *without group augmentation*, such as via workers feeding young or defenders reducing predator-caused mortality, as a mentioned in my previous review but these potentially kin-selected benefits are not allowed here.

Third, the parameter space is understandably little explored. This is necessarily an issue when trying to make general claims from an individual-based model where only a very narrow parameter region of a necessarily particular model can be feasibly explored. As in this model the two tasks ultimately only differ by their costs, the parameter values specifying their costs should be varied to determine their effects. In the main results, the model sets a very low survival cost for work (yh=0.1) and a very high survival cost for defense (xh=3), the latter of which can be compensated by the benefit of group augmentation (xn=3). Some limited variation of xh and xn is explored, always for very high values, effectively making defense unevolvable except if there is group augmentation. In this revision, additional runs have been included varying yh and keeping xh and xn constant (Fig. S6), so without addressing my comment as xn remains very high. Consequently, the main conclusion that "division of labor" needs group augmentation seems essentially enforced by the limited parameter exploration, in addition to the second reason above.

Fourth, my view is that what is called "division of labor" here is an overinterpretation. When the two helper types evolve, what exists in the model is some individuals that do reproduction-costly tasks (so-called "work") and survival-costly tasks (so-called "defense"). However, there are really no two tasks that are being completed, in the sense that completing both tasks (e.g., work and defense) is not necessary to achieve a goal (e.g., reproduction). In this model there is only one task (reproduction, equation 4,5) to which both helper types contribute equally and so one task doesn't need to be completed if completing the other task compensates for it; instead, it seems more fitting to say that there are two types of helpers, one that pays a fertility cost and another one a survival cost, for doing the same task. So, this model does not actually consider division of labor but the evolution of different helper types where both helper types are just as good at doing the single task but perhaps do it differently and so pay different types of costs. In this revision, the authors introduced a modified model where "work" and "defense" must be performed to a similar extent. Although I appreciate their effort, this model modification is rather unnatural and forces the evolution of different helper types if any help is to evolve.

I should end by saying that these comments don't aim to discourage the authors, who have worked hard to put together a worthwhile model and have patiently attended to my reviews. My hope is that these comments can be helpful to build upon what has been done to address the question posed.

[Editors' note: the authors have provided responses to the each of these points.]

Reviewer #1 (Public review):

Summary:

The authors aimed to characterize neurocomputational signals underlying interpersonal guilt and responsibility. Across two studies, one behavioral and one fMRI, participants made risky economic decisions for themselves or for themselves and a partner; they also experienced a condition in which the partners made decisions for themselves and the participant. The authors also assessed momentary happiness intermittently between choices in the task. Briefly, the results demonstrated that participants' self-reported happiness decreased after disadvantageous outcomes for themselves and when both they and their partner were affected; and this effect was exacerbated when participants were responsible for their partner's low outcome, rather than the opposite, reflecting experienced guilt. Consistent with previous work, BOLD signals in the insula correlated with experienced guilt and insula-right IFG connectivity was enhanced when participants made risky choices for themselves and safe choices for themselves and a partner.

Strengths:

This study implements an interesting approach to investigating guilt and responsibility; the paradigm in particular is well-suited to approach this question, offering participants the chance to make risky vs. safe choices that affect both themselves and others. I appreciate the assessment of happiness as a metric for assessing guilt across the different task/outcome conditions, as well as the implementation of both computational models and fMRI.

Weaknesses:

In spite of the overall strengths of the study, I think there are a few areas in which the paper fell a bit short and could be improved.

Comment on the revised submission:

I appreciate the authors' attention to all of my comments and questions regarding the initial version of the paper. However, I still do not believe that the point about the small volume correction in the insula has been adequately addressed. The authors claim that because the SVC was done using an anatomically defined ROI, that it is valid and not double dipping. I understand where the authors are coming from. However, there are a few issues here. First, any use of ROIs is best done via pre-registration (Gentili et al., 2021, European Journal of Neuroscience). Second, the whole set of analyses in this section leading up to the SVC seems somewhat circular. The first step was a whole brain contrast of lottery vs. safe outcomes, which revealed activation in many areas including the insula. Then, it appears that the parameter estimates from the insula were extracted and submitted offline to linear mixed models probing for effects of outcome magnitude, social condition and time, which revealed that the insula activation demonstrated the 'sought after' effect. Next, the manuscript states that the authors attempted to confirm these results with a univariate analysis for the so-called guilt effect within regions showing a stronger response to outcomes of risky relative to safe outcomes, which again showed activation in the insula (not surprisingly), and then a small volume correction was applied to these insula voxels. While an anatomical ROI from a different study was used for the correction, the issue is that multiple analyses already revealed that the insula was involved in the effect of interest. It is unclear why this is even necessary given that the LMM analysis demonstrated the expected result.

Reviewer #2 (Public review):

Summary

This manuscript focuses on the role of social responsibility and guilt in social decision making by integrating neuroimaging and computational modeling methods. Across two studies, participants completed a lottery task in which they made decisions for themselves or for a social partner. By measuring momentary happiness throughout the task, the authors show that being responsible for a partner's bad lottery outcome leads to decreased happiness compared to trials in which the participant was not responsible for their partner's bad outcome. At the neural level, this guilt effect was reflected in increased neural activity in the anterior insula, and altered functional connectivity between the insula and the inferior frontal gyrus. Using computational modeling, the authors show that trial by trial fluctuations in happiness were successfully captured by a model including participant and partner rewards and prediction errors (a 'responsibility' model), and model-based neuroimaging analyses suggested that prediction errors for the partner were tracked by the superior temporal sulcus. Taken together, these findings suggest that responsibility and interpersonal guilt influence social decision making.

Strengths

This manuscript investigates the concept of guilt in social decision making through both statistical and computational modeling. It integrates behavioral and neural data, providing a more comprehensive understanding of the psychological mechanisms. For the behavioral results, data from two different studies is included, and although minor differences are found between the two studies, the main findings remain consistent. The authors share all their code and materials, leading to transparency and reproducibility of their methods.

The manuscript is well-grounded in prior work. The task design is inspired by a large body of previous work on social decision making, and includes the necessary conditions to support their claims (i.e., Solo, Social, and Partner conditions). The computational models used in this study are inspired by previous work, and build on well-established economic theories of decision making. The research question and hypotheses clearly extend previous findings, and the more traditional univariate results align with prior work.

The authors conducted extensive analyses, as supported by the inclusion of different linear models and computational models described in the supplemental materials. Psychological concepts like risk preferences are defined and tested in different ways, and different types of analyses (e.g., univariate and multivariate neuroimaging analyses) are used to try to answer the research questions. The inclusion and comparison of different computational models provides compelling support for the claim that partner prediction errors indeed influence task behavior, as illustrated by the multiple model comparison metrics and the good model recovery.

The authors did a good job acknowledging other factors that could differ between the conditions, including the role of other emotions (like empathy) or agency in the decision making process. These additional analyses and nuances strengthen the manuscript and the interpretability of the findings.

Weaknesses

As the authors already note, they did not directly ask participants to report their feelings of guilt. The authors clearly describe this limitation, and also note that in addition to guilt, other emotions like empathy could also be at play in interpersonal decisions. Despite this limitation, this study provides insights into the neural and behavioral mechanisms of responsibility and guilt in social decision making, and how they influence behavior.

Reviewer #1 (Public 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.

Weaknesses:

While the study addresses an interesting and timely question with potentially broad implications for host-pathogen interactions and amyloid biology, several aspects of the experimental design and data analysis require further clarification and strengthening.

Major Comments:

(1) In Figure 1A, the author showed "stronger binding affinity" based on shifts at lower peptide concentrations, but no quantitative binding parameters (e.g., apparent Kd, fraction bound, or densitometric analysis) are presented. This claim would be better supported by including: (i) A binding curve with quantification of free vs bound RNA band intensities (ii) Replicates and error estimates (mean {plus minus} SD).

(2) The authors report droplet formation at low RNA (50 ng/µL) but protein aggregation at high RNA (400 ng/µL) through fluorescence microscopy. However, no intermediate RNA concentrations (e.g., 100-300 ng/µL) are tested or discussed, leaving a critical gap in understanding the full phase diagram and transition mechanisms. Additionally, the behaviour of PSMα3 in the absence of RNA under LLPS conditions is not shown. Without protein-only data, it is difficult to assess if droplets are RNA-induced or if protein has a weak baseline LLPS that RNA tunes. The saturation concentration (csat) for PSMα3 phase separation, either in the absence or presence of RNA, should be reported.

(3) For a convincing LLPS claim, it is important to show: Quantitative FRAP curves (mobile fraction and half-time of recovery) rather than only microscopy images and qualitative statements.

(4) The manuscript highly relies on fluorescence microscopy to show colocalization. However, the colocalization is presented in a qualitative manner only. The manuscript would benefit from the inclusion of quantitative metrics (e.g., Pearson's correlation coefficient, Manders' overlap coefficients, or intensity correlation analysis).

(5) In Figures 3 B and 3C, the contrast between "no AT630 at 30 min, strong at 2 h" (50 ng/μL) and "strong at 30 min" (400 ng/μL) is compelling, but a simple quantification (e.g., mean fluorescence intensity per area) would greatly increase rigor.

(6) In Figure S3 ssCD data, if possible, indicate whether the α-helical signal increases with RNA concentration or shows a non-linear dependence, which might link to the LLPS vs solid aggregate regimes.

(7) In Figure 5B, FRAP recovery in dying cells may reflect artifactual mobility rather than biological relevance. Additionally, the absence of quantification data limits interpretation; providing recovery curves would clarify relevance.

(8) The narrative conflates cytotoxicity endpoints (membrane damage, PI staining, aggregates) with localization data (nucleolar foci), creating ambiguity about whether nucleolar targeting drives toxicity or is a consequence of cell death. Separating toxicity assessment from localization analysis, or clearly demonstrating that nucleolar accumulation precedes cytotoxicity, would resolve this ambiguity.

(9) In Figure 8, to strengthen the LLPS assignment for LL-37, additional evidence, such as FRAP analysis or observation of droplet fusion events, would be valuable. This is particularly relevant given that the heat shock conditions (65{degree sign}C for 15 minutes) could potentially induce partial denaturation or nonspecific coacervation.

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 described the associated liquid-liquid phase separation. They also compare the influence of RNA on the aggregation and activity of LL-37, which shows differences from that on PSMalpha3.

Strengths:

That RNA impacts PSM cytotoxicity when co-incubated in vitro becomes clear.

Weaknesses:

I have two major and fundamental problems with this study:

(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, which 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.

(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.

Overall, the findings can be explained in a much more straightforward way with the common concept of cytotoxicity being due to monomeric PSMs, and the impact of nucleic acids on cytotoxicity being due to lowering of the concentration of that active form by RNA attachment. Further limiting the significance of the findings, whether this interaction has any biological significance on the physiology or infectivity of the PSM producer remains largely unexplored.

Reviewer #3 (Public review):

Summary:

The manuscript by Rayan et al. aims to investigate the role of RNA in modulating both virulent amyloid and host-defense peptides, with the objective of understanding their self-assembly mechanisms, morphological features, and aggregation pathways.

Strengths:

The overall content is well-structured with a logical flow of ideas that effectively conveys the research objectives.

Weaknesses:

(1) Figure 2 displays representative FRAP images demonstrating fluorescence recovery within seconds. To gain a more comprehensive understanding of how recovery after photobleaching varies under different conditions, it is recommended to supplement these images with corresponding quantitative fluorescence recovery curves for analysis.

(2) Ostwald ripening typically leads to the shrinkage or even disappearance of smaller droplets, accompanied by the further growth of large droplets. However, the droplet size in Figure 2D decreases significantly after 2 h of incubation. This observation prompts the question, what is the driving force underlying RNA-regulated phase separation and phase transition?

(3) The manuscript aims to study the role of RNA in modulating PSMα3 aggregation by using solution-state NMR to obtain residue-specific structural information. The current NMR data, as described in the method and figure captions, were recorded in the absence of RNA. Whether RNA binding induces conformational changes of PSMα3, and how these changes alter the NMR spectra? Also, the sequential NOE walk between neighboring residues can be annotated on the spectrum for clarity.

(4) The authors claim that LL-37 shares functional, sequence, and structural similarities with PSMα3. However, no droplet formation was observed of LL-37 in the presence of RNA only. The authors then applied thermal stress to induce phase separation of LL-37. What are the main factors contributing to the different phase behaviors exhibited by LL-37 and PSMα3? What are the differences in the conformation of amyloid aggregates and the kinetics of aggregation between the condensation-induced aggregation in the presence of RNA and the conventional nucleation-elongation process in the absence of RNA for these two proteins?

Reviewer #1 (Public review):

Summary:

In the ecological interactions between wild plants and specialized herbivorous insects, structural innovation-based diversification of secondary metabolites often occurs. In this study, Agrawal et al. utilized two milkweed species (Asclepias curassavica and Asclepias incarnata) and the specialist Monarch butterfly (Danaus plexippus) as a model system to investigate the effects of two N,S-cardenolides-formed through structural diversification and innovation in A. curassavica-on the growth, feeding, and chemical sequestration of D. plexippus, compared to other conventional cardenolides. Additionally, the study examined how cardenolide diversification resulting from the formation of N,S-cardenolides influences the growth and sequestration of D. plexippus. On this basis, the research elucidates the ecophysiological impact of toxin diversity in wild plants on the detoxification and transport mechanisms of highly adapted herbivores.

Strengths:

The study is characterized by the use of milkweed plants and the specialist Monarch butterfly, which represent a well-established model in chemical ecology research. On one hand, these two organisms have undergone extensive co-evolutionary interactions; on the other hand, the butterfly has developed a remarkable capacity for toxin sequestration. The authors, building upon their substantial prior research in this field and earlier observations of structural evolutionary innovation in cardenolides in A. curassavica, proposed two novel ecological hypotheses. While experimentally validating these hypotheses, they introduced the intriguing concept of a "non-additive diversity effect" of trace plant secondary metabolites when mixed-contrasting with traditional synergistic perspectives-in their impact on herbivores.

Weaknesses:

The manuscript has two main weaknesses. First, as a study reliant on the control of compound concentrations, the authors did not provide sufficient or persuasive justification for their selection of the natural proportions (and concentrations) of cardenolides. The ratios of these compounds likely vary significantly across different environmental conditions, developmental stages, pre- and post-herbivory, and different plant tissues. The ecological relevance of the "natural proportions" emphasized by the authors remains questionable. Furthermore, the same compound may even exert different effects on herbivorous insects at different concentrations. The authors should address this issue in detail within the Introduction, Methods, or Discussion sections.

Second, the study was conducted using leaf discs in an in vitro setting, which may not accurately reflect the responses of Monarch butterflies on living plants. This limitation undermines the foundation for the novel ecological theory proposed by the authors. If the observed phenomena could be validated using specifically engineered plant lines-such as those created through gene editing, knockdown, or overexpression of key enzymes involved in the synthesis of specific N,S-cardenolides-the findings would be substantially more compelling.

Reviewer #2 (Public review):

I have reviewed both the original and revised version of this manuscript and while no additional experiments were added, I find the interpretations and discussion of the limitations of the study have improved. This is appreciated.

My original concern regarding the mixture treatments largely remains. Figure 4 nicely shows that the mixtures are more potent than the average of all single compounds. However, Fig S3 shows that the effects of mixtures are not significantly different from effects of at least one, single N,S compound (voruscharin or uscharin) across all measured growth/sequestration responses. Essentially, the effects of single N,S compounds is similar to mixtures (which also contain N,S compounds).

While the current results are certainly interesting as presented, in my view the main takeaway of the manuscript would be more compelling if it could be demonstrated that it isn't simply the presence of N,S compounds in the mixtures driving the observations. For example, does a mixture of all compounds except voruscharin or uscharin still have stronger growth/sequestration effects compared to single non-N,S compounds?

Reviewer #1 (Public review):

Domínguez-Rodrigo and colleagues make a moderately convincing case for habitual elephant butchery by Early Pleistocene hominins at Olduvai Gorge (Tanzania), ca. 1.8-1.7 million years ago. They present this at the site scale (the EAK locality, which they excavated), as well as across the penecontemporaneous landscape, analyzing a series of findspots that contain stone tools and large-mammal bones. The latter are primarily elephants, but giraffids and bovids were also butchered in a few localities. The authors claim that this is the earliest well-documented evidence for elephant butchery; doing so requires debunking other purported cases of elephant butchery in the literature, or in one case, reinterpreting elephant bone manipulation as being nutritional (fracturing to obtain marrow) rather than technological (to make bone tools). The authors' critical discussion of these cases may not be consensual, but it surely advances the scientific discourse. The authors conclude by suggesting that an evolutionary threshold was achieved at ca. 1.8 ma, whereby regular elephant consumption rich in fats and perhaps food surplus, more advanced extractive technology (the Acheulian toolkit), and larger human group size had coincided.

The fieldwork and spatial statistics methods are presented in detail and are solid and helpful, especially the excellent description (all too rare in zooarchaeology papers) of bone conservation and preservation procedures. However, the methods of the zooarchaeological and taphonomic analysis - the core of the study - are peculiarly missing. Some of these are explained along the manuscript, but not in a standard Methods paragraph with suitable references and an explicit account of how the authors recorded bone-surface modifications and the mode of bone fragmentation. This seems more of a technical omission that can be easily fixed than a true shortcoming of the study. The results are detailed and clearly presented.

By and large, the authors achieved their aims, showcasing recurring elephant butchery in 1.8-1.7 million-year-old archaeological contexts. Nevertheless, some ambiguity surrounds the evolutionary significance part. The authors emphasize the temporal and spatial correlation of (1) elephant butchery, (2) Acheulian toolkits, and (3) larger sites, but do not actually discuss how these elements may be causally related. Is it not possible that larger group size or the adoption of Acheulian technology have nothing to do with megafaunal exploitation? Alternative hypotheses exist, and at least, the authors should try to defend the causation, not just put forward the correlation. The only exception is briefly mentioning food surplus as a "significant advantage", but how exactly, in the absence of food-preservation technologies? Moreover, in a landscape full of aggressive scavengers, such excess carcass parts may become a death trap for hominins, not an advantage. I do think that demonstrating habitual butchery bears very significant implications for human evolution, but more effort should be invested in explaining how this might have worked.

Overall, this is an interesting manuscript of broad interest that presents original data and interpretations from the Early Pleistocene archaeology of Olduvai Gorge. These observations and the authors' critical review of previously published evidence are an important contribution that will form the basis for building models of Early Pleistocene hominin adaptation.

Reviewer #2 (Public review):

The authors argue that the Emiliano Aguirre Korongo (EAK) assemblage from the base of Bed II at Olduvai Gorge shows systematic exploitation of elephants by hominins about 1.78 million years ago. They describe it as the earliest clear case of proboscidean butchery at Olduvai and link it to a larger behavioral shift from the Oldowan to the Acheulean.

The manuscript makes a valuable contribution to the Olduvai Gorge record, offering a detailed description of the EAK faunal assemblage. In particular, the paper provides a high-resolution record of a juvenile Elephas recki carcass, associated lithic artifacts, and several green-broken bone specimens. These data are inherently valuable and will be of significant interest to researchers studying Early Pleistocene taphonomy.

Comments on previous round of revisions:

The revised manuscript does a good job of using less definitive language, particularly by adding "possible" qualifiers to several interpretations. This addresses the concern about overstatement.

The main issue raised in the original review, however, remains unresolved. Only two elephant bone specimens at EAK show green-bone breakage interpreted as anthropogenic, and the diagnostic basis for that interpretation is not demonstrated clearly on the EAK material itself. The manuscript discusses a suite of fracture attributes described as diagnostic of dynamic percussive breakage, but these attributes are not explicitly documented on the EAK specimens. Instead, the diagnostic traits are illustrated using material from other Olduvai contexts, and that behavior is then extrapolated to make similar claims at EAK. For a paper making a potentially important behavioral argument, the key diagnostic evidence is not clearly demonstrated at the focal assemblage.

This problem is evident in the presentation of the EAK specimens. In their response, the authors state that one EAK specimen shows "overlapping scars" and constitutes a "long bone flake"; however, these features are not clearly identifiable in the figures or captions as currently presented. The authors state that Figures S21-S23 clearly indicate human agency, including a long bone flake with overlapping scars and a view of the medullary surface, but it is unclear which specimens or surfaces these descriptions refer to. Figure S21 does appear to show green fracture and is described only as an "elephant-sized flat bone fragment with green-bone curvilinear break." Figure S22 shows the same bone and cortical surface in a different orientation, providing no additional information. In Figure S23, I cannot clearly identify a medullary surface or evidence of green-bone fracture from this image. None of these images clearly demonstrates overlapping scars, and the figures would be substantially improved by explicitly identifying the features described in the text. Even if both EAK specimens are accepted as green-broken, they do not demonstrate the co-occurrence of multiple diagnostic fracture traits such as multiple green breaks, large step fractures, hackle marks, and overlapping scars that the authors state is required to attribute dynamic percussive activity to hominins and address equifinality.

I appreciate that the authors are careful to state that spatial association between stone tools and fossils alone does not demonstrate hominin behavior, and that they treat the spatial analyses as supportive rather than decisive. While the association is intriguing, the problem is downstream: spatial association is used to strengthen an interpretation of butchery at EAK that still depends on fracture evidence that is not clearly documented at the assemblage level.

The critique concerning Nyayanga is not addressed in the revision. The manuscript proposes alternative explanations for the Nyayanga material but does not demonstrate why these are more plausible than the interpretation advanced by Plummer et al. (2023). I am not arguing that the Nyayanga material should be accepted as butchery; rather, showing that trampling is possible does not establish it as more probable than cut marks. In contrast, the EAK material is treated as evidence of butchery on the basis of evidence that, in my opinion, is more limited and less clearly demonstrated. Even if this is not the authors' intention, the uneven treatment removes an earlier megafaunal case from the comparison and strengthens the case for interpreting EAK as marking a behavioral shift toward megafaunal butchery by excluding other early cases.

While I remain concerned about how the EAK evidence is documented and interpreted, I think the manuscript is appropriate for publication and will generate useful discussion. Readers can then assess for themselves whether the available evidence supports the strength of the behavioral claims.

[Editors' note: the authors are encouraged to make this version the Version of Record.]

Reviewer #1 (Public review):

Summary:

The authors investigate how UVC induced DNA damage alters the interaction between the mitochondrial transcription factor TFAM and mtDNA. Using live-cell imaging, qPCR, atomic force microscopy (AFM), fluorescence anisotropy, and high-throughput DNA-chip assays, they show that UVC irradiation reduces TFAM sequence specificity and increases mtDNA compaction without protecting mtDNA from lesion formation. From these findings the authors suggest that TFAM acts as a "sensor" of damage rather than a protective or repair-promoting factor.

Strengths:

(1) The focus on UVC damage offers a clean system to study mtDNA damage sensing independently of more commonly studied repair pathways, such as oxidative DNA damage. The impact of UVC damage is not well understood in the mitochondria and this study fills that gap in knowledge.

(2) In particular, the custom mitochondrial genome DNA chip provides high resolution mapping of TFAM binding and reveals a global loss of sequence specificity following UVC exposure.

(3) The combination of in vitro TFAM DNA biophysical approaches combined with cellular responses (gene expression, mtDNA turnover) provides a coherent multi-scale view.

(4) The authors demonstrate that TFAM induced compaction does not protect mtDNA from UVC lesions, an important contribution given assumptions about TFAM providing protection.

Weaknesses:

(1) The authors show a decrease in mtDNA levels and increased lysosomal colocalization but do not define the pathway responsible for degradation. Distinguishing between replication dilution, mitophagy, or targeted degradation would strengthen the interpretation and justifies future experiments.

(2) The manuscript briefly notes enrichment of TFAM at certain regions of the mitochondrial genome but provides little interpretation of why these regions are favored. Discussion of whether high-occupancy sites correspond to regulatory or structural elements would add valuable context.

(3) The authors provide a discrepancy between the anisotropy and binding array results. The reason for this is not clear and one wonders if an orthogonal approach for the binding experiments would elucidate this difference (minor point).

Assessment of conclusions:

The manuscript successfully meets its primary goal of testing whether TFAM protects mtDNA from UVC damage and the impact this has on the mtDNA. While their data points to an intriguing model that TFAM acts as a sensor of damaged mtDNA, the validation of this model requires further investigation to make the model more convincing. This is likely warranted for a followup study. Also the biological impact of this compaction, such as altering transcription levels is not clear in this study.

Impact and utility of the methods:

This work advances our understanding of how mitochondria manage UVC genome damage and proposes a structural mechanism for damage "sensing" independent of canonical repair. The methodology, including the custom TFAM DNA chip, will be broadly useful to the scientific community.

Context: The study supports a model in which mitochondrial genome integrity is maintained not only by repair factors, but also by selective sequestration or removal of damaged genomes. The demonstration that TFAM compaction correlates with damage rather than protection reframes an interesting role in mtDNA quality control.

Comments on revised version:

The authors addressed all concerns during the revision.

Reviewer #2 (Public review):

Summary:

King et al. present several sets of experiments aimed to address potential impact of UV irradiation on human mitochondrial DNA as well as possible role of mitochondrial TFAM protein in handling UV irradiated mitochondrial genomes. The carefully worded conclusion derived from the results of experiments performed with human HeLa cells, in vitro small plasmid DNA, with PCR-generated human mitochondrial DNA and with UV-irradiated small oligonucleotides is presented in the title of the manuscript: "UV irradiation alters TFAM binding to mitochondrial DNA". Authors also interpret results of somewhat unconnected experimental approaches to speculate that "TFAM as a potential DNA damage sensing protein in that it promotes UVC-dependent conformational changes in the [mitochondrial] nucleoids, making them more compact. They further propose that such a proposed compaction might trigger removal of UV-damaged mitochondrial genomes as well as facilitates replication of undamaged mitochondrial genomes.

Strengths:

(1) Authors presented convincing evidence that a very high dose (1500 J/m2) of UVC applied to oligonucleotides covering the entire mitochondrial DNA genome alleviates sequence specificity of TFAM binding (Figure 3). This high dose was sufficient to cause UV-lesions in a large fraction of individual oligonucleotides. The method has been developed in the lab of one of the corresponding authors (ref. 74) and is technically well refined. This result can be published as is or in combination with other data.

(2) Manuscript also presents AFM evidence (Figure 4) that TFAM, which was long known to facilitate compaction of mitochondrial genome (Alam et al., 2003; PMID 12626705 and follow up citations), causes in vitro compaction of a small pUC19 plasmid and that approximately 3 UVC lesions per plasmid molecule results in slight albeit detectable increase in TFAM compaction of the plasmid.

Both results are discussed in line of a possible extrapolation to in vivo phenomena. The revised version of the discussion includes a clear statement that no in vivo support was provided within the set of experiments presented in the manuscript.

Weaknesses:

The experiments presented on Figures 3 and 4 may support the speculation that TFAM can carry protective role of eliminating mitochondrial genomes with bulky lesions by way of excessive compaction and removal damaged genomes from the in vivo pool, however extensive additional studies that would go well beyond the experiments described in this paper are needed to fill the gap between this set of results and the proposed explanations.

Reviewer #3 (Public review):

Summary

The study is grounded in the observation that mitochondrial DNA (mtDNA) shows some resistance to mutagenesis under genotoxic stress. The manuscript focuses on the effects of UVC-induced DNA damage on TFAM-DNA binding in vitro and in cells. The authors demonstrate increased TFAM-DNA compaction following UVC irradiation in vitro, as assessed by high-throughput protein-DNA binding assays and atomic force microscopy (AFM). The authors did not observe a similar trend in fluorescence polarization assays and attributed the difference in the extent of TFAM oligomerization as a potential reason. In cells, the authors found that UVC exposure increased mRNA levels of TFAM, POLG, and POLRMT without altering mitochondrial membrane potential. Overexpressing TFAM in cells or varying TFAM concentration in reconstituted nucleoids did not alter the accumulation or disappearance of mtDNA damage. Based on their data, the authors proposed a plausible model: following UVC-induced DNA damage, TFAM facilitates nucleoid compaction, which may signal damage in the mitochondrial genome. The proposed model may inspire future follow-up studies to further study the role of TFAM in sensing UVC-induced damage.

Comments on revised version:

The authors have addressed the reviewer's concerns.

Reviewer #1 (Public review):

Summary:

This fundamental study identifies a new mechanism that involves a mycobacterial nucleomodulin manipulation of the host histone methyltransferase COMPASS complex to promote infection. Although other intracellular pathogens are known to manipulate histone methylation, this is the first report demonstrating specific targeting the COMPASS complex by a pathogen. The rigorous experimental design using of state-of-the art bioinformatic analysis, protein modeling, molecular and cellular interaction and functional approaches, culminating with in vivo infection modeling provide convincing, unequivocal evidence that supports the authors claims. This work will be of particular interest to cellular microbiologist working on microbial virulence mechanisms and effectors, specifically nucleomodulins, and cell/cancer biologists that examine COMPASS dysfunction in cancer biology.

Strengths:

(1) The strengths of this study include the rigorous and comprehensive experimental design that involved numerous state-of-the-art approaches to identify potential nucleomodulins, define molecular nucleomodulin-host interactions, cellular nucleomodulin localization, intracellular survival, and inflammatory gene transcriptional responses, and confirmation of the inflammatory and infection phenotype in a small animal model.

(2) The use of bioinformatic, cellular and in vivo modeling that are consistent and support the overall conclusions is a strengthen of the study. In addition, the rigorous experimental design and data analysis including the supplemental data provided, further strengthens the evidence supporting the conclusions.

Comments on revisions:

The authors have previously addressed the weaknesses that were identified by this reviewer by providing rational explanation and specific references that support the findings and conclusions.

Reviewer #2 (Public review):

Summary:

The manuscript by Chen et al addresses an important aspect of pathogenesis for mycobacterial pathogens, seeking to understand how bacterial effector proteins disrupt the host immune response. To address this question the authors sought to identify bacterial effectors from M. tuberculosis (Mtb) that localize to the host nucleus and disrupt host gene expression as a means of impairing host immune function. Their revised manuscript has strengthened their observations by performing additional experiments with BCG strains expressing tagged MgdE.

Strengths:

The researchers conducted a rigorous bioinformatic analysis to identify secreted effectors containing mammalian nuclear localization signal (NLS) sequences, which formed the basis of quantitative microscopy analysis to identify bacterial proteins that had nuclear targeting within human cells. The study used two complementary methods to detect protein-protein interaction: yeast two-hybrid assays and reciprocal immunoprecipitation (IP). The combined use of these techniques provides strong evidence of interactions between MgdE and SET1 components and suggests the interactions are in fact direct. The authors also carried out rigorous analysis of changes in gene expression in macrophages infected with MgdE mutant BCG. They found strong and consistent effects on key cytokines such as IL6 and CSF1/2, suggesting that nuclear-localized MgdE does in fact alter gene expression during infection of macrophages. The revised manuscript contains additional biochemical analyses of BCG strains expressing tagged MgdE that further supports their microscopy findings.

Reviewer #3 (Public review):

In this study, Chen L et al. systematically analyzed the mycobacterial nucleomodulins and identified MgdE as a key nucleomodulin in pathogenesis. They found that MgdE enters into host cell nucleus through two nuclear localization signals, KRIR108-111 and RLRRPR300-305, and then interacts with COMPASS complex subunits ASH2L and WDR5 to suppress H3K4 methylation-mediated transcription of pro-inflammatory cytokines, thereby promoting mycobacterial survival.

Comments on revisions:

The authors have previously adequately addressed previous concerns through additional experimentation. The revised data robustly support the main conclusions, demonstrating that MgdE engages the host COMPASS complex to suppress H3K4 methylation, thereby repressing pro-inflammatory gene expression and promoting mycobacterial survival. This work represents a significant conceptual advance.

Reviewer #1 (Public review):

Summary:

This work by Beaudet and colleagues aims at exploring the effect of phosphorylation on the formation of tau envelopes and consequently on axonal transport, both in vitro on reconstituted microtubules and in human excitatory neurons derived from IPSCs.

The authors found that a relatively widely used construct in which 14 serine or threonine residues, often hyperphosphorylated in Alzheimer's disease, are mutated to alanines (phosphodeficient), increases the density of tau envelopes compared to wildtype tau, whereas a phosphomimetic (same residues mutated to glutamic acid) reduces envelope density both in vitro and in human excitatory neurons derived from IPSCs.

By analysing the trafficking of different kinesins (KIF1a and KIF5C), they observed different effects of tau phosphorylation status on the movement of these two motors.

They then analyse transport of lysosomes by employing live imaging of lysotracker in human excitatory neurons derived from IPSCs transfected with wildtype, phosphodeficient or phosphomimetic tau, observing that phosphodeficient tau seems to reduce transport of lysosomes while phosphomimetic increases transport compared to wildtype tau.

Strengths:

(1) The work aims to study a novel and underexplored topic in the tau field, tau envelopes, and investigate their relevance to Alzheimer's disease pathology.

(2) Experiments are well conducted and of high quality.

Weaknesses:

Relying only on in vitro reconstituted microtubules and human neurons derived from IPSCs leaves some doubts about the relevance of these results for Alzheimer's disease, considering the embryonic state of IPSCs-derived neurons.

Reviewer #2 (Public review):

This manuscript examines how disease-associated hyperphosphorylation disrupts tau's role as a cooperative microtubule-binding regulator of intracellular transport. Using in vitro reconstitution assays and live-cell imaging in iPSC-derived neurons, the authors employ phosphomutant tau constructs (E14 to mimic hyperphosphorylation, AP to prevent phosphorylation) at 14 disease-associated residues to isolate phosphorylation effects independent of expression system-dependent PTM heterogeneity. The results show that hyperphosphorylated tau fails to form cooperative envelope-like structures on microtubules, instead binding diffusely and dissociating rapidly. In contrast, wild-type and phospho-resistant tau form cohesive envelopes that regulate motor protein access. At the single-molecule level, hyperphosphorylation reduces KIF5C inhibition while maintaining or enhancing KIF1A inhibition through altered processivity and detachment rates. In live neurons, hyperphosphorylated tau phenocopies tau knockout conditions, weakening tau-mediated inhibition of lysosome transport and increasing processive motility. The authors quantify tau binding using Gaussian mixture model-based image analysis and measure tau kinetics via FRAP, demonstrating that hyperphosphorylation-induced loss of cooperative binding correlates with dysregulated organelle transport. These findings establish a mechanism by which phosphorylation-driven disruption of tau's gatekeeper function on microtubules compromises axonal transport prior to aggregation in tauopathies. The paper provides interesting new knowledge for the field, but there are outstanding concerns that could be further addressed by the authors to strengthen and clarify the current manuscript:

(1) Lack of Phosphatase-Treated Control and Explicit WT Phosphorylation Quantification

Wild-type tau expressed in insect and mammalian cells is known to be phosphorylated by endogenous kinases (eg, GSK3, CDK5, MARK). The manuscript acknowledges this in the Discussion but provides no phosphatase-treated lysate control or quantification of endogenous phosphorylation on WT tau via phospho-specific Western blots. This leaves ambiguity about whether observed differences between WT and E14 reflect purely the introduced mutations or confounding baseline differences in phosphostate content.

(2) Limited Normalization of Motor Effects to Measured Tau Lattice Occupancy

Although kinesin trajectories are classified inside vs. outside tau envelopes (inherently normalizing to local tau density), motor parameters are not systematically reported as functions of tau fluorescence intensity across all constructs. Co-purifying MAPs or microtubule-modifying enzymes in cell lysates is not quantified or excluded, leaving residual uncertainty about tau-specificity of observed motor inhibition. This should be at least acknowledged in the results section.

(3) Insufficient Citation of Prior Neuronal Tau Envelope Evidence

In the Introduction, the authors state, "it was an open question if tau forms envelopes in neurons," but this understates existing evidence. Tan et al. (2019) report tau neuronal staining consistent with envelope formation, while Siahaan et al. (2021) provide more direct evidence in non-neuronal cells. The framing should acknowledge and integrate these prior findings.

(4) Unclear Wording on Expression System-Dependent Phosphorylation

The sentence "The phosphostate of tau is strongly dependent on the expression system" requires rewording. It is ambiguous whether this refers to the final phosphostate achieved after expression or the inherent phosphorylating capacity of each system. Clearer language would strengthen the methodological justification.

(5) Insufficient Quantification of Motor and Lysosome Transport Effect Magnitudes in Results Section

The data on molecular motor motility and lysosome transport are densely described. The magnitude of effects (fold-changes, percentage differences) should be explicitly stated in the Results section when first presenting findings to orient readers to biological significance. For example, effect magnitudes for lysosome run lengths, velocities, and directional bias should be quantified in text, not left to figure inspection.

(6) Incomplete Discussion of Projection Domain Necessity for Envelope Formation

The Discussion states the projection domain is "a critical regulator of both tau-tau and tau-microtubule interactions," but does not engage with prior domain dissection work. Tan et al. (2019) found that the entire projection domain is not necessary for envelope formation in vitro. The authors should discuss which projection domain regions are specifically regulated by phosphorylation vs. required for cooperativity, providing a more nuanced interpretation than implied by their current framing.

Reviewer #1 (Public review):

Summary:

This study uses high-throughput bacterial cell-surface display to identify LC3B-interacting peptides in the human proteome. The screen is unbiased, and this type of assay has not previously been used for selecting LC3B-interacting peptides. The screen was done with a library of 500,000 peptides, and they ended up with 427 peptides that they scored as high-confidence LC3B binders. The experiments performed are solid, and data are analyzed using well-documented methods and statistics.

The aim of the authors was to isolate LC3B-interacting peptides from the human proteome, and the screen succeeded in doing so. The selected set of peptides included several previously reported LIR motifs, but also many novel LC3B binding peptides that either contained or did not contain the canonical core LIR motif [WFY]xx[LVI].

Another aim was to identify binding determinants important for the LC3B interaction, and they made an interesting sequence logo based on selected LIR-containing peptides. However, this study does not really extend our knowledge related to binding determinants essential for LIR motifs in LC3B binding. They basically verify known characteristics, including the importance of varied types of electrostatic interactions supporting the docking of the core LIR into the LDS of LC3B.

Strengths:

The approach used here (high-throughput bacterial-surface-display) is new. The screen is unbiased, and the fact that peptides are directly tested for LC3B binding may facilitate the discovery of non-canonical LIR motifs. The screen appears to be highly selective and manages to distinguish between peptides that interact with LC3B and peptides that do not interact.

Weaknesses:

It is a limitation that no proteins are analyzed in this study. Further work is therefore needed to verify that identified LIR motifs are functional in full-length proteins and in cells.

Reviewer #2 (Public review):

Summary:

To discover peptides that interact with autophagy-related protein LC3B and profile the key binding determinants, the authors screened a library of ~500,000 36-residue peptides derived from the human proteome using bacterial cell-surface display. Analysis of the screening data revealed exceptions to the reported LIR motif and a strong preference for negatively charged residues adjacent to the LIR.<br /> These results support a refinement of the LIR motif definition and expand the network of candidate LC3B interaction partners.

Strengths:

High-throughput approach.

Weaknesses:

Lack of in vitro data and molecular dynamics simulations.

Reviewer #3 (Public review):

Summary:

The LC3 family of proteins, which includes LC3B, are ubiquitin-like proteins that are covalently linked to phosphatidylethanolamine in the expanding autophagosomal membrane during autophagy. LC3 family members bind to short sequences of amino acids that reside within dynamic regions in a wide variety of proteins. These sequences, termed LC3 Interacting Regions (LIRs), were initially thought to function primarily to link LIR-containing autophagy cargo receptors to LC3 family members to help facilitate their capture during autophagy. However, the functional importance of LIRs in autophagy has broadened to include more general functions in autophagy as well. While a general consensus for LIR sequences has been described as [FWY]0-X1-X2-[LVI]3, recent work has suggested that additional sequences outside of the canonical LIR sequence can bind LC3 family members and play important roles in autophagy. In this manuscript by Kosmatka et al, the authors perform a high-throughput screen using bacterial surface display coupled with fluorescence-associated cell sorting to identify which human sequences can bind to LC3B. They identify a variety of peptides capable of binding LC3B, including peptides from proteins that have not previously been described as LC3B-binding proteins. The results from the bacterial surface display were then used to guide sequence analysis, mutational analysis, and structural studies to further characterize the range of LIR sequences that are capable of binding LC3B. Taken together, this work adds to the growing knowledge of how LIR sequences interact with LC3 family members and demonstrates which amino acids both inside and outside of the LIR sequence aid in binding. This work also identifies new potential LC3 binding proteins, which may play unknown roles in autophagy regulation. Lastly, this work reinforces the importance of alternative LIR sequences such as the [WFY]0-X1-X2-[WFY]3 sequence, which the authors have dubbed the LIR+ sequence.

Strengths:

The manuscript uses a robust approach to identify and characterize different peptide sequences that can interact with LC3B. They validate a large number of sequences using biolayer interferometry (BLI) and attempt to correlate different amino acids with their binding affinity for LC3B. The large number of LC3B binding sequences and their dissociation constants adds significant new information to the field that will help others understand what sequences can bind to LC3B. The authors are also very careful to accurately report on their data and not overly interpret their findings.

Weaknesses:

After the authors identify proteins from their bacterial display assay, the remainder of the manuscript is focused on characterizing the different types of sequences that are identified in addition to validating the LC3B-LIR interactions using biochemical approaches, including BLI and X-ray crystallography. However, it's not entirely clear if the screen identified novel LC3B binders that interact with LC3B in cells. While I acknowledge that the focus of the manuscript is on the characterization of LIR sequences that can bind LC3B, it seems like a missed opportunity not to validate a few of the novel LC3B binders in vivo. This may result in the demonstration of novel binders of LC3B in cells and may further demonstrate the strength of this approach for identifying LC3 family member binding partners. Therefore, it would be helpful to look at a few proteins identified in the HC set that have not previously been identified as LC3B binders in cells to determine if they CO-IP with LC3B or interact with LC3B using a different approach.

Reviewer #1 (Public review):

Summary:

The study provides insightful characterization of the mycobacterial secreted effector protein MmpE which translocates to the host nucleus and exhibits phosphatase activity. The study characterizes the nuclear localization signal sequences and residues critical for the phosphatase activity, both of which are required for intracellular survival

Strengths:

(1) The study addresses the role of nucleomodulins, an understudied aspect in mycobacterial infections.

(2) The authors employ a combination of biochemical and computational analyses along with in vitro and in vivo validations to characterize the role of MmpE.

Weaknesses:

(1) While the study establishes that the phosphatase activity of MmpE operates independently of its NLS, there is a clear gap in understanding how this phosphatase activity supports mycobacterial infection. The investigation lacks experimental data on specific substrates of MmpE or pathways influenced by this virulence factor.

(2) The study does not explore whether the phosphatase activity of MmpE is dependent on the NLS within macrophages, which would provide critical insights into its biological relevance in host cells. Conducting experiments with double knockout/mutant strains and comparing their intracellular survival with single mutants could elucidate these dependencies and further validate the significance of MmpE's dual functions.

(3) The study does not provide direct experimental validation of the MmpE deletion on lysosomal trafficking of the bacteria.

(4) The role of MmpE as a mycobacterial effector would be more relevant using virulent mycobacterial strains such as H37Rv.

Comments on revisions:

I appreciate the work the authors have done to address reviewers comments. The revised manuscript looks significantly improved. My major concern in the revised version is the microscopy data where the BCG staining using the DiD fluorescent stain does not bring out the rod-shaped bacilli structure. I suggest the authors either use a GFP reporter or some other fluorescent stain to address this issue.

Reviewer #2 (Public review):

Summary:

In this paper, the authors have characterized Rv2577 as a Fe3+/Zn2+ -dependent metallophosphatase and a nucleomodulin protein. The authors have also identified His348 and Asn359 as critical residues for Fe3+ coordination. The authors show that the proteins encode for two nuclease localization signals. Using C-terminal Flag expression constructs, the authors have shown that MmpE protein is secretory. The authors have prepared genetic deletion strains and show that MmpE is essential for intracellular survival of M. bovis BCG in THP-1 macrophages, RAW264.7 macrophages and mice model of infection. The authors have also performed RNA-seq analysis to compare the transcriptional profiles of macrophages infected with wild type and mmpE mutant strain. The relative levels of ~ 175 transcripts were altered in mmpE mutant infected macrophages and majority of these were associated with various immune and inflammatory signalling pathways. Using these deletion strains, the authors proposed that MmpE inhibits inflammatory gene expression by binding to the promoter region of vitamin D receptor. The authors also showed that MmpE arrests phagosome maturation by regulating the expression of several lysosome associated genes such as TFEB, LAMP1, LAMP2 etc. These findings reveal a sophisticated mechanism by which a bacterial effector protein manipulates gene transcription and promotes intracellular survival.

Strength:

The authors have used a combination of cell biology, microbiology and transcriptomics to elucidate the mechanisms by which Rv2577 contributes to intracellular survival.

Weakness:

The authors should thoroughly check the mice data and show individual replicate values in bar graphs.

Comments on revisions:

Thanks to the authors for addressing the concerns raised during the review of the original manuscript. The data is now presented with clarity, and discrepancies in mouse experiments have also been addressed with additional experiments.

Reviewer #3 (Public review):

Summary:

In this manuscript titled "Mycobacterial Metallophosphatase MmpE Acts as a Nucleomodulin to Regulate Host Gene Expression and Promote Intracellular Survival", Chen et al describe biochemical characterisation, localisation and potential functions of the gene using a genetic approach in M. bovis BCG and perform macrophage and mice infections to understand the roles of this potentially secreted protein in the host cell nucleus. The findings demonstrate the role of a secreted phosphatase of M. bovis BCG in shaping the transcriptional profile of infected macrophages, potentially through nuclear localisation and direct binding to transcriptional start sites, thereby regulating the inflammatory response to infection.

Strengths:

The authors demonstrate using a transient transfection method that MmpE when expressed as a GFP-tagged protein in HEK293T cells, exhibits nuclear localisation. The authors identify two NLS motifs that together are required for nuclear localisation of the protein. A deletion of the gene in M. bovis BCG results in poorer survival compared to the wild type parent strain, which is also killed by macrophages. Relative to the WT strain infected macrophages, macrophages infected with the mmpE strain exhibited differential gene expression. Overexpression of the gene in HEK293T led to occupancy of the transcription start site of several genes, including the Vitamin D Receptor. Expression of VDR in THP1 macrophages was lower in case of mmpE infection compared to WT infection. This data supports the utility of the overexpression system in identifying potential target loci of MmpE using the HEK293T transfection model. The authors also demonstrate that the protein is a phosphatase and the phosphatase activity of the protein is partially required for bacterial survival but not for regulation of the VDR gene expression.

Weaknesses:

There are significant differences in lysosomal retention between M. tuberculosis and M. bovis BCG. This study uses BCG and MMPE overexpression to draw conclusions about the impact of the MMPE gene on host gene expression and the bacteria's lysosomal localisation. While the authors have convincingly supported their claims with this model system, the relevance of this mechanism in M. tuberculosis infection remains unaddressed.

Reviewer #1 (Public review):

Summary:

Metabolic dysfunction-associated steatotic liver disease (MASLD) ranges from simple steatosis, steatohepatitis, fibrosis/cirrhosis, and hepatocellular carcinoma. In the current study, the authors aimed to determine the early molecular signatures differentiating patients with MASLD associated fibrosis from those patients with early MASLD but no symptoms. The authors recruited 109 obese individuals before bariatric surgery. They separated the cohorts as no MASLD (without histological abnormalities) and MASLD. The liver samples were then subjected to transcriptomic and metabolomic analysis. The serum samples were subjected to metabolomic analysis. The authors identified dysregulated lipid metabolism, including glyceride lipids, in the liver samples of MASLD patients compared to the no MASLD ones. Circulating metabolomic changes in lipid profiles slightly correlated with MASLD, possibly due to the no MASLD samples derived from obese patients. Several genes involved in lipid droplet formation were also found elevated in MASLD patients. Besides, elevated levels of amino acids, which are possibly related to collagen synthesis, were observed in MASLD patients. Several antioxidant metabolites were increased in MASLD patients. Furthermore, dysregulated genes involved in mitochondrial function and autophagy were identified in MASLD patients, likely linking oxidative stress to MASLD progression. The authors then determined the representative gene signatures in the development of fibrosis by comparing this cohort with the other two published cohorts. Top enriched pathways in fibrotic patients included GTPas signaling and innate immune responses, suggesting the involvement of GTPas in MASLD progression to fibrosis. The authors then challenged human patient derived 3D spheroid system with a dual PPARa/d agonist and found that this treatment restored the expression levels of GTPase-related genes in MASLD 3D spheroids. In conclusion, the authors suggested the involvement of upregulated GTPase-related genes during fibrosis initiation.

Significance:

Overall, the current study might provide some new resources regarding transcriptomic and metabolomic data derived from obese patients with and without MASLD. The MASLD research community will be interested in the resource data.

Comments on revised version:

I have no further comments. Thank you.

Reviewer #3 (Public review):

Summary:

Metabolic dysfunction associated liver disease (MASLD) describes a spectrum of progressive liver pathologies linked to life style-associated metabolic alterations (such as increased body weight and elevated blood sugar levels), reaching from steatosis over steatohepatitis to fibrosis and finally end stage complications, such as liver failure and hepatocellular carcinoma. Treatment options for MASLD include diet adjustments, weight loss, and the receptor-β (THR-β) agonist resmetirom, but remain limited at this stage, motivating further studies to elucidate molecular disease mechanisms to identify novel therapeutic targets.

In their present study, the authors aim to identify early molecular changes in MASLD linked to obesity. To this end, they study a cohort of 109 obese individuals with no or early-stage MASLD combining measurements from two anatomic sides: 1. bulk RNA-sequencing and metabolomics of liver biopsies, and 2. metabolomics from patient blood. Their major finding is that GTPase-related genes are transcriptionally altered in livers of individuals with steatosis with fibrosis compared to steatosis without fibrosis.

Major comments:

(1) Confounders (such as (pre-)diabetes)

The patient table shows significant differences in non-MASLD vs. MASLD individuals, with the latter suffering more often from diabetes or hypertriglyceridemia. Rather than just stating corrections, subgroup analyses should be performed (accompanied with designated statistical power analyses) to infer the degree to which these conditions contribute to the observations. I.e., major findings stating MASLD-associated changes should hold true in the subgroup of MASLD patients without diabetes/of female sex and so forth (testing for each of the significant differences between groups).

Post-rebuttal update: The authors have performed the requested sub-group analysis and find the gene signatures hold for the non-diabetic sub-cohort, but not the diabetic subgroup. They denote a likely interaction between fibrosis and diabetes, that was not corrected for in the original analysis.

Post-post-rebuttal update: I thank the authors for having added Figure 5-figure supplement 2 to show this analysis.

(2) External validation

Additionally, to back up the major GTPase signature findings, it would be desirable to analyze an external dataset of (pre)diabetes patients (other biased groups) for alternations in these genes. It would be important to know if this signature also shows in non-MASLD diabetic patients vs. healthy patients or is a feature specific to MASLD. Also, could the matched metabolic data be used to validate metabolite alterations that would be expected under GTPase-associated protein dysregulation?

Post-rebuttal update: The authors confirm that with the present data, insulin resistance cannot be fully ruled out as a confounder to the GTP-ase related gene signature. They however plan future mouse model experiments to study whether the GTPase-fibrosis signature differs in diabetic vs. non-diabetic conditions.

(3) 3D liver spheroid MASH model, Fig. 6D/E

This 3D experiment is technically not an external validation of GTPase-related genes being involved in MASLD, since patient-derived cells may only retain changes that have happened in vivo. To demonstrate that the GTPase expression signature is specifically invoked by fibrosis the LX-2 set up is more convincing, however, the up-regulation of the GTPase-related genes upon fibrosis induction with TGF-beta, in concordance with the patient data, needs to be shown first (qPCR or RNA-seq). Additionally, the description of the 3D model is too uncritical. The maintenance of functional PHHs is a major challenge (PMID: 38750036, PMID: 21953633, PMID: 40240606, PMID: 31023926). It cannot be ruled out that their findings are largely attributable to either 1) the (other present) mesenchymal cells (i.e., mesenchyme-derived cells, such as for example hepatic stellate cells, not to be confused with mesenchymal stem cells, MSCs), or 2) related to potential changes in PHHs in culture, and these limitations need to be stated.

Post-rebuttal update: To address the concern of other cells than hepatocytes contributing to the observed effects in culture, the authors performed TGF-beta treatment in independent mono-cultures (Figure R4): LX-2 and hepatocytes, and the spheroid system. Surprisingly, important genes highlighted in Figure 6E for the spheroid system (RAB6A, ARL4A, RAB27B, DIRAS2) are all absent from this qPCR(?) validation experiment. The authors evaluate instead RAC1, RHOU, VAV1, DOCK2, RAB32. ­In spheroids, RHOU and RAB32 are down-regulated with TGF-B. In hepatocytes DOCK2 and RAC seemed up-regulated. They find no difference in these genes in LX-2 cells. Surprisingly, ACTA2 expression values are missing for LX-2 cells. Together, it is hard to judge which individual cell type recapitulates the changes observed in patients in this validation experiment, as the major genes called out in Figure 6E are not analyzed.

Post-post-rebuttal update: I thank the authors for having added Figure 6-figure supplement 5 to show qPCR results for this question.

Unfortunately, the 3D liver spheroid model used (as presente­d in PMID39605182) lacks important functional validation tests of maintained hepatocyte identity in culture (at the very least Albumin expression and secretion plus CYP3A4 assay). This functional data (acquired at the time point in culture when the RNA expression analysis in 6E was performed) is indispensable prior to stating that mature hepatocytes cause the observed effects.

Post-post-rebuttal update: I thank the authors for having added more references, I still think a quick functional validation of the system (at the time point in culture when the RNA expression analysis in 6E was performed) would be beneficial.

(4) Novelty / references

Similar studies that also combined liver and blood lipidomics/metabolomics in obese individuals with and without MASLD (e.g. PMID 39731853, 39653777) should be cited. Additionally, it would benefit the quality of the discussion to state how findings in this study add new insights over previous studies, if their findings/insights differ, and if so, why.

Post-rebuttal update: The authors have included the studies into their discussion.

Overall post-post-rebuttal update: I thank the authors for having added more data, important discussion points, and references, and have no further requests.

Reviewer #1 (Public review):

Summary:

The hippocampus, especially the ventral subregion, has been related to emotional processing. However, the specific circuitry involved deserves further investigation. By using a bidirectional optogenetic modulation, Kambali et al. have investigated the role of different inputs to vCA1 (i.e., from vCA3 and entorhinal cortex) in anxiety- and fear-related responses. The major findings of this work suggested that both inputs to vCA1 control fear-related responses, whereas only the projection between vCA3 and vCA1 controls anxiety-related behavior. Overall, the authors used an advanced methodological approach, which allows them to modulate specific brain circuits, to study specific hippocampal projections, providing some new information regarding the hippocampal function in anxiety and fear.

Strengths:

(1) The manuscript is well written, clear and has a detailed and specific discussion.

(2) Results from each optogenetic manipulation are clear in different anxiety- and fear-related tasks, demonstrating the robustness of the findings.

(3) The overall conclusions are very interesting and might be relevant for the field of mental health disorders accompanied by anxiety- and fear-related alterations.

Weaknesses:

(1) The major differences in basal behavioral performance in the different paradigms between the two optogenetic modulations prevent the achievement of strong conclusive results.

(2) Data presentation and representative figures need a major revision.

(3) No analysis has been performed to analyze potential sex differences in behavioral domains where sex is important.

Reviewer #2 (Public review):

Summary:

This paper uses an optogenetic approach to either activate or inhibit separate neural pathways projecting to the ventral CA1 hippocampal subregion, from either CA3 or the entorhinal cortex. The authors report that manipulation of the vCA3→vCA1 pathway affected behavioural performance on a number of tasks: elevated plus maze, open field, Vogel conflict test and freezing behaviour to both context and a trace CS cue. In contrast, optogenetic manipulation of neural activity in the EC→vCA1 pathway only affected behaviour on the trace CS/context fear memory test but had no effect on the elevated plus maze, open field or Vogel conflict test. The authors suggest different roles for these two ventral hippocampal pathways in fear versus anxiety.

Strengths:

This is an interesting study addressing an important question in a highly topical subject area. The experiments are well conducted and have generated interesting and important data.

Weaknesses:

While I am broadly sympathetic to the overall narrative of the paper, I have some questions/comments around the specific interpretation of the results presented. In my view, the authors' claims may not be completely supported by their data, but the data are interesting nonetheless.

In terms of the framework presented by the authors for interpreting their data, many would argue that freezing (or at least reduced activity/behavioural inhibition) to the context provides a readout of conditioned anxiety rather than fear. In this sense, the context is a signal of potential threat (i.e. the context becomes associated with both shock and with the absence of shock) and thus generates anxiety rather than fear. Likewise, the trace CS cue could be considered as an ambiguous predictor of shock in that the shock doesn't occur straight away. In contrast, a punctate CS cue which co-terminates with shock would be a reliable signal of imminent threat and thus generates a fear response. Thus, it might be argued that all of the assays adopted by the authors are readouts of anxiety (albeit comprising tests of both conditioned and unconditioned anxiety). For example, from the authors' perspective, it is not clear a priori why the Vogel conflict test is considered anxiety, but contextual freezing is considered fear? Indeed, in the Discussion, the authors mention another study in which the data from the Vogel conflict test align with fear assays rather than anxiety tests. Can the authors elaborate on their distinction? I appreciate that, in practice, it might be difficult to distinguish between fear and anxiety at the behavioural level in rodents (although opposing effects of fear and anxiety on pain responses might be one option). At the very least, this issue merits further discussion.

Another question is whether rather than representing a qualitative difference between the contributions of the vCA3→vCA1 and EC→vCA1 pathways to different aspects of fear/anxiety behaviours, the different results reflect a quantitative difference between the magnitude of effects in vCA1 that are generated from optogenetic manipulation of the two pathways, coupled with the possibility that behaviour on the trace CS/context fear memory task is more sensitive to manipulation than the "anxiety tests". The possibility that vCA3→vCA1 stimulation is more effective is potentially supported by the c-fos measurements in vCA1. vCA3→vCA1 stimulation produced a much bigger vCA1 c-fos response (approx. 350% c-fos cell activation; see Figure 1E) compared to activation of the EC→vCA1 pathway (approx. 170% c-fos cell activation; see Figure 4E).

Furthermore, in some studies, there seem to be quite large differences between the laser OFF conditions for the different groups (which presumably one would not expect to be different). For example, compare laser OFF for the Inhibition group for time in open arms of EPM in Figure 5C (> 40%) versus laser OFF for the Inhibition group for time in open arms of EPM in Fig. 2C (< 20%). This could potentially result in ceiling effects, such that it is very hard to see a further increase in time in the open arms from a level already above 40% when the laser is then switched on. This could complicate the interpretation of the laser ON condition.

Likewise, there is a big difference between the behavioral performance of the two SHAM groups in Figure 3 (compare SHAM in 3 B, C and SHAM in 3 D, E). How is this explained? Could this generate a ceiling effect? This may also merit some discussion. More details on the SHAM procedure(s) in the main manuscript may also be helpful.

According to Figure 3A, the test of freezing response to the trace Tone CS is conducted in a different context from the conditioning context. The data presented in Figure 3 for tone fear are the levels of freezing during the presentation of this cue in the different contexts. It would be important to present both pre-CS and CS freezing levels here to determine how much of the freezing is actually driven by the punctate tone CS. The pre-CS freezing levels in this different context would also provide a nice control for the contextual fear conditioning.

Reviewer #3 (Public review):

Summary:

In their paper entitled "Ventral hippocampal temporoammonic and Schaffer collateral pathways differential control fear- and anxiety-related behaviors" the authors use a bidirectional optogenetic approach to elucidate the role of temporammonic (TA) and Schaffer collateral (SC) inputs to the ventral hippocampus (CA1) in modulating both fear and anxiety-related behaviors. While fear and anxiety behaviors are often considered on a continuous spectrum, identifying neural pathways that are differentially activated represents an important open question in the field. The authors find that optogenetic stimulation or inhibition of the Schaffer Collateral pathway in the ventral hippocampus (CA3-CA1) bidirectionally modulates both fear-related and anxiety-related behavioral paradigms. More specifically, optogenetic excitation of the CA3-CA1 pathway using ChR2-expressing viral constructs increases anxiety-like behaviors in numerous behavioral paradigms (elevated plus maze, open field, Vogel conflict test). Conversely, optogenetic inhibition using halorhodopsin reduced anxiety-like behaviours. To examine fear behaviors, the authors examined contextual and trace fear conditioning. Similar to their results with anxiety-like behaviors, the authors observed bidirectional fear modulation following optogenetic stimulation of the vCA3-vCA1 pathway. The authors next examined the temporammonic pathway originating from the lateral entorhinal cortex to vCA1. Unlike with SC stimulation, stimulation of the TA pathway had no effect on anxiety-like behaviors but did bidirectionally modulate contextual fear conditioning. Together, these results differentiate the SC and TA pathways in the ventral hippocampus as distinct regulators of affective behavior.

Strengths:

The paper has numerous technical strengths, including dissecting the role of both excitation and inhibition of both pathways and the use of behavioral measures of anxiety and fear. This balanced and internally controlled design allows readers to evaluate the effects of both pathways in a single study, thereby reducing technical complications from experiments being completed across laboratories and experimental conditions.

Weaknesses:

There are a few limitations of the study, however, which bear discussion.

(1) The authors use halorhodopsin to achieve optogenetic inhibition. Halorhodopsin is generally considered a first-generation optogenetic actuator, as it is a Cl- pump rather than an ion channel. This limits the degree of inhibition (i.e. by preventing shunting inhibition) and can result in altered chloride gradients in the period immediately following optogenetic stimulation. This is of particular concern in this paper as the stimulation parameters and behavioral analysis are not temporally correlated, therefore confounds of disrupted chloride cannot be experimentally accounted for or controlled.

(2) The authors use an AAV-CaMKII-eGFP as a control (Sham) throughout the dataset; however, in the trace fear conditioning experiments, there are no AAV-CaMKII-ChR2-eYFP or AAV-CaMKII-eNpHR3.0-eYFP controls without optogenetic stimulation. Therefore, it is unclear the extent to which viral expression of optogenetic actuators impacts behavior. Additionally, the authors only provided optogenetic stimulation during contextual fear recall and tone fear recall. Additional experiments disrupting each pathway during trace conditioning would have provided additional insight into the role of each pathway in the initial encoding of fear memories.

(3) The location and extent of viral expression across animals were not systematically quantified.

Overall, however, these weaknesses do not significantly detract from the main conclusions of the paper. The authors' data convincingly demonstrates that disruption of the trisynaptic circuit bidirectionally modulates both fear- and anxiety-like behaviors while disruption of the temporammonic pathway has no effect on anxiety-like behaviors but disrupts fear-related behaviors. It is interesting to note, however, that the TA activation had no effect on tone-related fear conditioning, suggesting a potential specialized role of the temporammonic pathway specifically in contextual fear memory.

Reviewer #1 (Public review):

The main significance of this work is characterizing the function of a new gene Lmod1 in muscle stem cell biology. The study suggests an intriguing regulatory mechanism by which Sirt1 sequesters Lmod1 in a specific temporal window during myogenesis.

Comments on revisions:

The authors have satisfactorily addressed my inquires. Thank you.

Reviewer #2 (Public review):

Summary:

In this manuscript, the authors identify Leiomodin-1 (LMOD1) as a key regulator of early myogenic differentiation, demonstrating its interaction with SIRT1 to influence SIRT1's cellular localization and gene expression. The authors propose that LMOD1 translocates SIRT1 from the nucleus to the cytoplasm to permit the expression of myogenic differentiating genes such as MYOD or Myogenin.

Strengths:

A major strength of this work lies in the robust temporal resolution achieved through a time-course mass spectrometry analysis of in vitro muscle differentiation. This provides novel insights into the dynamic process of myogenic differentiation, often under explored in terms of temporal progression. The authors provide a strong mechanistic case for how LMOD1 exerts its role on muscle differentiation which opens avenues to modulate.

Weaknesses:

In the revised manuscript, the authors begin to translate their in vitro findings to an in vivo context by examining SIRT1 expression across a regeneration time course (Fig. 4I). They observe an increase in SIRT1 expression concomitant with LMOD1, supporting a potential role for SIRT1 in myogenic differentiation. Future studies will be required to provide deeper mechanistic insight into SIRT1 function in vivo.

Discussion:

Overall, the study emphasizes the importance of understanding the temporal dynamics of molecular players during myogenic differentiation and provides valuable proteomic data that will benefit the field. Future studies should explore whether LMOD1 modulates the nuclear-cytoplasmic shuttling of other transcription factors during muscle development and how these processes are mechanistically achieved. Investigating whether LMOD1 can be therapeutically targeted to enhance muscle regeneration in contexts such as exercise, aging, and disease will be critical for translational applications. Additionally, elucidating the interplay among LMOD1, LMOD2, and LMOD3 could uncover broader implications for actin cytoskeletal regulation in muscle biology. The authors have nicely updated their discussion.

Reviewer #3 (Public review):

Summary:

In this manuscript, the investigators identified LMOD1 as one of a subset of cytoskeletal proteins that levels increase in early stages of myogenic differentiation. Lmod1 is understudied in striated muscle and in particular in myogenic differentiation. Thus, this is an important study. It is also a very thorough study, with perhaps even too much data presented. Importantly, the investigators observed that LMOD1 appears to be important for skeletal regeneration, myogenic differentiation and that it interacts with SIRT1. Both primary myoblast differentiation and skeletal muscle regeneration were studied. Rescue experiments confirmed these observations: SIRT1 can rescue perturbations of myogenic differentiation as a result of LMOD1 knockdown.

Strengths:

Particular strengths include: an important topic, the use of primary skeletal cultures, the use of both cell culture and in vivo approaches, careful biomarker analysis of primary mouse myoblast differentiation, the use of two methods to probe the function of the Lmod1/SIRT1 pathway via using depletion approaches and inhibitors, and the generation of six independent myoblast cultures. Results support their conclusions.

Weaknesses:

(1) Figure 1. Images of cells in Figure 1A are too small to be meaningful (especially in comparison to the other data presented in this figure). Perhaps make graphs smaller?

(2) Line 148 "We found LMOD2 to be the most abundant Lmod in whole skeletal muscle." This is confusing since most, if not all, prior studies have shown that Lmod3 is the predominant isoform in skeletal muscle. The two papers that are cited are incorrectly cited. Clarification to resolve this discrepancy is needed.

(3) Figure 2. Immunofluorescence (IF) panels are too small to be meaningful. Perhaps the graphs could be made smaller and more space allocated for the IF panels? This issue is apparent for just about all IF panels - they are simply too small to be meaningful. Additionally, in many of the immunofluorescence figures, the colors that were used make it difficult to discern the stained cellular structures. For example, in Figure S1, orange and purple are used - they do not stand out as well as other colors that are more commonly used.

(4) There is huge variability in many experiments presented - as such, more samples appear to be required to allow for meaningful data to be obtained. For example, Figure S2. Many experimental groups, only have 3 samples - this is highly problematic - I would estimate that 5-6 would be the minimum.

(5) Ponceau S staining is often used as a loading control in this manuscript for western blots. The area/molecular weight range actually used should be specified. Not clear why in some experiments GAPDH staining is used, in other experiments Ponceau S staining is used, and in some, both are used. In some experiments the variability of total protein loaded from lane-to-lane is disconcerting. For example, in Figure S4C there appears to be more than normal variability. Can the protein assay be redone and the samples run again?

(6) Figure S3 - Lmod3 is included in the figure but no mention of it occurs in the title of the figure and/or legend.

(7) Abstract, line 25. "overexpression accelerates and improves the formation of myotubes". This is a confusing sentence. How is it improving the formation? A little more information about how they are different than developing myotubes in normal/healthy muscle would be helpful

(8) Impossible from IF figures presented to determine where Lmod1 localizes in the myocytes. Information on its subcellular localization is important. Does it localize with Lmod2 and Lmod3 at thin filament pointed ends?

Comments on revisions:

Many comments have been adequately addressed. However, some concerns remain.

Former Concern #2. The issue with the lack of detection of LMOD3 in their muscle samples is troublesome and has not been adequately resolved in the revised manuscript. It is a fact that most, if not all, studies on Lmod3 report that it is the most abundant isoform in skeletal muscle. This issue should be discussed in the manuscript. It is recognized that a different assay was utilized in this paper. The papers that are cited continue to remain incorrect. Specifically:

Tsukada et al., reports abundance of LMOD2 in cardiac muscle, not in skeletal muscle.

Nworu et al., 2015 reports on LMOD3 in skeletal muscle.

Kiss et al.,2020. While this paper reveals an important function for Lmod2 in thin filament length regulation, it is clearly shows many examples of high expression of Lmod3 in various skeletal muscles isolated from mice.

Former Concern #3. With respect to small sample numbers. Hopefully a statistical editor is available to comment. While this reviewer is happy that other assays were used to verify their data, the problem still remains that many experimental groups only have 3 samples (with high variability).

Former Concern #3. Many immunofluorescence panels are hard to evaluate because of their small size.

Reviewer #1 (Public review):

In this study, the noncanonical amino acid acridon-2-ylalanine (Acd) was inserted at various positions within the human Hv1 protein using a genetic code expansion approach. The purified mutants with incorporated fluorophore were shown to be functional using a proton flux assay in proteoliposomes. FRET between native tryptophan and tyrosine residues and Acd were quantified using spectral FRET analysis. Predicted FRET efficiencies calculated from an AlphaFold model of the Hv1 dimer were compared to the corresponding experimental values. Spectral FRET analysis was also used to test whether structural rearrangements caused by Zn2+, a well-known Hv1 inhibitor, could be detected. The experimental data provide a good validation of the approach, but further expansion of the analysis will be necessary to differentiate between intra- and intersubunit structural features.

Interestingly, the observed rearrangements induced by Zn2+ were not limited to the protein region proximal to the extracellular binding site but extended to the intracellular side of the channel. This finding agrees with previous studies showing that some extracellular Hv1 inhibitors, such as Zn2+ or AGAP/W38F, can cause long-range structural changes propagating to the intracellular vestibule of the channel (De La Rosa et al. J. Gen. Physiol. 2018, and Tang et al. Brit J. Pharm 2020). The authors should consider adding these references.

Since one of the main goals of this work was to validate Acd incorporation and the spectral FRET analysis approach to detect conformational changes in hHv1 in preparation for future studies, the authors should consider removing one subunit from their dimer model, recalculating FRET efficiencies for the monomer, and comparing the predicted values to the experimental FRET data. This comparison could support the idea that the reported FRET measurements can inform not only on intrasubunit structural features but also on subunit organization.

Reviewer #2 (Public review):

This manuscript by Carmona, Zagotta, and Gordon is generally well-written. It presents a crude and incomplete structural analysis of the voltage-gated proton channel based on measured FRET distances. The primary experimental approach is Förster Resonance Energy Transfer (FRET), using a fluorescent probe attached to a noncanonical amino acid. This strategy is advantageous because the noncanonical amino acid likely occupies less space than conventional labels, allowing more effective incorporation into the channel structure.

Fourteen individual positions within the channel were mutated for site-specific labeling, twelve of which yielded functional protein expression. These twelve labeling sites span discrete regions of the channel, including P1, P2, S0, S1, S2, S3, S4, and the dimer-connecting coiled-coil domain. FRET measurements are achieved using acridon-2-ylalanine (Acd) as the acceptor, with four tryptophan or four tyrosine residues per monomer serving as donors. In addition to estimating distances from FRET efficiency, the authors analyze full FRET spectra and investigate fluorescence lifetimes on the nanosecond timescale.

Despite these strengths, the manuscript does not provide a clear explanation of how channel structure changes during gating. While a discrepancy between AlphaFold structural predictions and the experimental measurements is noted, it remains unclear whether this mismatch arises from limitations of the model or from the experimental approach. No further structural analysis is presented to resolve this issue or to clarify the conformational states of the protein.

The manuscript successfully demonstrates that Acd can be incorporated at specific positions without abolishing channel function, and it is noteworthy that the reconstituted proteins function as voltage-activated proton channels in liposomes. The authors also report reversible zinc inhibition of the channel, suggesting that zinc induces structural changes in certain channel regions that can be reversed by EDTA chelation. However, this observation is not explored in sufficient depth to yield meaningful mechanistic insight.

Overall, while the study introduces an interesting labeling strategy and provides valuable methodological observations, the analysis appears incomplete. Additional structural interpretation and mechanistic insight are needed.

Major Points

(1) Tryptophan and tyrosine exhibit similar quantum yields, but their extinction coefficients differ substantially. Is this difference accounted for in your FRET analysis? Please clarify whether this would result in a stronger weighting of tryptophan compared to tyrosine.

(2) Is the fluorescence of acridon-2-ylalanine (Acd) pH-dependent? If so, could local pH variations within the channel environment influence the probe's photophysical properties and affect the measurements?

(3) Several constructs (e.g., K125Tag, Y134Tag, I217Tag, and Q233Tag) display two bands on SDS-PAGE rather than a single band. Could this indicate incomplete translation or premature termination at the introduced tag site? Please clarify.

(4) In Figure 5F, the comparison between predicted FRET values and experimentally determined ratio values appears largely uninformative. The discussion on page 9 suggests either an inaccurate structural model or insufficient quantification of protein dynamics. If the underlying cause cannot be distinguished, how do the authors propose to improve the structural model of hHV1 or better describe its conformational dynamics?

(5) Cu²⁺, Ru²⁺, and Ni²⁺ are presented as suitable FRET acceptors for Acd. Would Zn²⁺ also be expected to function as an acceptor in this context? If so, could structural information be derived from zinc binding independently of Trp/Tyr?

(6) The investigated structure is most likely dimeric. Previous studies report that zinc stabilizes interactions between hHV1 monomers more strongly than in the native dimeric state. Could this provide an explanation for the observed zinc-dependent effects? Additionally, do the detergent micelles used in this study predominantly contain monomers or dimers?

(7) hHV1 normally inserts into a phospholipid bilayer, as used in the reconstitution experiments. In contrast, detergent micelles may form monolayers rather than bilayers. Could the authors clarify the nature of the micelles used and discuss whether the protein is expected to adopt the same fold in a monolayer environment as in a bilayer?

Reviewer #1 (Public review):

Summary:

This revised manuscript describes critical intermediate reaction steps of a HA synthase at the molecular level; specifically, they examine the 2nd step, polymerization, adding GlcA to GlcNAc to form the initial disaccharide of the repeating HA structure. Unlike the vast majority of known glycosyltransferases, the viral HAS (a convenient proxy extrapolated to resemble the vertebrate forms) uses a single pocket to catalyze both monosaccharide transfer steps. The authors work illustrates the interactions needed to bind & proof-read the UDP-GlcA using direct and '2nd layer' amino acid residues. This step also allows the HAS to distinguish the two UDP-sugars; this is very important as the enzymes are not known or observed to make homopolymers of only GlcA or GlcNAc, but only make the HA disaccharide repeats GlcNAc-GlcA.

Strengths:

Techniques & analysis; overview of HA synthase mechanisms

Weaknesses:

None

Comments on revisions:

Previous clarity issues in the original submission were all resolved. Again, this is a very well done body of work!!

Reviewer #2 (Public review):

Summary:

The paper by Stephens and co-workers provides important mechanistic insight into how hyaluronan synthase (HAS) coordinates alternating GlcNAc and GlcA incorporation using a single Type-I catalytic centre. Through cryo-EM structures capturing both "proofreading" and fully "inserted" binding poses of UDP-GlcA, combined with detailed biochemical analysis, the authors show how the enzyme selectively recognizes the GlcA carboxylate, stabilizes substrates through conformational gating, and requires a priming GlcNAc for productive turnover.

These findings clarify how one active site can manage two chemically distinct donor sugars while simultaneously coupling catalysis to polymer translocation.

The work also reports a DDM-bound, detergent-inhibited conformation that possibly illuminates features of the acceptor pocket, although this appears to be a purification artefact (it is indeed inhibitory) rather than a relevant biological state.

Overall, the study convincingly establishes a unified catalytic mechanism for Type-I HAS enzymes and represents a significant advance in understanding HA biosynthesis at the molecular level.

Strengths:

There are many strengths.

This is a multi-disciplinary study with very high-quality cryo-EM and enzyme kinetics (backed up with orthogonal methods of product analysis) to justify the conclusions discussed above.

Comments on revisions:

The suggestions made in the initial comments have all been responded to very well.

Reviewer #1 (Public review):

This work analyzes innate resistance to drugs in mycobacteria by comparing minimum inhibitory concentrations (MICs) across a diverse panel of mycobacterial species. The results show that MICs are poorly correlated with growth rate while phylogeny associated with horizontal gene transfer underlies the observed differences in MIC, an important demonstration. A further investigation into the driver for the vast differences in susceptibility profiles shows that for three drugs the MIC is not correlated with intrabacterial drug concentrations where intrabacterial drug concentration is comprised of cytosolic and cell wall associated drug. This is a striking observation. The authors delve into the mechanisms that drive resistance to rifamycins and confirm that resistance is driven by ADP-ribosyltransferases of which two variant groups exist, one of which is kinetically faster and apparently is superior at modifying more hydrophobic rifamycins. The relative role of the two ADP-ribosyltransferases in conferring resistance especially in the species with both orthologs is not fully understood since the modified drug can possibly be further modified and transcriptional downregulation experiments performed in this work do not provide genetic evidence of perturbation of mRNA levels of the respective open reading frames.

Comments on revisions:

Demonstration of the level of transcriptional downregulation of the two Arr orthologs would have been a nice demonstration of (1) the utility of CRISPRi in other mycobacteria, (2) that the difference in rifabutin susceptibility during knockdown of Arr-1 vs Arr-X can fully be ascribed to the role of Arr-X in modifying the drug.

Reviewer #3 (Public review):

This manuscript presents a macroevolutionary approach to identification of novel high-level antibiotic resistance determinants that takes advantage of the natural genetic diversity within a genus (mycobacteria, in this case) by comparing antibiotic resistance profiles across related bacterial species and then using computational, molecular, and cellular approaches to identify and characterize the distinguishing mechanisms of resistance. The approach is contrasted with "microevolutionary" approaches based on comparing resistant and susceptible strains of the same species and approaches based on ecological sampling that may not include clinically relevant pathogens or related species. The potential for new discoveries with the macroevolution-inspired approach is evident in the diversity of drug susceptibility profiles revealed amongst the selected mycobacterial species and the identification and characterization of a new group of rifamycin-modifying ADP-ribosyltransferase (Arr) orthologs of previously described mycobacterial Arr enzymes. Additional findings that intra-bacterial antibiotic accumulation does not always predict potency within this genus, that M. marinum is a better proxy for M. tuberculosis drug susceptibility than the commonly used saprophyte M. smegmatis, and that susceptibility to semi-synthetic antibiotic classes is generally less variable than susceptibility to antibiotics more directly derived from natural products strengthen the claim that the macroevolutionary lens is valuable for elucidating general principles of susceptibility within a genus.

There are some limitations to the work. The argument for the novelty of the approach could be better articulated. While the opportunities for new discoveries presented by identification of discrepant susceptibility results between related species is evident, it is less clear how the macroevolutionary approach is further leveraged for the discovery of truly novel resistance mechanisms. The example of the discovery of Arr-X enzymes presented here relied upon foundational knowledge of previously characterized Arr orthologs. There is less clarity about what the pipeline would look like for discovery of previously unknown determinants when one is agnostic to putative mechanisms. From the point at which interspecies differences in susceptibility are noted, does the framework still remain distinct from other discovery frameworks and approaches?

While the experimentation and analyses performed are generally well designed and rigorous, there are a few instances in which broad claims are based on inferences from sample sets or data sets that are, at present, too limited to provide robust support. For example, the claim that rifampicin modification, and precisely ADP-ribosylation, is the dominant mechanism of resistance to rifampicin in mycobacteria is still a bit premature or at least an over-generalization, as other enzymatic modification mechanisms and other mechanisms such as helR-mediated dissociation of rifampicin-stalled RNA polymerases, efflux, etc were not examined. CRISPR interference was used in a demonstrative example to support this assertion, but would need to be applied more systematically to be more conclusive. The general claim that intra-bacterial antibiotic accumulation does not predict potency in mycobacteria may be another over-generalization based on the limited set of drugs and species studied.

Comments on revisions:

Discussion, lines 321-323: "We found that resistance to these antibiotics in mycobacteria do not correlate with by uptake/efflux mechanisms in the species tested..." is an over-generalization and conflicts with the following statement on lines 199-201: "for BDQ we could observe some correlation between antibiotic potency and [BDQ]IB which could be indicative of efflux playing a role in antibiotic efficacy. Given that the current statement in the Discussion only applies to 2 of 3 drugs tested, a more specific or nuanced interpretation seems warranted.

Reviewer #1 (Public 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.

Comments on revised version:

I'm satisfied with the revised manuscript and the responses to my previous concerns.

Reviewer #2 (Public review):

Summary:

In this manuscript, submitted to Review Commons (journal agnostic), 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 revised version:

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

Reviewer #4 (Public review):

Summary and background:

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.

Mouse IR/IGF1R double knockdown model:

A double knockdown mouse model was generated by interbreeding mice with different genetic backgrounds carrying floxed sites for IR and IGF-1R to produce mixed background offspring with both floxed IR and IGF-1R genes. These mice were crossed so that the podocin promoter driven-Cre (that comes on at about embryonic day 12 bas podocytes are developing) would delete IR and IGF-1R genes. Since podocin is believed to be an absolutely podocyte-specific protein, this podocin promoter this is predicted to specifically knock down the IR and IGF1R genes only in podocytes. The weight and growth of double KO offspring was not different from controls, but some proportion of the double knockdown mice subsequently developed proteinuria by 6 months and 20% died, although no specific data is provided to identify the cause of the deaths since eGFR was not decreased. Surviving mice were evaluated at 6 months of age. The efficacy of knockdown was not demonstrated in the mouse model itself, although a temperature-sensitive cell line developed from these double knockdown mice showed that expression of IR and IGF-1R proteins in the Cre-treated cell line were both reduced by about 50% (no statistical analysis of this result provided). In the knockout mice, proteinuria was significantly increased by 6 months, but not at earlier time points. Histologic analysis showed proteinaceous casts, glomerulosclerosis and interstitial fibrosis. Podocyte number was stated to be reduced by about 30% in double knockdown mice, although the method by which this was evaluated seems to have been by counting WT1 positive nuclei in glomerular cross-sections, an approach that is well-known not to be a reliable way of assessing true podocyte number. No information is provided about podocyte size, density or glomerular volume.

Comment: If IR/IGF1R deletion plays a significant role in normal podocyte function sufficient to cause proteinuria and glomerulosclerosis then the effect of reduced IR and IGF1R protein expression on podocyte function would have been expected to produce a phenotype before 6 months. A more likely scenario to explain the overall result is that deleting the IR and IGF1R genes at about embryonic day12 impacted podocyte development to a variable extent such that some mice developed fewer podocytes per glomerulus than other mice. As mice grow and their glomeruli and glomerular capillary area increases, those mice with fewer podocytes would not be able to completely cover the filtration surface with foot processes and would develop proteinuria and glomerulosclerosis. If reduced podocyte number per glomerulus is the proximate cause of the observed proteinuria, then modulation of the body and kidney growth rate by calorie restriction to slow growth (lower circulating IGF-1 levels) would be expected to be protective, while a high protein high calorie diet (higher circulating IGF-1 levels) or uni-nephrectomy to increase kidney growth rate would be expected to enhance proteinuria and glomerulosclerosis.

The model as used may be more representative of a variable degree of podocyte depletion than an effect of impaired IR/IGF1R signaling. Therefore, although the phenotype may be ultimately attributable to the IR/IGF1R gene deletions the proteinuria and glomerulosclerotic phenotype itself was probably a consequence of defective podocyte development. Examining podocyte number, size, density and glomerular volume at earlier time points (4 weeks) would help to answer this question. Therefore, a more appropriate title would be "The insulin/IGF axis is critically important (for) normal podocyte development and deployment". In this context the effect of the knockdowns on splicing would make more sense.

Cell culture studies. A cell line was generated using a temperature sensitive SV40 system that has been previously reported from this laboratory. A detailed analysis is provided to show that double knockout cells exhibited abnormal spliceosome activity. This forms the basis for the conclusion that "The insulin/IGF axis is critically important (for) controlling gene transcription in the podocyte". There are several concerns that weaken this conclusion.

(1) In the double knockdown cell culture system about 30% of cells were "lost" by 3 days and about 70% of cells were "lost" by 5days. The studies were done at the 3 day time point. It is not clear whether "lost" cells were in the process of dying, stress-induced detachment, or just growing more slowly than control due to reduced IR and IGF-1R signaling. These processes could have impacted splicing in a non-specific way independent of IR/IGF1R signaling itself.

(2) Can a single cell line derived from the double floxed mice be relied on to provide an unbiased picture of the effect of deleting IR and IGF-1R? Presumably, the transfection and selection process will select for cells that survive thereby including unknown biases, possibly related to spliceosome function. Is a single cell line adequate? These investigators have extensive experience with this type of analysis, but this question is not addressed in the discussion.

(3) To determine whether the effect is specific to reduced IR/IGFR signaling the deletion of IR and IGF-1R could be corrected by transfecting full length IR and IGF-1R cDNAs into the cells to restore normal IR/IGF1R signaling. If transfected cells with intact IR and IGF-1R expression and activity returns spliceosome activity to normal this would be evidence that receptors themselves play some role in spliceosome activity, as opposed to the downstream effect on growth limitation/stress on the cells.

(4) Other ways of testing whether the splicing effect is specifically due to reduced IR/IGF-1R signaling would be to (a) block IR and IGF1R receptors using available inhibitors, (b) remove or reduce insulin, IGF-1 and IGF-2 levels in the culture medium, (c) use low glucose and amino acid culture medium to slow growth rate independent of receptor function, (d) or block intra-cellular signaling via the IR and IGF-1R receptors through mTORC1 inhibition using rapamycin or other signaling targets.

(5) It would be useful to determine whether the cultured cells stressed in other ways (e.g. ischemia, toxins, etc.) also results in the same splicing abnormalities.

Reviewer #1 (Public review):

Summary:

The authors show that genetic deletion of the orphan tumor necrosis factor receptor DR6 in mice does not protect peripheral axons against degeneration after axotomy. Similarly, Schwann cells in DR6 mutant mice react to axotomy similarly to wild type controls. These negative results are important because previous work has indicated that loss or inhibition of DR6 is protective in disease models and also against Wallerian degeneration of axons following injury. This carefully executed counterexample is important for the field to consider.

Strengths:

A strength of the paper is the use of two independent mouse strains that knockout DR6 in slightly different ways. The authors confirm that DR6 mRNA is absent in these models (western blots for DR6 protein are less convincingly null, but given the absence of mRNA, this is likely an issue of antibody specificity). One of the DR6 knockout strains used is the same strain used in a previous paper examining the effects of DR6 on Wallerian degeneration.

The authors use a series of established assays to evaluate axon degeneration, including light and electron microscopy on nerve histological samples and cultured dorsal root ganglion neurons in which axons are mechanically severed and degeneration is scored in time lapse microscopy. These assays consistently show a lack of effect of loss of DR6 on Wallerian degeneration in both mouse strains examined.

Additional strengths are that the authors examine both the axonal response and the Schwann cell response to axotomy and use both in vivo and in vitro assays.

Therefore, these experiments, the author's data support their conclusion that loss of DR6 does not protect against Wallerian degeneration.

Weaknesses:

A weakness of this paper is that no effort is made to determine why the results presented here may differ from previous studies. A notable possibility is that the original mouse strain that showed 5 of 13 mice being protected from Wallerian degeneration was studies on a segregating C57BL/6.129S background.

Finally, it is important to note that previously reported effects of DR6 inhibition, such as protection of cultured cortical neurons from beta-amyloid toxicity, are not necessarily the same as Wallerian degeneration of axons distal to an injury studied here. The negative results presented here showing that loss of DR6 is not protective against Wallerian degeneration induced by injury are important given the interest in DR6 as a therapeutic target. However, care should be taken in attempting to extrapolate these results to other disease contexts such as ALS or Alzheimer's disease.

Reviewer #3 (Public review):

Summary:

The authors revisit the role of DR6 in axon degeneration following physical injury (Wallerian degeneration), examining both its effects on axons and its role in regulating the Schwann cell response to injury. Surprisingly, and in contrast to previous studies, they find that DR6 deletion does not delay the rate of axon degeneration after injury, suggesting that DR6 is not a mediator of this process.

Overall, this is a valuable study. As the authors note, the current literature on DR6 is inconsistent, and these results provide useful new data and clarification. This work will help other researchers interpret their own data and re-evaluate studies related to DR6 and axon degeneration.

Strengths:

(1) The use of two independent DR6 knockout mouse models strengthens the conclusions, particularly when reporting the absence of a phenotype.

(2) The focus on early time points after injury addresses a key limitation of previous studies. This approach reduces the risk of missing subtle protective phenotypes and avoids confounding results with regenerating axons at later time points after axotomy.

Comments on revisions:

I thank the authors for their thorough responses to my previous comments. The revisions have addressed the points raised and have improved the clarity and overall quality of the manuscript. I appreciate the effort taken to strengthen the presentation of the work.

Reviewer #1 (Public review):

Summary:

In this study, the authors investigate the physiological role of the Type VI secretion system (T6SS) in a naturally evolved gut microbiome derived from wild mice (the WildR microbiome). Focusing on Bacteroides acidifaciens, the authors use newly developed genetic tools and strain-replacement strategies to test how T6SS-mediated antagonism influences colonization, persistence, and fitness within a complex gut community. They further show that the T6SS resides on an integrative and conjugative element (ICE), is distributed among select community members, and can be horizontally transferred, with context-dependent effects on colonization and persistence. The authors conclude that the T6SS stabilizes strain presence in the gut microbiome while imposing ecological and physiological constraints that shape its value across contexts.

This study is likely to have a significant impact on the microbiome field by moving experimental tests of T6SS function out of simplified systems and into a naturally co-evolved gut community. The WildR system, together with the strain replacement strategy, ICE-seq approach, and genetic toolkit, represents a powerful and reusable platform for future mechanistic studies of microbial antagonism and mobile genetic elements in vivo.

The datasets, including isolate genomes, metagenomes, and ICE distribution maps, will be a valuable community resource, particularly for researchers interested in strain-resolved dynamics, horizontal gene transfer, and ecological context dependence. Even where mechanistic resolution is incomplete, the work provides a strong experimental foundation upon which such questions can be directly addressed.

Overall, this study occupies a space between system building and mechanistic dissection. The authors demonstrate that the T6SS influences persistence and community structure in vivo, but the physiological basis of these effects remains unresolved. Interpreting the results as evidence of fitness costs or selective advantage, therefore, requires caution, as multiple ecological and host-mediated processes could produce similar abundance trajectories.

Placing the findings within the broader literature on microbial antagonism, particularly work emphasizing measurable costs, benefits, and tradeoffs, would help readers better contextualize what is directly demonstrated here versus what remains an open question. Viewed in this light, the principal contribution of the study is to show that such questions can now be addressed experimentally in a realistic gut ecosystem.

Strengths:

A major strength of this study is that it directly interrogates the physiological role of the T6SS in a naturally evolved gut microbiome, rather than relying on simplified pairwise or in vitro systems. By working within the WildR community, the authors advance beyond descriptive surveys of T6SS prevalence and address function in an ecologically relevant context.

The authors provide clear genetic evidence that Bacteroides acidifaciens uses a T6SS to antagonize co-resident Bacteroidales, and that loss of T6SS function specifically compromises long-term persistence without affecting initial colonization. This temporal separation is well designed and supports the conclusion that the T6SS contributes to maintenance rather than establishment within the community.

Another strength is the identification of the T6SS on an integrative and conjugative element (ICE) and the demonstration that this element is distributed among, and exchanged between, community members. The use of ICE-seq to track distribution and transfer provides strong support for horizontal mobility and adds mechanistic depth to the study.

Finally, the transfer of the T6SS-ICE into Phocaeicola vulgatus and the observation of context-dependent colonization benefits followed by decline is a compelling result that moves the study beyond simple "T6SS is beneficial" narratives and highlights ecological contingency.

Weaknesses:

Despite these strengths, there is a mismatch between the precision of the claims and the precision of the measurements, particularly regarding fitness costs, physiological burden, and the mechanistic role of the T6SS.

First, while the authors conclude that the T6SS "stabilizes strain presence" and that its value is constrained by fitness costs, these costs are not directly measured. Persistence, abundance trajectories, and eventual loss are informative outcomes, but they do not uniquely identify fitness tradeoffs. Decline could arise from multiple non-exclusive mechanisms, including community restructuring, host-mediated effects, incompatibilities of the ICE in new hosts, or ecological retaliation, none of which are disentangled here.

Second, the manuscript frames the T6SS as having a defined physiological role, yet the data do not resolve which physiological processes are under selection. The experiments demonstrate that T6SS activity affects persistence, but they do not distinguish whether this occurs via direct killing, resource release, niche modification, or higher-order community effects. As a result, "physiological role" remains underspecified and risks being conflated with ecological outcome.

Third, although the authors emphasize context dependence, the study offers limited quantitative insight into what aspects of context matter. Differences between native and recipient hosts, or between early and late colonization phases, are described but not mechanistically interrogated, making it difficult to generalize beyond the specific cases examined.

Fourth is the lack of engagement with recent experimental literature demonstrating functional roles of the T6SS beyond simple interference competition. While the authors focus on persistence and competitive outcomes, they do not adequately situate their findings within recent work demonstrating that T6SS-mediated antagonism can serve additional physiological functions, including resource acquisition and DNA uptake, thereby linking killing to measurable benefits and tradeoffs. The absence of this literature makes it difficult to place the authors' conclusions about physiological role and fitness cost within the current conceptual framework of the field. Without this context, the physiological interpretation of the results remains incomplete, and alternative functional explanations for the observed dynamics are underexplored.

A further limitation concerns the taxonomic scope of the functional analysis. The authors state that the role of the T6SS in the murine environment is functionally investigated using genetically tractable Bacteroides species, citing the lack of genetic tools for Mucispirillum schaedleri. While this is a reasonable, practical choice, it means that a substantial fraction of T6SS-encoding species in the WildR community are not experimentally interrogated. Consequently, conclusions about the role of the T6SS in the murine gut necessarily reflect the subset of taxa that are genetically accessible and may not fully capture community-level or niche-specific functions of T6SS activity. Given that M. schaedleri is represented as a metagenome-assembled genome, its isolation and genetic manipulation would be technically challenging. Nonetheless, explicitly acknowledging this limitation and slightly tempering claims of generality would strengthen the manuscript.

Finally, several interpretations would benefit from more cautious language. In particular, claims invoking fitness costs, selective advantage, or physiological burden should be explicitly framed as inferences from persistence dynamics, rather than as direct measurements, unless supported by additional quantitative fitness or growth assays.

Reviewer #2 (Public review):

Summary:

In this study, the authors set out to determine how a contact-dependent bacterial antagonistic system contributes to the ability of specific bacterial strains to persist within a complex, native gut community derived from wild animals. Rather than focusing on simplified or artificial models, the authors aimed to examine this system in a biologically realistic setting that captures the ecological complexity of the gut environment. To achieve this, they combined controlled laboratory experiments with animal colonization studies and sequencing-based tracking approaches that allow individual strains and mobile genetic elements to be followed over time.

Strengths:

A major strength of the work is the integration of multiple complementary approaches to address the same biological question. The use of defined but complex communities, together with in vivo experiments, provides a strong ecological context for interpreting the results. The data consistently show that the antagonistic system is not required for initial establishment but plays a critical role in long-term strain persistence. This insight that moves beyond traditional invasion-based views of microbial competition. The observation that transferable genetic elements can confer only temporary advantages, and may impose longer-term costs depending on community context, adds important nuance to current understanding of microbial fitness.

Weaknesses:

Overall, there is not a lack of evidence, but a deliberate trade-off between ecological realism and mechanistic resolution, which leaves some causal pathways open to interpretation.

Reviewer #3 (Public review):

Summary:

Shen et al. investigate the contribution of the type VI secretion system of Bacteroidales in the gut microbiome assembly and targeting of closely related species. They demonstrate that B. acidifaciens relies on T6SS-mediated antagonism to prevent displacement by co-resident Bacteroidales and other members of the microbiome, allowing B. acidifaciens to persist in the gut.

Strengths:

Using a gnotobiotic model colonized with a wild-mouse microbiome is a significant strength of this study. This approach allows tracking of microbiome changes over time and directly examining targeting by Bacteroidales carrying T6SS in a more natural setting. The development of ICE-seq for mapping the distribution of the T6SS in the microbiome is remarkable, enabling the study of how this bacterial weapon is transferred between microbiome members without requiring long-read metagenomics methods.

Weaknesses:

Some conclusions are based on only four mice per condition. The author should consider increasing the sample size.

Overall, the authors successfully achieved their objectives, and their experimental design and results support their findings. As mentioned in the discussion, it would be important to investigate the role of the T6SS in resilience to disturbances in the microbiome, such as antibiotics, diet, or pathogen invasion. This work represents a step forward in understanding how contact-dependent competition influences the gut microbiome in relevant ecological contexts.

Reviewer #1 (Public review):

Summary:

The authors aim to determine whether TENT5A, a post-transcriptional regulator previously implicated in bone formation, also plays a role in enamel development. Using a mouse model lacking TENT5A, they report hypomineralized enamel with structural defects, accompanied by reduced expression, altered poly(A) tail length, and impaired secretion of enamel matrix proteins, particularly amelogenin. By combining ultrastructural imaging, transcriptomics, direct RNA sequencing, and protein localization analyses, the study proposes that TENT5A promotes cytoplasmic polyadenylation and translation of a subset of extracellular matrix transcripts required for enamel biomineralization.

Strengths:

A major strength of this work is its conceptual novelty. To my knowledge, this is the first study to demonstrate that a non-canonical poly(A) polymerase plays a direct role in enamel development, extending post-transcriptional regulation by cytoplasmic polyadenylation from bone to enamel, a biologically distinct and non-regenerative mineralized tissue. The identification of amelogenin as a dominant, tissue-specific target provides a new perspective on how enamel matrix production is regulated beyond transcriptional control.

In addition, the study is supported by a comprehensive and complementary set of approaches linking molecular changes to tissue-level phenotypes. The use of direct RNA sequencing provides strong evidence for selective regulation of poly(A) tail length in specific transcripts rather than global effects on mRNA metabolism, and the phenotypic analyses convincingly connect altered post-transcriptional regulation to defects in enamel structure and mineralization.

Weaknesses:

Although the data support a role for TENT5A in stabilizing and promoting translation of amelogenin and related transcripts, the mechanism underlying substrate specificity remains unresolved. Poly(A) tail length alone does not explain why certain transcripts are regulated while others are not, and the proposed involvement of protein partners or RNA processing steps remains speculative. This limitation should be more clearly framed as an open question rather than an emerging mechanism.

A further limitation is the lack of direct human genetic or clinical evidence linking TENT5A to enamel defects. In humans, loss-of-function variants in TENT5A are known to cause a recessive form of osteogenesis imperfecta, but TENT5A has not been associated with amelogenesis imperfecta or other enamel phenotypes. This limits immediate translational interpretation of the mouse enamel phenotype and highlights the need for future human genetic or clinical studies.

Finally, the manuscript does not address whether other members of the TENT5 family are expressed in ameloblasts or could compensate for the loss of TENT5A, leaving open questions about redundancy and specificity within this family.

Reviewer #2 (Public review):

Summary:

The manuscript by Aranaz-Novaliches describes a study of Tent5a knockout (KO) mice. The authors demonstrate a severe enamel phenotype in these mice, characterized by hypoplastic enamel with markedly disturbed organization of enamel rods. Additionally, they report that Amelx expression is reduced in the mutant compared to wild type (WT) at both mRNA and protein levels. The authors also examine the distribution and co-localization of Amelx and Ambn in ameloblasts and the enamel matrix. These findings are novel and provide important insights into the role of polyadenylation in regulating enamel matrix protein translation and its downstream effects on protein trafficking, secretion, and enamel formation. However, I have multiple concerns regarding the data and its analysis that need to be addressed.

Specific comments:

(1) Introduction

The structure of the introduction is unconventional. The first sentence of the third paragraph states that the goal of this study is to investigate the role of TENT5A in enamel formation, but the rest of the paragraph focuses on enamel in general. The following paragraph claims that the authors discovered the effects of Tent5a deficiency on enamel formation for the first time, yet most of the paragraph discusses enamel proteins and amelogenesis. The choice of references is problematic. The authors cite Sire et al. (2007), which focuses on the origin and evolution of enamel mineralisation genes, a poor fit for this context. A more appropriate source would be a recent review, e.g., Lacruz R et al., Physiol Rev. 2017;97(3):939-993. Ambn constitutes ~5% of the enamel matrix, not 10%. Reference 16 (Martin) is not ideal for murine enamel; more detailed studies exist, e.g., Smith CE et al., J Anat. 2019;234(2):274-290. References on protein-protein interactions (17-19) are also off: Wald et al. studied Ambn-Ambn and Amelx-Amelx interactions separately; Fang et al. focused on Amelx self-assembly only; Kawasaki and Weiss addressed gene evolution. The authors should cite work from Moradian-Oldak's lab, which clearly demonstrates Amelx-Ambn interactions. The last paragraph contains confusing statements, e.g., "TENT5a localized in rER promotes the expression of AmelX and other secreted protein transcripts." Also, the manuscript does not convincingly show disruption of self-assembly beyond overall enamel disorganization.

(2) Results

(a) microCT

Quantitative microCT analyses of WT and KO enamel are needed. At a minimum, enamel thickness and density should be measured from at least three biological replicates per genotype. Severe malocclusion in KO mice is not discussed. The mandibular incisor appears abraded, while the maxillary incisor is overgrown. Is maxillary enamel as affected as mandibular? The age of the mice is not specified. High-resolution scans of isolated mandibular incisors described in Materials and Methods should be included.

(b) SEM

The term "disorganized crystal structure" is incorrect - SEM cannot reveal crystal structure. This requires electron/X-ray diffraction or vibrational spectroscopy. Likely, the authors meant disorganized rods and interrod enamel. The phrase "weak HAP composition" is unclear. Can the increase in interprismatic matrix volume and reduction in rod diameter be quantified? Since rods are secreted by distal Tomes' processes and interrod by proximal Tomes' processes, an imbalance may indicate alterations in the ameloblast secretory apparatus. TEM studies of demineralized incisors are recommended to assess ameloblast ultrastructure.

(c) EMP expression

There is a discrepancy between WB images and data in Figure S2a. In Figure 2b, Amelx band is stronger than Ambn (expected, as Amelx is ~20× more abundant), but in Figure S2a, Ambn appears higher. How was protein intensity in Fig. S2a calculated? Optical density? Was normalization applied? Co-localization in Figure 2d was performed on LS8 cells, which lack a true ameloblast phenotype. Amelx expression in LS8 cells is ~2% of actin (Sarkar et al., 2014), whereas in murine incisors, it is ~600× higher than actin (Bui et al., 2023). Ambn signal is weaker than Amelx, which may affect co-localization results.

(d) Splicing products in Figure 2e

All isoforms except one contain exon 4. The major functional splice product of Amelx lacks exon 4 (Haruyama et al. J Oral Biosci. 2011;53(3):257-266), and there are some indications that the presence of exon 4 can lead to enamel defects. Can it be that the observed phenotype is due to the presence of exon 4?

(e) Co-localization studies

The presented co-localization studies do not demonstrate self-assembly defects; they reflect enamel microstructural defects observed by SEM. Self-assembly occurs at the nanoscale and cannot be assessed by light microscopy except with advanced optical methods. Conclusions based on single images are weak. The authors should perform experiments at least on three biological replicates per genotype, quantify results (e.g., total gray values per ROI of equal pixel size), and use co-localization metrics such as Mander's coefficient. Claims about alternative secretory pathways require much stronger evidence.

The authors should avoid implying that mRNA is inside the ER lumen. It is likely associated with the outer rER surface, which is expected. The resolution of the methods used is insufficient to confirm ER lumen localization.

Reviewer #3 (Public review):

Summary:

It is well established that poly(A) tails at the 3' end of mRNA are critical for mRNA stability, providing another layer of gene regulation. TENT5A is one of the non-canonical poly(A) polymerases that add an extra poly(A) tail. This manuscript demonstrates that the Tent5A mutation leads to mineralization abnormalities in the tooth, shorter poly(A) tails in amelogenin mRNA and some other selected mRNAs, and provides a list of TENT5A interacting proteins.

Strengths:

(1) The authors show in vivo genetic evidence that Tent5a is critical for normal tooth mineralization.

(2) The authors show that the length of the poly(A) tail in amelogenin (AmelX) is 13 bases shorter in Tent5a mutants but not in other mRNAs, such as ameloblastin (Ambn).

(3) Differentially expressed genes (DEGs) in Tent5A mutant tissues (cervical loop) are identified, and some of them show different lengths of poly(A) tails.

(4) TENT5A interacting proteins are identified. Together with the DEGs, these datasets will provide valuable research tools to the community.

Weaknesses:

(1) There is no direct evidence to support the main conclusion; the length of the poly(A) tail is critical for normal tooth mineralization.

(2) The RNAseq data to identify TENT5A substrate is based on the assumption that shorter poly(A) tailed RNA is less stable. However, there are multiple reasons for the differential expression of RNA in Tent5A mutant tissues.

(3) Several TENT5A-interacting proteins have been identified, but, beyond their colocalization with a target mRNA, no mechanistic studies have been conducted.

Reviewer #1 (Public review):

Summary:

This manuscript describes a multi-modal study of associative learning and memory in humans that combines scalp EEG, pupillometry and behavioral analysis to explore the construct of mnemonic prediction errors (MPEs), in terms of their relationship to attention and cognitive control. Across two pooled studies, participants performed associative memory tasks in which they learned the relationship between a cue word (action verb) and a subsequent picture (animate or inanimate) with a strong vs. weak (4 or 1 repetitions) encoding manipulation. At test, participants were encouraged to generate a prediction following the cue word to determine whether the subsequently presented picture was a match or a mismatch. The timecourse of pupillary responses during match decisions was decomposed using temporal principal components analysis, which identified 6 distinct and overlapping processes. Some of the components (PC3/PC4) exhibited sensitivity to both the strength and mismatch conditions, as well as behavior (both RT and accuracy) and retrieval success on the subsequent trial. Furthermore, relationships were also observed between pupillary responses (specifically for PC4) and both frontal theta and posterior alpha power measures obtained from scalp EEG in Experiment 2, as well as for frontal theta and subsequent learning from mismatch stimuli (assessed using subsequent memory findings from a surprise recognition test). The authors suggest the findings indicate that MPEs elicit changes in attention, arousal and cognitive control which impact subsequent learning.

Strengths:

This manuscript has many strengths, including a clever study design, thoughtful integration of multiple neurocognitive measures, and a set of rigorous and technically sophisticated analyses, which reveal a large set of relationships among the measures and behavior. The findings demonstrating brain/physiology-behavior relationships are particularly important, in that they point to potential functional consequences of MPES.

Weaknesses:

The technical proficiency and complexity of the study and analysis also present a clear limitation and challenge for interpretation. As a reader, even those who are quite knowledgeable about the methods, constructs, and questions being addressed will often struggle (as this reviewer did) to keep the large set of findings in mind and gain an understanding of how they all fit together.

Indeed, it seems like there are many threads running together in the paper, which makes it challenging to find the through-line of the key findings, or to understand how they might relate to some pre-existing hypotheses, rather than merely interesting patterns detected in the data. In the Introduction and Discussion, it seems as if the key question is to understand the pathways by which MPEs impact cognition, but this is a rather broad topic, so it is not clear exactly what the authors are aiming at with this question and study design.

As an example, authors operationalize frontal theta power as an index of cognitive control demand, and one of the pathways by which MPEs impact cognition. But this point becomes somewhat circular, since it is not clear how or why the Mismatch x Strength interaction in frontal theta reflects that demand. It would have been better to set this pattern up in the Introduction as a theoretically driven hypothesis, since it currently appears more like a post-hoc interpretation. This is mirrored by how the issue is first brought up in the Introduction, where it states somewhat vaguely: "whether MPEs are followed by an increase in frontal theta... warrants closer examination". Later in the results, there are findings relating frontal theta to pupil dilation, posterior alpha suppression and then subsequent memory. It was hard to understand how all the findings might be linked together functionally or conceptually. Are the authors potentially postulating a mediating or mechanistic pathway, in which the MPE leads to increased cognitive control (frontal theta), which then leads to enhanced subsequent memory of those events? If this is the case, then maybe a formal path analysis would be the best way to test or state this hypothesis. It would also be useful to specify more clearly how the pupil components and alpha suppression factor into this mediating path, since it was not clear.

Relatedly, the authors suggest that internal attention and arousal also play relevant roles in this pathway, but these are also not clear. In some cases, it is stated as if this is a distinct pathway from the cognitive control one, since there is a focus in the results on the independence of frontal theta and posterior alpha, but elsewhere they seem to be treated as two aspects, or distinct steps, within a single pathway. Again, these different threads of the findings were quite challenging for the reader to follow. Pathway analyses, such as with multiple mediation or moderated mediation, could be a useful way to address this question. For example, it seems as if readiness-to-remember is another behavioral outcome (like subsequent memory) that could be used in the search for mediators.

At the minimum, it would be quite helpful to have diagrammatic figures that specify the hypothesized and observed relationships between independent variables (Strength, Mismatch), physiological indices (pupil dilation components, frontal theta, posterior alpha) and key outcome measures (accuracy, RT, next-trial retrieval success, subsequent memory), so that the reader can refer back to them as each component of the analyses is conducted.

Minor Points:

Many figures had x-axes showing a pupil component or EEG power metric broken down by quartile or quintile. Yet nowhere is it ever explained why this graphical (or analytic?) approach is used and what it reflects, or how it is decided which break down to use (quartile/quintile). If the data are analyzed as a correlation, why is a scatterplot not shown instead?

It was surprising that, unlike readiness-to-remember, which was analyzed via logistic regression and odds-ratio, subsequent memory was not analyzed in the same fashion (i.e., as a binary outcome variable predicted by frontal theta), rather than in a reverse chronological one (subsequent memory predicting frontal theta). Historically, it was the case that subsequent memory was analyzed in this manner, but that was before the era in which trial-level linear mixed-effect models were in wide usage, as they are implemented in this study. Thus, the choice seems like a wasted opportunity or a step backwards analytically.

Reviewer #2 (Public review):

Summary:

The authors studied cognitive control and attention in response to mnemonic prediction errors (MPEs): situations in which the external reality violates internal memory-based predictions. The behavioral task first established strong versus weak predictions, and then either confirmed or violated these predictions. The authors examined markers of cognitive control (frontal theta) and attention (posterior alpha suppression, pupil response) while strong and weak predictions were confirmed or violated. They found increased cognitive control (frontal theta) for strong MPEs, which correlated with subsequent memory. Markers of attention (alpha suppression, pupil response) also accompanied strong MPEs but did not correlate with subsequent memory. Pupil response was investigated using an interesting approach that decomposes the response into different components, finding that different components respond earlier or later and show different correlations with MPEs and their strength. The authors also investigated how EEG, reaction time, and pupil responses correlated with one another, providing further insight into the mechanism underlying the response to MPEs. Together, the study points toward multiple control and attention mechanisms involved in MPE response and memory.

Strengths:

The study has a clear behavioral paradigm with multiple measures - behavioral, EEG, and pupillometry that offer an investigation into different aspects of MPE response and memory.

The study is also very comprehensive in looking at multiple phases in processing MPEs: the prediction phase (prior to the violation), the response to MPEs, and subsequent memory of MPEs, all within one study. Specifically, the link between neural mechanisms and subsequent memory is a major advancement, as most prior studies did not include this component. Mechanisms underlying subsequent memory of MPEs are theoretically important, as a primary function of MPEs is to promote learning and memory. As the authors mention, the different neural and pupillary signals are not robustly correlated, suggesting multiple mechanisms underlying MPE detections, which is interesting, offers avenues for future research, and can facilitate a better theory of how MPEs are processed in the brain. Finally, the decomposition of pupil response into different components and their correlation with behavior (RT during match/MPE detection) is interesting.

Weaknesses:

The methods are rigorous, and the claims are mostly supported by the data, but there are a few weaknesses or places that could be improved:

(1) The authors conduct PCA analysis to identify different components of the pupillary response to MPE and relate them to behavior. Specifically, the authors identify components PC3 and PC4, which they interpret as related to MPE. However, some parts of the interpretation could be clearer or better justified:

(a) The authors refer to PC4 as "post-decision cognitive processing". But, given that RT was between .5-.7s, and PC3 peaked after more than 1s, wouldn't it be cautious to interpret PC3 as post-decision as well?

(b) MPEs overall elicit longer RTs in this study, suggesting that long RT is a behavioral marker of MPE. Nonetheless, the authors argue on p. 12: "Altogether, these findings indicate that when stronger mnemonic predictions (as indexed by shorter RTs) were violated." And, PC3 is correlated with shorter RTs for mismatches, meaning that behaviorally, these trials were more similar to matches. Thus, how do the authors interpret shorter versus longer RTs for MPEs, and what processes do these RT reflect?

(2) The brain to pupil relationship (p. 13-14): If I understand correctly, this was done on a trial-by-trial basis, but the high temporal resolution allows doing the analysis in a time-resolved manner - does brain activity at a certain time point preceding/following the pupil response correlate with the pupil response? It might be that cognitive control influences attention mechanisms or vice versa (because there is some overlap in the response). Although not testing causality, this temporally resolved correlation would be an interesting way to start probing how signals might influence each other.

(3) The relationships the authors find between brain measures and pupil components were largely not specific to mismatches/matches. However, are they specific to this task? I think it would benefit the paper to show that these relationships are potentially specific to making match/mismatch memory decisions, versus, e.g., any stimulus processing. For example, the authors could run the same analyses locked to stimuli in the study phase, anticipating a different pattern, if indeed these findings are specific to the associative memory task.

(4) During memory retrieval (i.e., before the probe), the authors find that frontal theta, a marker of cognitive control, was associated on a trial-by-trial basis with more posterior alpha (i.e., less alpha suppression, potentially reflecting less attention), and that this association was stronger for weaker predictions. The authors interpreted this as weaker predictions necessitating more cognitive control, and that more cognitive control was recruited specifically in trials where retrieval included less content (memory reinstatement) to attend to. Generally, cognitive control is recruited to facilitate memory retrieval. If so, one possible interpretation is that this correlation reflects cognitive control effort that has failed to produce enough memory reinstatement. The other possibility is that this correlation reflects more specific retrieval of the correct probe, without retrieval of interfering items (i.e., overall less content). I believe that the former explanation predicts that this correlation would be associated with longer RTs (more difficult decisions), while the latter predicts shorter RTs (easier decisions due to successful retrieval), at least for matches.

(5) In section 3, the authors found a positive relationship between alpha during memory retrieval and PC3 during MPE. If I understood correctly, this means that less attention during retrieval (less suppression) is correlated with a stronger PC3 response. How do the authors interpret this? Maybe along the same lines as in (5), specifically retrieving the correct information (i.e., less retrieved content to attend to) means a stronger prediction, leading to a stronger MPE, and a stronger MPE response, as reflected by PC3?

(6) The results with subsequent memory are important and address a major gap in the field that largely did not relate neural effects of MPE to subsequent memory. However, one major limitation of the study is that the authors did not test memory for matches. I understand the logic of avoiding testing matches. Because matches were repeated more times in the study, it's not a fair comparison, and could change participants' overall criterion for old/new decisions. However, one possibility would have been to test only the weak prediction; this could have given some specificity to the neural subsequent memory findings.

(7) The authors nicely characterized the different PC of pupillary MPE response. But, with respect to subsequent memory, they only present pupil size. Unless there is some methodological reason that prevents testing subsequent memory on the PC, I think this will be very informative about the potential mechanisms underlying memory of MPE.

(8) This paper includes many interesting findings, and I am not sure how they all come together into a cohesive mechanistic understanding of MPE response and subsequent memory. I think the paper would benefit from either a conceptual mechanism figure or, in the Discussion, have a summary of a proposed mechanism integrating the findings together.

(9) Relatedly, the section "Immediate, strength-sensitive neurocognitive impacts of MPEs" does not link the arguments to specific data points, so it's hard to follow which data specifically the authors are interpreting.

(10) If I understand correctly, the authors did not find improved memory for strong compared to weak MPE. First, I think this behavioral result should be incorporated in the main paper and in the interpretation of the results. Second, given that the neural effects the authors tested either correlated with memory for strong MPE or did not show a relationship with memory, what neural/pupil response could explain memory for weak MPE?

Reviewer #1 (Public review):

Summary:

This computational modelling study addresses the important question of how neurons can learn non-linear functions using biologically realistic plasticity mechanisms. The study extends the previous related work on metaplasticity by Khodadadi et al. (2025), using the same detailed biophysical model and basic study design, while significantly simplifying the synaptic plasticity rule by removing non-linearities, reducing the number of free parameters, and limiting plasticity to only excitatory synapses. The rule itself is supervised by the presence or absence of a binary dopamine reward signal, and gated by separate calcium-sensitive thresholds for potentiation and depression. The author shows that, when paired with a strong form of dendritic non-linearity called a "plateau potential" and appropriate pre-existing dendritic clustering of features, this simpler learning mechanism can solve a non-linear classification task similar to the classic XOR logic operator, with equal or better performance than the previous publication. The primary claims of this publication are that metaplasticity is required for learning non-linear feature classification, and that simultaneous dynamics in two separate thresholds (for potentiation and depression) are critical in this process. By systematically studying the properties of a biophysically plausible supervised learning rule, this paper adds interesting insights into the mechanics of learning complex computations in single neurons.

Strengths:

The simplified form of the learning rule makes it easier to understand and study than previous metaplasticity rules, and makes the conclusions more generalizable, while preserving biological realism. Since similar biophysical mechanisms and dynamics exist in many different cell types across the whole brain, the proposed rule could easily be integrated into a wide range of computational models specializing in brain regions beyond the striatum (which is the focus of this study), making it of broad interest to computational neuroscientists. The general approach of systematically fixing or modifying each variable while observing the effects and interactions with other variables is sound and brings great clarity to understanding the dynamic properties and mechanics of the proposed learning rule.

Weaknesses:

General notes

(1) The credibility of the main claims is mainly limited by the very narrow range of model parameters that was explored, including several seemingly arbitrary choices that were not adequately justified or explored.

(2) The choice to use a morphologically detailed biophysical model, rather than a simpler multi-compartment model, adds a great deal of complexity that further increases uncertainty as to whether the conclusions can generalize beyond the specific choices of model and morphology studied in this paper.

(3) The requirement for pre-existing synaptic clustering, while not implausible, greatly limits the flexibility of this rule to solve non-linear problems more generally.

(4) In order to claim that two thresholds are truly necessary, the author would have to show that other well-known rules with a single threshold (e.g., BCM) cannot solve this problem. No such direct head-to-head comparisons are made, raising the question of whether the same task could be achieved without having two separate plasticity thresholds.

Specific notes

(1) Regarding the limited hyperparameter search:

(a) On page 5, the author introduces the upper LTP threshold Theta_LTP. It is not clear why this upper threshold is necessary when the weights are already bounded by w_max. Since w_max is just another hyperparameter, why not set it to a lower value if the goal is to avoid excessively strong synapses? The values of w_max and Theta_LTP appear to have been chosen arbitrarily, but this question could be resolved by doing a proper hyperparameter search over w_max in the absence of an upper Theta_LTP.

(b) The author does not explore the effect of having separate learning rates for theta_LTP and theta_LTD, which could also improve learning performance in the NFBP. A more comprehensive exploration of these parameters would make the inclusion of theta_max (and the specific value chosen) a lot less arbitrary.

(c) Figure 4 Supplements 3-4: The author shows results for a hyperparameter search of the learning rule parameters, which is important to see. However, the parameter search is very limited: only 3 parameter values were tried, and there is no explanation or rationale for choosing these specific parameters. In particular, the metaplasticity learning rates do not even span one order of magnitude. If the author wants to claim that the learning rule is insensitive to this parameter, it should be explored over a much broader range of values (e.g., something like the range [0.1-10]).

(2) Regarding the similarity to BCM, the author would ideally directly implement the BCM learning rule in their model, but at the least the author could have shown whether a slight variant of their rule presented here can be effective: for example having a single (plastic, not fixed) Ca-dependent threshold that applies to both LTP and LTD, with a single learning rate parameter.

(3) This paper is extremely similar (and essentially an extension) to the work of Khodadadi et al. (2025). Yet this paper is not mentioned at all in the introduction, and the relation between these papers is not made clear until the discussion, leaving me initially puzzled as to what problems this paper addresses that have not already been extensively solved. The introduction could be reworked to make this connection clearer while pointing out the main differences in approach (e.g., the important distinction between "boosting" nonlinearities and plateau potentials).

(4) The introduction is missing some citations of other recent work that has addressed single-neuron non-linear computation and learning, such as Gidon et al (2020); Jones & Kording (2021).

(5) Figure 1: The figure prominently features mGluR next to the CaV channel, but there is no mention of mGluR in the introduction. The introduction should be updated to include this.

(6) Could the author explain why there is a non-monotonic increase/decrease in the [Ca]_L in Figure 2B_4? Perhaps my confusion comes from not understanding what a single line represents. Does each line represent the [Ca] in a single spine (and if so, which spine), or is each line an average of all the spines in a given stim condition?

(7) Row 124 (page 4): L-type Ca microdomains (in which ions don't diffuse and therefore don't interact with Ca_NMDA) is a critical assumption of this model. The references for this appear only in the discussion, so when reading this paper, I found myself a bit confused about why the same ion is treated as two completely independent variables with separate dynamics. Highlighting the assumption (with citations) a bit more clearly in the results section when describing the rule would help with understanding.

(8) Row 149 (page 5): The current formulation of the update rule is not actually multiplicative. The fact that the update is weight-dependent alone does not make it a multiplicative rule, and judging by equation (1) it appears to simply be an additive rule with a weight regularization term that guarantees weight bounds. For example, a similar weight-dependent update is also a core component of BTSP (Milstein et al. 2021; Galloni et al. 2025), which is another well-known *additive* rule. An actual multiplicative rule implies that the update itself is applied via a multiplication, i.e. w_new = w_old * delta_w

For an example of a genuinely multiplicative rule, see: Cornford et al. 2024, "Brain-like learning with exponentiated gradients"). Multiplicative rules have very different properties to additive rules, since larger weights tend to grow quickly while small weights shrink towards 0.

(9) Equation 1 (page 5): Shouldn't the depression term be written as: (w_min - w)? This term would be negative if w is larger than w_min, leading to LTD. As it is written now, a large w and small w_min would just cause further potentiation instead of depression.

(10) In the introduction, the teaching signal is described in binary terms (DA peak, or DA pause), but in Equation 1, it actually appears to take on 3 different values. Could the author clarify what the difference is between a "DA pause" and the "no DA" condition? The way I read it, pause = absence of DA = no DA

(11) Figure 3: In these experimental simulations, DA feedback comes in 400ms after the stimulus. The author could motivate this choice a bit better and explain the significance of this delay. Clearly, the equations have a delta_t term, but as far as the learning algorithm is concerned, it seems like learning would be more effective at delta_t=0. Is the choice of 400ms mainly motivated by experimental observations? On a related note, is it meaningful that the 200ms delta_t before the next stimulus is shorter than the 400ms pause from the first stimulus? Wouldn't the DA that arrives shortly before a stimulus also have an effect on the learning rule?

(12) Figure 4C: How is it possible that the theta_LTP value goes higher than the upper threshold (dashed line)? Equation 3 implies that it should always be lower.

(13) Row 429 (page 11): The statement that "without metaplasticity the NFBP cannot be solved" is overly general and not supported by the evidence presented. There exist many papers in which people solve similar non-linear feature learning problems with Hebbian or other bio-plausible rules that don't have metaplasticity. A more accurate statement that can be made here is that the specific rule presented in this paper requires metaplasticity.

(14) The methods section does not make any mention of publicly available code or a GitHub repository. The author should add a link to the code and put some effort into improving the documentation so that others can more easily assess the code and reproduce the simulations.

Reviewer #2 (Public review):

Summary:

The manuscript proposes interesting synaptic plasticity rules grounded in experimental data. Its main features are:

(1) plasticity depends on local calcium concentration driven by presynaptic activity and is independent of somatic action potentials,

(2) the rules incorporate metaplasticity, and (3) they demonstrate how a single neuron could address the feature-binding problem at the dendritic level.

The work extends a previous study (https://doi.org/10.7554/eLife.97274.2), to which the author also contributed.

The author models two calcium thresholds (LTP/LTD) from two different calcium sources (NMDA/VGCC), and these thresholds are flexible (metaplasticity rule, similar to BCM), which is claimed to be necessary for successful learning of both FBP and NFBP (linear and nonlinear feature binding problem with 1 or 2 patterns). The role of each threshold seems to be opposite and complementary. One extra condition has been added: an upper threshold for LTP. This threshold serves to stop synaptic strengthening once synapses are strong enough to evoke a plateau. With that, synapses are not strengthened to the maximal value, avoiding strong supralinear integration for irrelevant patterns.

Strengths:

The current model implements not only local synaptic plasticity but also metaplasticity and solves the FBP at the dendrite level. Another strong aspect of the model is that metaplasticity in the LTD threshold protects strengthened synapses from weakening. In this way, as the author mentioned, metaplasticity is able to protect learned patterns from being forgotten or weakened and prevent irrelevant patterns from being stored. This is a nice modelling example of metaplasticity being helpful in preventing the catastrophic interference or forgetting (as has been explicitly discussed in a recent article https://doi.org/10.1016/j.tins.2022.06.002 ). The author might want to briefly mention or emphasize this aspect of the model, which might be interesting also for the AI community.

Weaknesses:

(1) What is novel in the current paper as compared to Khodadadi et al. eLife 2025? That is not completely clear and should be made clearer. Is it only a minor difference related to the fact that the new learning rule has metaplasticity in both calcium thresholds and is simpler? This seems to be just an incremental increase in knowledge/methods. Can the author defend his paper against this point from the „devil's advocate"? How is the conclusion of the author in the abstract that „metaplasticity in both thresholds is necessary" reconcilable with his previous publication (Khodadadi et al. eLife 2025), in which only metaplasticity in one threshold was successful in solving the nonlinear feature binding problem?

(2) As far as I can judge without testing the model, metaplasticity causes thresholds to monotonically increase during systematic pattern presentation, which stabilizes weights and allows pattern separation. Due to the closed-loop nature of the current implementation, where metaplasticity only happens if plasticity happens, this also effectively locks patterns in place. However, flexible learning is an essential mechanism for survival. Imagine a mutation event takes place and bananas suddenly become red and/or strawberries turn yellow. It seems that the current model would be unable to adapt to these new patterns even if rewards were to be shifted. While out of the scope of the study, due to its importance, I feel that pattern shifting/relearning should at least be briefly discussed. How could the model be improved to allow relearning?

Reviewer #1 (Public review):

The manuscript entitled "Blocking SHP2 1 benefits FGFR2 inhibitor and overcomes its resistance in 2 FGFR2-amplified gastric cancer" by Zhang, et al., reports that FGFR2 was amplification in 6.2% (10/161) of gastric cancer samples and that dual blocking SHP2 and FGFR2 enhanced the effects of FGFR2 inhibitor (FGFR2i) in FGFR2-amplified GC both in vitro and in vivo via suppressing RAS/ERK and PI3K/AKT pathways. Furthermore, the authors also showed that SHP2 blockade suppressed PD-1 expression and promoted IFN-γ secretion of CD8+ 46 T cells, enhancing the cytotoxic functions of T cells. Thus, the authors concluded that dual blocking SHP2 and FGFR2 is a compelling strategy for treatment of FGFR2-amplified gastric cancer. Although the finding is interesting, the finding that FGFR2 is amplified in gastric cancer and that FGFR inhibitors have some effect on treating gastric cancer is not novel. The data quality is not high, the effects of double inhibitions are not significant. It appears that the conclusions are largely overstated, the supporting data is weak and not compelling.

The data in Figure 1 is not novel; similar data have been reported elsewhere.

It is unclear why the two panels in fig 2a and 2b can not be integrated into one panel, which will make it easier to compare the activities.

The synergetic effects of azd4547 and shp099 are not significant in Fig 2e and 2f, as well as in Fig. 3g and Fig. 4f

Data in Fig. 5 is weak and can be removed. It is unclear why FGFR inhibitor has some activities toward t cells since t cells do not express FGFR.

Reviewer #2 (Public review):

Summary:

This manuscript reports the application of a combined targeted therapeutic approach to gastric cancer treatment. The RTK, FGFR2 and the phosphatase, SHP2 are targeted with existing drugs; AZD457 and SHP099, respectively. Having shown increased mRNA levels of FGFR2 and SHP2 in a patient population and highlighted the issue of resistance to single therapies the combination of inhibitors is shown to reduce cancer-related signalling in two gastric cell lines. The efficacy of the dual therapy is further demonstrated in a single patient case study and mouse xenograft models. Finally, the rationale for SHP2 inhibition is shown to be linked to immune response.

Strengths:

The data is generally well presented, and the study invokes a novel patient data set which could have wider value. The study provides additional evidence to support the combined therapeutic approach of RTK and phosphatase inhibition.

Weaknesses:

Combined therapy approaches targeting RTKs and SHP2 have been widely reported. Indeed, SHP099 in combination with FGFR inhibitors has been shown to overcome adaptive resistance in FGFR-driven cancers. Furthermore, the inhibition of SHP2 has been documented to have important implications in both targeting proliferative signalling as well as immune response. Thus, it is difficult to see novelty or a significant scientific advance in this manuscript. Although the data is generally well presented, there is inconsistency in the interpretation of the experimental outcomes from ex vivo, patient and mouse systems investigated. In addition, the study provides only minor or circumstantial understanding of the dual mechanism.

Using data from a 161 patient cohort FGFR2 was identified as displaying amplification of FGFR2 in ~6% with concomitant elevation of mRNA of patients which correlated with PTPN11 (SHP2) mRNA expression. The broader context of this data is of value and could add a different patient demographic to other data on gastric cancer. However, there is no detail on patient stratification or prior therapeutic intervention.

Comments on revisions: This has been attended to in the revised version

In SNU16 and KATOIII cells the combined therapy is shown to be effective and appears to be correlated with increase apoptotic effects (i.e. not immune response).

Fig 2E suggests that the combined therapy in SNU16 cells is little better than FGFR2-directed AZD457 inhibitor alone, particularly at the higher dose.

The individual patient case study described via Fig 3 suggests efficacy of the combined therapy (at very high dosage), however the cell biopsies only show reduced phosphorylation of ERK, but not AKT. This is at odds with the ex vivo cell-based assays. Thus, it is not clear how relevant this study is.

The mouse xenograft study shows a convincing reduction in tumor mass/volume and a clear reduction in pAKT, whilst pERK remains largely unaffected by the combined therapeutic approach. This is in conflict with the previous data which seems to show the opposite effect.

Comments on revisions: The authors have clarified this point

In all, the impact of the dual therapy is unclear with respect to the two pathways mediated by ERK and AKT.

Finally, the authors demonstrate the impact of SHP2 on PD-1 expression and propose that the SHP099/AZD4547 combination therapy significantly induces the production of IFN-γ in CD8+ T cells. This part of the study is unconvincing and would benefit from an investigation of the tumor micro-environment to assess T cell infiltration.

Reviewer #3 (Public review):

Summary:

Fibroblast growth factor receptor 2 (FGFR2) is a receptor tyrosine kinase that can be amplified in gastric cancer and serves as a potential therapeutic target for this patient population. However, targeting FGFR2 has shown limited efficacy. Thus, this study seeks to identify additional molecules that can be effectively targeted in FGFR2 amplified gastric cancer, with a focus on Src homology region 2-containing protein tyrosine phosphatase 2 (SHP2). The authors first demonstrate that 6% of gastric cancer patients in a cohort of human patient samples exhibit FGFR2 amplification. Furthermore, they demonstrate that FGFR2 mRNA expression is positively correlated with PTPN11 gene expression (which is the gene that encodes the SHP2 protein). Using human gastric cancer cell lines with amplified FGFR2, the authors then test the effects of combining the FGFR inhibitor AZD4547 with the SHP2 inhibitor SHP099 on tumor cell death and signaling molecules. They demonstrate that combining the two inhibitors is more effective at tumor cell killing and reducing activation of downstream signaling pathways than either inhibitor alone. In further studies, the authors obtained gastric cancer cells with FGFR2 amplification from a patient that was treated with FGFR2 inhibitor. While this patient initially showed a partial response, the patient ultimately progressed, demonstrating resistance to FGFR2 inhibition. Following isolation of tumor cells from the patient's ascites, the authors demonstrate that these cells are sensitive to the combination treatment of AZD4547 and SHP099. Further studies were performed using a xenograft model using athymic nude mice in which the combination of SHP099 and AZD4547 were found to reduce tumor growth more significantly than either treatment alone. Finally, the authors demonstrate using an in vitro culture model that this combination treatment enhances T cell mediated cytotoxicity. The authors conclude that targeting FGFR2 and SHP2 represents a potential combination strategy in gastric patients with FGFR2 amplification.

Strengths:

The authors demonstrate that FGFR2 amplification positively correlates with PTPN11 in human gastric cancer samples, providing a rationale for combination therapies. Furthermore, convincing data are provided demonstrating that targeting both FGFR and SHP2 is more effective than targeting either pathway alone using in vitro and in vivo models. The use of cells derived from a gastric cancer patient that progressed following treatment with an FGFR inhibitor is also a strength. The findings from this study support the conclusion that SHP2 inhibitors enhance the efficacy of FGFR-targeted therapies in cancer patients. This study also suggests that targeting SHP2 may also be an effective strategy for targeting cancers that are resistant to FGFR-targeted therapies.

Weaknesses:

The main caveat with these studies is the lack of an immune competent model with which to test the finding that this combination therapy enhances T cell cytotoxicity in vivo.

Reviewer #1 (Public review):

Summary:

This paper investigates the thermal and mechanical unfolding pathways of the doubly knotted protein TrmD-Tm1570 using molecular simulations, optical tweezers experiments, and other methods. In particular, the detailed analysis of the four major unfolding pathways using a well-established simulation method is an interesting and convincing result.

Strengths:

A key finding that lends credibility to the simulation results is that the molecular simulations at least qualitatively reproduce the characteristic force-extension distance profiles obtained from optical tweezers experiments during mechanical unfolding. Furthermore, a major strength is that the authors have consistently studied the folding and unfolding processes of knotted proteins, and this paper represents a careful advancement building upon that foundation.

Weaknesses:

While optical tweezers experiments offer valuable insights, the knowledge gained from them is limited, as the experiments are restricted to this single technique.

The paper mentions that the high aggregation propensity of the TrmD-Tm1570 protein appears to hinder other types of experiments. This is likely the reason why a key aspect, such as whether a ribosome or molecular chaperones are essential for the folding of TrmD-Tm1570, has not been experimentally clarified, even though it should be possible in principle.

Comments on revisions:

According to reviewers' comments, the authors revised the manuscript appropriately.

Reviewer #2 (Public review):

Summary:

In this manuscript, the authors combined coarse-grained structure-based model simulation, optical tweezer experiments, and AI-based analysis to assess the knotting behavior of the TrmD-Tm1570 protein. Interestingly, they found that while the structure-based model can fold the single knot from TrmD and Tm1570, the double-knot protein TrmD-Tm1570 cannot form a knot itself, suggesting the need for chaperone proteins to facilitate this knotting process. This study has strong potential to understand the molecular mechanism of knotted proteins, supported by many experimental and simulation evidence. However, there are a few places that appear to lack sufficient details, and more clarification in the presentation is needed.

Strengths:

A combination of both experimental and computational studies. The authors have addressed my questions in their revised manuscript. I appreciate their efforts.

Reviewer #1 (Public review):

Summary:

Since dimerization is essential for SARS-CoV-2 Mpro enzymatic activity, the authors investigated how different classes of inhibitors, including peptidomimetic inhibitors (PF-07321332, PF-00835231, GC376, boceprevir), non-peptidomimetic inhibitors (carmofur, ebselen, and its analog MR6-31-2), and allosteric inhibitors (AT7519 and pelitinib), influence the Mpro monomer-dimer equilibrium using native mass spectrometry. Further analyses with isotope labeling, HDX-MS, and MD simulations examined subunit exchange and conformational dynamics. Distinct inhibitory mechanisms were identified: peptidomimetic inhibitors stabilized dimerization and suppressed subunit exchange and structural flexibility, whereas ebselen covalently bound to a newly identified site at C300, disrupting dimerization and increasing conformational dynamics. This study provides detailed mechanistic evidence of how Mpro inhibitors modulate dimerization and structural dynamics. The newly identified covalently binding site C300 represents novelty as a druggable allosteric hotspot.

Strengths:

This manuscript investigates how different classes of inhibitors modulate SARS-CoV-2 main protease dimerization and structural dynamics, and identifies a newly observed covalent binding site for ebselen.

Weaknesses:

The major concern is the absence of mutagenesis data to support the proposed inhibitory mechanisms, particularly regarding the role of the inhibitor binding site.

Reviewer #2 (Public review):

Summary:

This is a mechanistic study that provides new insights into the inhibition of SARS-CoV-2 Mpro.

Strengths:

The identification of dimer interface stabilization/destabilization as distinct inhibitory mechanisms and the discovery of C300 as a potential allosteric site for ebselen are important contributions to the field. The experimental approach is modern, multi-faceted, and generally well-executed.

Weaknesses:

The primary weaknesses relate to linking the biophysical observations more directly to functional enzymatic outcomes and providing more quantitative rigor in some analyses. While the study is overall strong, addressing its weaknesses and limitations would elevate the impact and translational relevance of the current manuscript.

(1) Correlation with Functional Activity:

The most significant gap is the lack of direct enzymatic activity assays under the exact conditions used for MS and HDX. While EC50 values are listed from literature, demonstrating how the observed dimer stabilization (by peptidomimetics) or dimer disruption (by ebselen) directly correlates with inhibition of proteolytic activity in the same experimental setup would solidify the functional relevance of the biophysical observations. For instance, does the fraction of monomer measured by native MS quantitatively predict the loss of activity? Also, the single inhibitor concentration used in each MS experiment needs to be specified in the main text and legends. A discussion on whether the inhibitor concentrations required to observe these dimerization effects (in native MS) or structural dynamics (in HDX-MS) align with EC50 values would be helpful for contextualizing the findings.

(2) For the two Cys residues found to be targeted by ebselen, what are their respective modification stoichiometry related to the ebselen concentration? Especially for the covalent binding site C300, which is proposed in this study to represent a novel allosteric inhibition mechanism of ebselen, more direct experimental evidence is needed to support this major hypothesis. Does mutation or modification of C300 affect the Mpro dimerization/monomer equilibrium and alter the enzymatic activity? If ebselen acts as a covalent inhibitor linked to multiple Cys, why is its activity only in the uM range?

(3) For the allosteric inhibitor pelitinib with low-uM activity, no significant differences in deuterium uptake of Mpro were observed. In terms of the binding affinity, what is the difference between pelitinib and ebselen? Some explanations could be provided about the different HDX-MS results between the two non-peptidomimetic inhibitors with similar activities.

(4) Native MS Quantification:

The analysis of monomer-dimer ratios from native MS spectra appears qualitative or semi-quantitative. A more rigorous and quantified analysis of the percentage of dimer/monomer species under each condition, with statistical replicates, would strengthen the equilibrium shift claims. For native MS analysis of each inhibitor, the representative spectrum can be shown in the main figure together with quantified dimer/monomer fractions from replicates to show significance by statistical tests.

(5) Changes of HDX rates in certain regions seem very subtle. For example, as it states 'residues 296-304 in the C-terminal region of M pro were more flexible upon ebselen binding (Figure 4c)', the difference is barely observable. The percentage of HDX rate changes between two conditions (with p values) can be specified in the text for each fragment discussed, and any change below 5% or 10% is negligible.

Reviewer #1 (Public review):

Summary:

Despite accumulating prior studies on the expressions of AVP and AVPR1a in the brain, a detailed, gender-specific mapping of AVP/AVPR1a neuronal nodes has been lacking. Using RNAscope, a cutting-edge technology that detects single RNA transcripts, the authors created a comprehensive neuroanatomical atlas of Avp and Avpr1a in male and female brains.

Strengths:

This well-executed study provides valuable new insights into gender differences in the distribution of Avp and Avpr1a. The atlas is an important resource for the neuroscience community.

The authors have previously adequately addressed all of my concerns. I have no further questions or concerns.

Reviewer #2 (Public review):

Summary:

The authors conducted a brain-wide survey of Avp (arginine vasopressin) and its Avpr1a gene expression in the mouse brain using RNAscope, a high-resolution in situ hybridization method. Overall, the findings are useful and important because they identify brain regions that express the Avpr1a transcript. A comprehensive overview of Avpr1a expression in the mouse brain could be highly informative and impactful. The authors used RNAscope (a proprietary in situ hybridization method) to assess transcript abundance of Avp and one of its receptors, Avpr1a. The finding of Avp-expressing cells outside the hypothalamus and the extended amygdala is novel and is nicely demonstrated by new photomicrographs in the revised manuscript. The Avpr1a data suggest expression in numerous brain regions. In the revised manuscript, reworked figures make the data easier to interpret.

Strengths:

A survey of Avpr1a expression in the mouse brain is an important tool for exploring vasopressin function in the mammalian brain and for developing hypotheses about cell- and circuit-level function.

[Editors' note: The authors have substantially addressed all the reviewers' concerns and comments.]

Reviewer #1 (Public review):

Summary:

RNA modification has emerged as an important modulator of protein synthesis. Recent studies found that mRNA can be acetylated (ac4c), which can alter mRNA stability and translation efficiency. The role of ac4c mRNA in the brain has not been studied. In this paper, the authors convincingly show that ac4c occurs selectively on mRNAs localized at synapses, but not cell wide. The ac4c "writer" NAT10 is highly expressed in hippocampal excitatory neurons. Using NAT10 conditional KO mice, decreasing levels of NAT10 resulted in decreases in ac4c of mRNAs and also showed deficits in LTP and spatial memory. These results reveal a potential role for ac4c mRNA in memory consolidation.

This is a new type of mRNA regulation that seems to act specifically at synapses, which may help elucidate the mechanisms of local protein synthesis in memory consolidation. Overall, the studies are well carried out and presented. The precise mRNAs that require ac4c to carry out memory consolidation is not clear, but is an important focus of future work. The specificity of changes occurring only at the end of training, rather than after each day of training is interesting and also warrants further investigation. This timeframe is puzzling because the authors show that ac4c can dynamically increase within 1hr after cLTP.

Strengths:

(1) The studies show that mRNA acetylation (ac4c) occurs selectively at mRNAs localized to synaptic compartments (using synaptoneurosome preps).

(2) The authors identify a few key mRNAs acetylated involved in plasticity and memory - eg Arc.

(3) The authors show that Ac4c is induced by learning and neuronal activity (cLTP).

(4) The studies show that the ac4c "writer" NAT10 is expressed in hippocampal excitatory neurons and may relocated to synapses after cLTP/learning induction.

(5) The authors used floxed NAT10 mice injected with AAV-Cre in the hippocampus (NAT10 cKO) to show that NAT10 may play a role in LTP maintenance and memory consolidation (using the Morris Water Maze).

Weaknesses:

(1) The NAT10 cKO mice are useful to test the causal role of NAT10 in ac4a and plasticity/memory but all the experiments used AAV-CRE injections in the dorsal hippocampus that showed somewhat modest decreases in total NAT10 protein levels. For these experiments, it would be better to cross the NAT10 floxed animals to CRE lines where better knock down of NAT10 can be achieved postnatally in specific neurons, with less variability.

(2) Because knock down is only modest (~50%), it is not clear if the remaining ac4c on mRNAs is due to remaining NAT10 protein or due to alternative writer (as the authors pose).

Reviewer #2 (Public review):

This is an interesting study that shows that mRNA acetylation at synapses is dynamically regulated at synapses by spatial memory in the mouse hippocampus. The dynamic changes of ac4C-mRNAs regulated by memory were validated by methods including ac4C dot-blot and liquid 13 chromatography-tandem mass spectrometry (LC-MS/MS).

Reviewer #1 (Public review):

Summary:

This study uncovers a protective role of the ubiquitin-conjugating enzyme variant Uev1A in mitigating cell death caused by over-expressed oncogenic Ras in polyploid Drosophila nurse cells and by RasK12 in diploid human tumor cell lines. The authors previously showed that over-expression of oncogenic Ras induces death in nurse cells, and now they perform a deficiency- screen for modifiers. They identified Uev1A as a suppressor of this Ras-induced cell death. Using genetics and biochemistry, the authors found that Uev1A collaborates with the APC/C E3 ubiquitin ligase complex to promote proteasomal degradation of Cyclin A. This function of Uev1A appears to extend to diploid cells, where its human homologs UBE2V1 and UBE2V2 suppress oncogenic Ras-dependent phenotypes in human colorectal cancer cells in vitro and in xenografts in mice.

Strengths:

(1) Most of the data is supported by sufficient sample size and appropriate statistics.

(2) Good mix of genetics and biochemistry.

(3) Generation of new transgenes and Drosophila alleles that will be beneficial for the community.

Comments on revisions:

The authors have greatly improved the manuscript and satisfactorily addressed all of my concerns.

Reviewer #2 (Public review):

Summary:

The authors performed a genetic screen using deficiency lines and identified Uev1a as a factor that protects nurse cells from RasG12V-induced cell death. According to a previous study from the same lab, this cell death is caused by aberrant mitotic stress due to CycA upregulation (Zhang et al.). This paper further reveals that Uev1a forms a complex with APC/C to promote proteasome-mediated degradation of CycA.

In addition to polyploid nurse cells, the authors also examined the effect of RasG12V-overexpression in diploid germline cells, where RasG12V-overexpression triggers active proliferation not cell death. Uev1a was found to suppress its overgrowth as well.

Finally, the authors show that the overexpression of the human homolog, UBE2V1 and UBE2V2, suppresses tumor growth in human colorectal cancer xenografts and cell lines. Notably, these genes' expression correlates with the survival of colorectal cancer patients carrying Ras mutation.

Strength:

This paper presents a significant finding that UBE2V1/2 may serve as a potential therapy for cancers harboring Ras mutations. The authors propose a fascinating mechanism in which Uev1a forms a complex with APC/C to inhibit aberrant cell cycle progression.

Comments on revisions:

The authors have addressed several of the major concerns, including the addition of new data and improved figure presentation. However, some issues remain insufficiently resolved, particularly regarding control reuse (Major Comment 3) and experimental interpretation (Major Comments 5 and 8).

Regarding Major Comment 5, the authors state that UAS copy number affects the frequency of egg chamber degradation in Fig. 2D, and thus explains the reduced phenotype in RasG12V + GFP-RNAi compared to RasG12V alone. However, this explanation is not consistent with other data in the manuscript. UAS-RasG12V combined with UAS-lacZ in Fig. 2G shows a phenotype comparable to UAS-RasV12 alone, despite also increasing the UAS copy number. This suggests that the effect is not simply due to copy number.

I understand that the authors used UAS-RasG12V + GFP-RNAi as a control for the RNAi experiments and UAS-RasG12V + lacZ for the overexpression experiments. I suggest examining the phenotype frequency of UAS-RasG12V + UAS-GFP, to figure the reason out. Overall, these results indicate that there is a spectrum of phenotype frequencies, and therefore appropriate controls should be included for each experiment rather than reusing the same dataset across different experiments, as also noted in Major Comment 3.

Reviewer #1 (Public review):

Summary:

The authors used an in vitro microfluidic system where HUVECs are exposed to high, low or physiologic (normal) shear stress to demonstrate that both high and low shear stress for 24 hours resulted in decreased KLF6 expression, decreased lipid peroxidation and increased cell death which was reversible upon treatment with Fer-1, the ferroptosis inhibitor. RNA sequencing (LSS vs normal SS) revealed decreased steroid synthesis and UPR signaling in low shear stress conditions, which they confirmed by showing reduced expression of proteins that mitigate ER stress under both LSS and HSS. Decreased KLF6 expression after exposure to HSS/LSS was associated with decreased expression of regulators of ER stress (PERK, BiP, MVD) which was restored with KLF6 overexpression. Overexpression of KLF6 also restored SLC7A11 expression, Coq10 and reduced c11 bodipy oxidation state- all markers of lipid peroxidation and ferroptosis. The authors then used vascular smooth muscle cells (atherosclerotic model) with HUVECs and monocytes to show that KLF6 overexpression reduces the adhesion of monocytes and lipid accumulation in conditions of low shear stress.

Strengths:

(1) The use of a microfluidic device used to simulate shear stress while keeping the pressure constant when varying shear stress applied is improved and more physiologic compared to traditional cone and shearing devices. Similarly, the utilization of both low and high shear stress in most experiments is a strength.

(2) This study provides a link between disturbed shear stress and ferroptosis, which is novel, and fits nicely with existing knowledge that endothelial cell ferroptosis promote atherosclerosis. This concept was also recently reported Sept 2025 when a publication also demonstrated that LSS trigger ferroptosis in vascular endothelial cells (PMID: 40939914), which partly validates these findings.

Weaknesses:

(1) While HUVECs are commonly used in endothelial in vitro studies, it would be preferable to confirm the findings using an arterial cell line such as human coronary artery cells when studying mechanisms of early atherosclerosis. Furthermore, physiologic arterial shear stress is higher than venous shear stress, and different vascular beds have varying responses to altered shear stress and as such, the up and downregulated pathways in HUVECs should be confirmed in an arterial system.

(2) The authors provide convincing evidence of disturbances in shear stress inducing endothelial ferroptosis with assays for impaired lipid peroxidation and increased cell death that was reversed with a ferroptosis inhibitor. However more detailed characterization of ferroptosis with iron accumulation assays, as well as evaluating GPX4 activity as a consequence of the impaired mevalonate pathway, and testing for concomitant apoptosis in addition to ferroptosis would add to the data.

(3) The authors state that KLF2 and KLF4 are not amongst the differentially expressed genes downregulated by reduced shear stress, which is contrary to previous data, where both KLF2 and KLF4 are well studied to be upregulated by physiologic laminar shear stress. While this might be due to the added pressure in their microfluidic system, it also might be due to changes in gene expression over time. In this case, a time course experiment would be needed. It is possible that KLF2, KLF4 and KLF6 are all reduced in low (and high) shear stress and cooperatively regulate the endothelial cell phenotype. Both KLF2 and KLF4 have been shown to be protective against atherosclerosis.

Comments on revisions:

The authors have failed to respond to all the preceding critiques with supporting experimental data. Recommend a reassessment of the initial critiques.

Reviewer #1 (Public review):

The study provides a robust bioinformatic characterization of the evolution of pT181. My main criticism of the work is the lack of experimental validation for the hypotheses proposed by the authors.

Comments on the study:

(1) One potential reason for the decline in pT181 copy number over time may be a high cost associated with the multicopy state. In this sense, it would be interesting if the authors could use (or construct) isogenic strains differing only in the state of the plasmid (multicopy/integrated). With this system, the authors could measure the fitness of the strains in the presence and absence of tetracycline, and they could be able to understand the benefit associated with the plasmid transition. The authors discuss these ideas, but it would be nice to test them.

(2) It would be interesting to know the transfer frequencies of the multicopy mobilizable pT181 plasmid, compared to the transfer frequency of the plasmid integrated into the SSCmec element (which can be co-transferred, integrated in conjugative plasmids, or by transduction).

(3) One important limitation of the study that should be mentioned is that inferring pT181 PCN from whole genome data can be problematic. For example, some DNA extraction methods may underestimate the copy number of small plasmids because the small, circular plasmids are preferentially depleted during the process (see, for example, https://www.nature.com/articles/srep28063).

Reviewer #2 (Public review):

Summary:

The authors performed bioinformatic analyses to trace the genomic history of the clinically relevant pT181 plasmid. Specifically, they:

(1) tracked the presence of pT181 across different S. aureus strain backgrounds through time. It was first found in one, later multiple strains, though this may reflect changes in sampling over time.

(2) estimated the mutation rate of the chromosome and plasmid.

(3) estimated the plasmid copy number of pT181, and found that it decreased over time. The latter was supported by two sets of statistical analyses, first showing that the number of single-copy isolates increased over time, and second, that the multicopy isolates demonstrated a lower PCN over time.

(4) reported the different integration sites at which pT181 integrated into the genome.

As a caveat, they mentioned that identical plasmid sequences have variable plasmid copy numbers across different genomes in their dataset.

Strengths:

This is a very solid, well-considered bioinformatic study on publicly available data. I greatly appreciate the thoughtful approach the authors have taken to their subject matter, neither over- nor underselling their results. It is a strength that the authors focussed on a single plasmid in a single bacterial species, as it allowed them to take into account unique knowledge about the biology of this system and really dive deep into the evolution of this specific plasmid. It makes for a compelling case study. At the same time, I think the introduction and discussion can be strengthened to demonstrate what lessons might be drawn from this case study for other plasmids.

Weaknesses:

The finding that the pT181 copy number declined over time is the most interesting claim of the paper to me, and not something that I have seen done before. While the authors have looked at some confounders in this analysis, I think this could be strengthened further in a revision.

For the flow of the storyline, I also think the estimation of mutation rates (starting L181) and integration into the chromosome (starting L255) could be moved to the supplement or a later position in the main text.

Clearly, the use of publicly available data prevents the authors from controlling the growth and sequencing conditions of the isolates. It is striking that they observe a clear signal in spite of this, but I would have loved to see more discussion of the metadata that came with the publicly available sequences and even more use of that metadata to control for confounding.

Reviewer #1 (Public review):

Summary:

PSD95 has long been studied in detail to understand molecular mechanisms of synaptic plasticity as related to specific cell types (excitatory), circuits (visual cortex) and circuit development and function (ocular dominance plasticity ). While much was known about the molecular and cellular details of its function, it remained unclear whether and how it might contribute to the development of specific aspects of visual perception. While overall vision is preserved in PSD95 KO (Knockout) mice, studying natural, visually-guided prey capture behavior revealed robust, yet specific, perturbations to binocular processing during the behavior.

Strengths:

A major strength of the paper is being able to quantify precise measures of the visual aspects versus the motor aspects of prey pursuit. Comparing changes in behavior due to monocular occlusion was particularly revealing that mice indeed employ binocular summation to extract visual cues useful for prey pursuit. This result further suggested that in cases with poor binocular vision, monocular input can improve perceptual and behavioral processes as it does in human subjects with comparable challenges.

The study not only provided a useful finding regarding the function of PSD95, but also outlined a useful general approach toward identifying and quantifying specific deficits in binocular summation. This is likely to broadly impact studies of visual system development, behavior, and neural circuit function. The careful attention to details, observations, and openness about subject variance will also be helpful to those studying specific visual pursuit and natural prey capture behavior in the mouse.

Weaknesses:

Lack of eye movement monitoring and detailed head movement analysis preclude total certainty for the interpretation of observed behaviors.

Reviewer #2 (Public review):

Summary:

This manuscript studies the impacts of knocking out a protein known to be involved in synapse maturation in mice, measuring their ability to hunt prey items (and to discriminate simple visual patterns) under binocular and monocular viewing conditions. The main results are that the mice with this protein knocked out are impaired when performing visual tasks with binocular viewing, but are actually better when they perform monocularly. The interpretation is that the knocked-out protein has affected binocular visual integration.

Strengths:

Overall, the attempt to connect a protein to behavior/perception, via known mechanistic effects on synapse development and visual critical periods, is admirable.

The use of multiple visual conditions and behavioral paradigms (binocular/monocular, cricket hunting/orientation discrimination, light/dark) strengthens and enriches the results.

Weaknesses:

The primary interpretation - that binocular integration is affected in the PSD-95 knockouts- is not supported by the behavioral evidence. Using behavior to isolate a particular stage in visual processing (and further, to distinguish it from elements of generating the behavioral response and/or acquiring the visual information in the first place) is notoriously difficult. Such attempts are, of course, the domain of psychophysics. In fact, the most classical and loveliest success is in the domain of binocular integration- Bela Julesz's "psychoanatomy" that used random dot stereograms to isolate stereoscopic computations.

I mention this example because it is, in fact, directly relevant to my primary concern about the evidence used as support for the favored interpretation here. Julesz's stimuli were extremely clever in isolating binocular mechanisms (i.e., binocular mechanisms MUST be used to perform the task), and any perceptual/behavioral reports are very straightforward to interpret (i.e., a stereoscopically-defined shape can be identified, or not).

Now compare this to the work described in this manuscript. KO (knockout) mice are worse than wild types at chasing prey items or at moving towards a rewarded orientation, but they get better when performing this task monocularly. No argument that that is an interesting bit of scientific phenomenology to characterize. However, the behaviors do not require binocular integration, the freely-moving paradigms involve a variety of gaze and body-movement strategies, and the metrics used to quantify performance are similarly high-dimensional. Bottom line, it is not possible to glean whether the KO's intriguing binocular-vs-monocular differences are due to binocular integration per se, or something better thought of as fundamentally sensorimotor in origin. The tasks do not isolate visual from sensorimotor processing, and the behaviors and associated metrics cannot definitely adjudicate between a multitude of possible specific interpretations.

More specifically, the KO mice may have abnormal patterns of binocular coordination. Eye movements were not tracked in these studies, despite the availability of such instrumentation and their successful application in many preceding studies of mouse prey capture. If the KO mice do not coordinate their eye movements (in task-specific/task-relevant ways), they might receive binocular input that is abnormal. Under monocular conditions, that mismatched or inappropriately coordinated binocular input is absent, which would relieve them of the confusing visual information. That is rather different than having an impairment of binocular integration, as it is basically a question of whether the visual system is impaired, or whether the inputs to the visual system are abnormal due to differences in binocular coordination.

It is also possible that the binocular deficit, as measured in behavior,r occurs in a distinct part of the sensorimotor loop. Even if the binocular eye movements are normal, and binocular visual integration is normal, PSD-95 KO mice may be confused or distracted by the larger visual field that comes from binocular viewing (quite profound in species with mostly lateralized eyes). Such a "post-sensory" interpretation related to target selection (from what could be a totally normal visual representation) is difficult to rule out as well.

In summary, this reviewer appreciates the value of trying to connect this molecular mechanism to sensory processing and behavior. The use of naturalistic tasks and freely-moving paradigms is also something to commend. However, the sorts of visual stimuli and behavioral paradigms used here are not well-suited to supporting the rather specific interpretation that has been put forth in this manuscript.

Reviewer #3 (Public review):

Summary:

Bhattacharya et al. describe significant differences in prey capture behaviour in PSD-95 KO (Knockout) and wild-type (WT) mice. This work develops logically from their previous findings that KO of PSD-95 inhibits the maturation in the primary visual cortex. However, their previous work revealed that the visual deficits in the KO mice were relatively modest. Here, by employing an ethologically-relevant behavioural task, they show that several aspects of prey capture are impaired in the KO. Importantly, the deficits in predatory behavior in the KO mouse improved with monocular deprivation, consistent with deficits in binocular vision.

Strengths:

Overall, the data presented are convincing and valuable, and support the idea that PSD-95 expression is important for the maturation of visual responses.

Weaknesses:

The manuscript could be strengthened by consideration of the following points:

(1) The deficits in predatory behavior are interpreted to reveal several possible visual defects, including the absence of binocularity, binocular summation, or binocular mismatch in V1 neurons. Yet this is done with insufficient detail about each possible mechanism and without direct neuronal evidence.

(2) The observation that binocular visual field bias is intact in the PSD-95 KO mice is interesting but appears to contradict other data suggesting the absence of binocularity in the KO visual system, and this is not discussed in sufficient detail.

(3) No consideration of previous work using constitutive PSD-95 KOs that documented a learning deficit.

(4) Throughout the manuscript, including the first paragraph of the discussion, the authors state that "This study explored whether the maturation of CP closure, inhibited by PSD-95 influences binocular visual behaviour". However, if this were the case, the current experiments would have compared cricket capture behavior at two ages across the two genotypes: pre- and post-CP closure in WTs and at matching chronological ages in KOs.

(5) Freeman and others have shown that the influence of binocular summation on orientation discrimination is highest at low stimulus contrast and short duration stimuli. How does this impact the interpretation of predatory behavior and discrimination in the VWT?

Reviewer #2 (Public review):

The revised manuscript does a good job of using less definitive language, particularly by adding "possible" qualifiers to several interpretations. This addresses the concern about overstatement.

The main issue raised in the original review, however, remains unresolved. Only two elephant bone specimens at EAK show green-bone breakage interpreted as anthropogenic, and the diagnostic basis for that interpretation is not demonstrated clearly on the EAK material itself. The manuscript discusses a suite of fracture attributes described as diagnostic of dynamic percussive breakage, but these attributes are not explicitly documented on the EAK specimens. Instead, the diagnostic traits are illustrated using material from other Olduvai contexts, and that behavior is then extrapolated to make similar claims at EAK. For a paper making a potentially important behavioral argument, the key diagnostic evidence is not clearly demonstrated at the focal assemblage.

This problem is evident in the presentation of the EAK specimens. In their response, the authors state that one EAK specimen shows "overlapping scars" and constitutes a "long bone flake"; however, these features are not clearly identifiable in the figures or captions as currently presented. The authors state that Figures S21-S23 clearly indicate human agency, including a long bone flake with overlapping scars and a view of the medullary surface, but it is unclear which specimens or surfaces these descriptions refer to. Figure S21 does appear to show green fracture and is described only as an "elephant-sized flat bone fragment with green-bone curvilinear break." Figure S22 shows the same bone and cortical surface in a different orientation, providing no additional information. In Figure S23, I cannot clearly identify a medullary surface or evidence of green-bone fracture from this image. None of these images clearly demonstrates overlapping scars, and the figures would be substantially improved by explicitly identifying the features described in the text. Even if both EAK specimens are accepted as green-broken, they do not demonstrate the co-occurrence of multiple diagnostic fracture traits such as multiple green breaks, large step fractures, hackle marks, and overlapping scars that the authors state is required to attribute dynamic percussive activity to hominins and address equifinality.

I appreciate that the authors are careful to state that spatial association between stone tools and fossils alone does not demonstrate hominin behavior, and that they treat the spatial analyses as supportive rather than decisive. While the association is intriguing, the problem is downstream: spatial association is used to strengthen an interpretation of butchery at EAK that still depends on fracture evidence that is not clearly documented at the assemblage level.

The critique concerning Nyayanga is not addressed in the revision. The manuscript proposes alternative explanations for the Nyayanga material but does not demonstrate why these are more plausible than the interpretation advanced by Plummer et al. (2023). I am not arguing that the Nyayanga material should be accepted as butchery; rather, showing that trampling is possible does not establish it as more probable than cut marks. In contrast, the EAK material is treated as evidence of butchery on the basis of evidence that, in my opinion, is more limited and less clearly demonstrated. Even if this is not the authors' intention, the uneven treatment removes an earlier megafaunal case from the comparison and strengthens the case for interpreting EAK as marking a behavioral shift toward megafaunal butchery by excluding other early cases.

While I remain concerned about how the EAK evidence is documented and interpreted, I think the manuscript is appropriate for publication and will generate useful discussion. Readers can then assess for themselves whether the available evidence supports the strength of the behavioral claims.

Reviewer #1 (Public review):

Summary:

This manuscript follows up previous work from this group using a conditional TCF4 mouse where Cre-expression turns "on" expression of TCF4 to investigate whether postnatal re-expression of TCF4 is effective to correct phenotypes related to Pitt-Hopkins Syndrome (PTHS) in humans. Results may inform gene therapy human PTHS gene therapy efforts on effective developmental windows for gene therapy. The authors demonstrate that re-expression of TCF4, induced by retro-orbital (RO) AAV-PHP.eB-Cre, during 2-4th postnatal week, does not rescue brain or body weight, anxiety-like or nest-building behaviors, but rescues an object location memory task, a measure of cognition. These results are novel and interesting in that they reveal distinct developmental roles for TCF4 in distinct behaviors and suggest that TCF4 plays a role in the mature brain in hippocampal and memory-related plasticity. Results may inform gene therapy design in PTHS.

Strengths:

The results are rigorous and high quality. Multiple methods are used to assess AAV-mediated re-expression of Cre, reactivation of TCF4, and the developmental time course of expression. Multiple behavioral phenotypes and molecular rescue are assessed. Most behavioral phenotypes are reproducible and robust, and it is clear whether a rescue was observed.

Weaknesses:

(1) Although the authors demonstrate the time course and spatial extent of Cre and a Cre-reporter (TdTom) in the brain with the AAV-Cre, it is unclear how many cells are transduced. Similarly, the authors do not measure TCF4 levels with immunohistochemistry or western blot. So the level of protein reactivation is unknown. A possible reason the rescue is incomplete is that the TCF4 protein is not induced in a large % of neurons in specific brain regions that mediate specific behaviors, such as the hippocampus vs. the striatum.

(2) The authors perform bulk qPCR to demonstrate a 20% increase in TCF4 RNA with Cre-mediated activation. It is unclear why the full gene reactivation is not observed. An alternative interpretation of the incomplete rescue of the phenotypes is that full TCF4 expression is required at later developmental time points.

Reviewer #2 (Public review):

Summary:

The basic helix-loop-helix transcription factor TCF4 (also known, as ITF2, SEF2, or E2-2) is a protein involved in the development and functioning of many different cell types. TCF4 plays important roles in the nervous system, both in health and disease. Its importance in the nervous system is underlined by its association with common and rare cognitive disorders. Specifically, variants of the TCF4 gene are implicated in increased susceptibility to schizophrenia, and mutations in the TCF4 gene cause Pitt-Hopkins syndrome (PTHS) or mild to moderate non-syndromic intellectual disability.

In this manuscript, the authors have studied whether reinstating TCF4 later in postnatal development in juvenile PTHS model mice could reverse behavioral phenotypes, thereby simulating gene therapy. Previous research by the same group has demonstrated that restoring TCF4 during embryonic or neonatal stages, corresponding to prenatal or neonatal periods in humans, improved phenotypes in a PTHS mouse model. In the current study, a conditional TCF4 reinstatement mouse model, Tcf4-lox-stop-lox (Tcf4-LSL), previously developed and characterized by their lab, where Cre-mediated recombination removes a floxed transcriptional stop cassette downstream of exon 17, leading to reinstatement of all TCF4 isoforms at appropriate levels in neurons, was used. The study showed that this later intervention failed to correct most phenotypes, suggesting that perinatal reinstatement of TCF4 holds the greatest potential to treat behavioral symptoms of PTHS. However, the study also suggests that some cognitive behaviors may still be responsive to TCF4 reinstatement later in life.

Strengths:

This is a very important study aimed at developing gene therapy for PTHS. The study is technically very well performed and written.

Weaknesses:

The only weakness is that a human disease is modelled in a mouse, which is evolutionarily not the closest mammal to humans. Hopefully, in the future, similar studies will also be performed in a nonhuman primate model, for example rhesus macaque.

Reviewer #1 (Public review):

Summary:

The authors aimed to develop a translational framework for predicting vaccine reactogenicity by training a penalized ordinal regression model on mouse muscle transcriptomics and applying it across tissues and species to rank human vaccines by their inflammatory potential.

Strengths:

The study addresses an important gap in preclinical vaccine safety assessment. The identification of IL6/JAK/STAT3 signaling as a key pathway implicated in reactogenicity is biologically plausible, and the observation of coordinated changes between muscle and blood compartments supports the biological relevance of the signature. The model achieves near-perfect classification in mouse muscle tissue and successfully identifies Fluad (MF59-adjuvanted) as the most reactogenic among licensed human vaccines, consistent with clinical safety data.

Weaknesses:

The methodological foundation has several concerns. The reactogenicity class definitions rely on PC1 scores with modest variance explained, yet no sensitivity analyses demonstrate robustness to different normalization strategies, feature selection approaches, or dimensionality reduction methods. I suggest performing sensitivity analyses demonstrating that reactogenicity class definitions are robust to alternative normalization methods, feature selection criteria, and dimensionality reduction approaches.

The combined mouse analysis reveals that tissue effects dominate over vaccine-induced variation, and no explicit batch or compartment correction was reported. The authors can apply batch/compartment correction (e.g., SVA) when analyzing combined mouse muscle and blood data, then recompute PCA and downstream analyses.

The central claim regarding cross-species ranking capability is not fully supported. In human blood, the model largely distinguishes Fluad from other vaccines but shows limited separation among non-Fluad formulations, with many pairwise comparisons yielding non-significant adjusted p-values. This pattern suggests the model may be tuned to detect large inflammatory magnitudes-likely a consequence of training on extreme stimuli such as LPS and whole-cell pertussis-rather than capturing the finer gradations relevant for distinguishing licensed vaccines with moderate reactogenicity profiles. I highly suggest retraining the model, excluding extreme stimuli (LPS, Pentavac), to evaluate whether mid-range separations among licensed vaccines can be recovered.

Impact:

While the conceptual framework is promising, the current evidence does not convincingly demonstrate that the model can rank vaccines beyond identifying highly inflammatory outliers. The utility for preclinical assessment of novel vaccine candidates with moderate reactogenicity profiles remains uncertain.

Reviewer #2 (Public review):

Summary:

The authors derived a time-specific signature of reactogenicity from mouse muscle following exposure to vaccines /TLRs for capturing the reactogenicity patterns. They tested this reactogenicity signature in mouse blood, and then they applied the reactogenicity signature to human blood from subjects having received different vaccines. They identified biomarkers in mouse muscle which are also observed in mouse and human blood and could be used as a reactogenicity signature in mice, instead of CRP.

Strengths:

(1) The authors used transcriptomic response following vaccination and used common genes to human and mice for defining a reactogenic signature.

(2) As the authors used different formulations in mice, the model was trained across a broad reactogenicity spectrum, which has the advantage of being used for evaluating new vaccines/vaccine platforms.

Weaknesses:

(1) The muscle gene signature reflects local reactogenicity. Systemic reactogenicity is not specifically addressed, except where overlapping gene signatures are observed for both local and systemic reactogenicity.

(2) In the same logic, could we find additional genes in the blood which are not captured in the muscle?

(3) The peak of the reactogenicity is usually 24h; it is not certain that additional TPs have helped the findings. If they have, the authors should explain.

Reviewer #1 (Public review):

This manuscript by Toczyski and colleagues explores the role of ubiquitin-dependent degradation in the co-regulation between pro- and anti-apoptotic proteins. The binding of the pro-apoptotic sensor Bim to BCL2 anti-apoptotic proteins sequesters it into inactive complexes, inhibiting BCL2 members but also preventing Bim from activating the apoptotic executors BAX and BAK. The authors now suggest that the E3 ubiquitin ligase Cul5-Wsb2 targets Bim turnover while in complex with BLC2 members. The authors reveal the importance of WSB2 in apoptosis of neuroblastoma cell lines, highlighting the importance of Wsb2 as a cancer biomarker. In sum, this study identifies Bim as a novel Wsb2 target and suggests a novel co-receptor mechanism using BCL-2 members as bridging factors, thus adding a novel mechanistic layer to the apoptosis repressor role of Wsb2. Their experimental approach is sound, and in most cases, the conclusions are justified. However, whether Cul5-Wsb2 targets Bim via BLC2 anti-apoptotic members would require further analysis.

Major comments:

(1) They find that Wsb2 or Cul5 downregulation increases the levels of Puma and Bim isoforms, and that Wsb2 strongly interacts with all Bim isoforms. Moreover, Wsb2 regulates Bim turnover, especially visible for Bim-EL, and controls Bim-L ubiquitylation. Finally, Figure 2E suggests that Wsb2-Bim interaction is bridged by Bcl-xL, and they identify the domain in Bcl-xL/Wsb2 responsible for their binding in Figure 4A-E. However, Figure 4F shows only a mild decrease between Bim-EL and HA-Wsb2EEE, which is inconsistent with their model. This important gap should be backed up by further experimental evidence. For example, by performing (a) coIP studies between Bim and Wsb2 in the presence of Bcl-xlAAA and (b) Bim stability and ubiquitylation analysis in the presence of either Bcl-xlAAA or Wsb2EEE.

(2) The manuscript lacks quantifications and statistical analysis in most figures, which are particularly important for Figure 1D - especially regarding the upregulation of Puma and Bim isoforms upon downregulation of Cul5 and Wsb2, for Fig 3A - also including statistical analyses of Bim1 stability in presence or absence of proteasomal inhibitors, and for Figure 4D, F, especially regarding the interaction of Bim-EL- with WT and mutant Bcl-xL in 4D and with WT and mutant Wsb2 in 4F.

(3) The localization of BCL2 family members at the mitochondrial outer membrane is a crucial step in the implementation of apoptosis, and BCL2 members recruit Bim to the OM. Despite their finding suggesting that Bim insertion into the OM might be dispensable for interaction with Bim, the interaction was abolished by BH3-mimetics that disrupt Bcl-xL interaction with BIM. This suggests that Wsb2 interacts with Bim at the mitochondrial surface. Therefore, it would be interesting to investigate the sub-cellular localization Bim and WSB2 with and without ABT-263.

(4) Wsb2 mildly interacts with Bcl-xL and with Mcl1, but does not interact with Bcl-w or Bcl2. However, they show that Wsb2 recognizes Bcl-xl through a motif conserved between Bcl-xl, Bcl-w and Bcl2. Therefore, it would be helpful to precipitate Bcl-w or Bcl2 and check interaction with Wsb2.

Reviewer #2 (Public review):

Summary

This manuscript proposes an original and conceptually interesting model in which anti-apoptotic BCL-2 family proteins, particularly BCL-XL and MCL-1, not only sequester BIM but also act as adaptor "co-receptors" that recruit BIM to the CUL5-WSB2 ubiquitin ligase complex for degradation. The authors present a mechanistic framework supported by structure-guided mutagenesis, BH3 mimetic perturbations and co-immunoprecipitation assays performed in RPE1 cells. In parallel, the study shows that neuroblastoma cell lines are highly dependent on WSB2 for survival. These observations give the work both conceptual and translational relevance.

Strengths

The principal strength of the study lies in its conceptual novelty. Reframing BCL-XL and MCL-1 not only as sequestration factors but also as adaptors that facilitate substrate engagement by an E3 ligase substantially extends current models of apoptotic regulation. The mechanistic narrative developed in RPE1 cells is clear and internally consistent: the combination of AlphaFold-guided motif identification with complementary mutagenesis provides a persuasive framework for how WSB2 associates with anti-apoptotic BCL-2 family members and promotes BIM turnover. The definition of a BCL-XL/MCL-1 co-receptor mechanism for WSB2-mediated BIM degradation is therefore both intuitive and mechanistically appealing. In parallel, the authors present a distinct experimental series showing that neuroblastoma cells exhibit pronounced sensitivity to WSB2 loss, undergo apoptosis upon its depletion and display reduced competitiveness in mixed-culture assays. Although the mechanistic connection between these observations requires further clarification, the convergence of a well-defined biochemical model with a clear cancer-relevant phenotype enhances the potential biological significance of WSB2 and raises the possibility that its regulation may hold therapeutic relevance.

Weaknesses

There are several limitations that readers should consider when interpreting the study. The most fundamental issue is the disconnect between the mechanistic model established in RPE1 cells and the apoptotic phenotype observed in neuroblastoma. Although the manuscript convincingly demonstrates the WSB2-BCL-XL/MCL-1-BIM axis in RPE1 cells and independently shows that WSB2 loss compromises neuroblastoma viability, it does not examine whether BIM levels are elevated upon WSB2 depletion in neuroblastoma, nor whether apoptosis in these cells requires BIM. Without demonstrating WSB2-BCL-2-BIM complex formation or BIM dependence in the disease-relevant context, it remains unclear whether the co-receptor mechanism characterised in RPE1 cells explains the phenotype. This gap is compounded by the observation that PUMA, another potent pro-apoptotic factor, also increases following WSB2 loss, raising the possibility that multiple death pathways contribute to the outcome. The absence of a genetic rescue experiment, such as re-expression of an shRNA-resistant WSB2 restoring viability and suppressing apoptosis, further limits causal inference regarding WSB2's role in neuroblastoma.

Many central claims rely on single Western blots and pulldown assays without quantification or assessment of reproducibility. This complicates the interpretation of CHX chase experiments (where initial steady-state levels differ between samples) and limits confidence in BH3 mimetic experiments, which use a single concentration and short exposure time. Without dose-response curves, time-course analyses, caspase inhibition, or orthogonal genetic perturbation of BCL-XL or MCL-1, indirect or off-target drug effects cannot be excluded. Reduced co-IP signals in these assays could therefore reflect early apoptotic events or compound instability rather than specific disruption of protein-protein interactions.

A further limitation concerns the inference of a direct WSB2-BCL-XL interaction. The mutagenesis analyses are performed in lysates that contain endogenous or overexpressed BIM, and BH3 mimetics disrupt the WSB2 interaction only when the BCL-XL-BIM heterodimer is dismantled. The study thus cannot distinguish whether the mapped WSB2 motifs mediate direct contact with BCL-XL or whether they influence the architecture or stability of the BCL-XL-BIM complex. Because no purified protein reconstitution or biophysical binding assays are presented, the evidence for direct binding remains suggestive rather than conclusive.

The ubiquitination data also remain incomplete. Although the WSB2 mutation reduces the ubiquitin smear on BIM, the assay does not demonstrate dependence on CUL5, RBX2 or ARIH2, leaving open which ligase components are directly responsible. MLN4924 implicates CRLs more broadly, but the ubiquitination assay itself does not assign activity to the CUL5-WSB2 module.

Finally, several methodological details are insufficiently described, including the generation and validation of the doxycycline-inducible WSB2 and HA-WSB2 lines and the suitability of the WSB2-overexpressing control line used in immunoprecipitations.

Collectively, these issues do not undermine the conceptual interest of the proposed co-receptor model, but they do limit the strength of the mechanistic claims and weaken the connection between the defined mechanism and the neuroblastoma phenotype.

Reviewer #1 (Public review):

Kotzadimitriou et al. investigate how synaptotagmin-7 (syt7) contributes to short-term plasticity at cortical glutamatergic synapses. Using quantal-level iGluSnFR imaging and failure-based analyses at single boutons, the authors distinguish between synchronous and asynchronous glutamate release across boutons with differing baseline efficacy. They show that knocking out syt7 abolishes facilitation of synchronous release while leaving asynchronous facilitation largely intact, although reduced in magnitude. Furthermore, they argue that synchronous and asynchronous events arise from functionally distinct vesicle pools. The manuscript concludes that syt7 is essential for the facilitation of synchronous release, while other calcium sensors govern asynchronous release.

Strengths:

(1) The use of iGluSnFR provides a robust readout of single-synapse activity. Unlike traditional ephys methods that average the activity of thousands of synapses (which may mask the facilitation of low Pr synapses), the authors employ quantal imaging to analyze thousands of individual boutons and stratify them by efficacy. The representative images and traces in Figure 1 are of high quality, and the quantal analysis demonstrating multiple quantal peaks aligns well with previously published work (Mendonca et al., 2022; Wang et al., 2022).

(2) The failure-based analysis is thoughtfully implemented. By isolating trials in which no release occurred, the authors effectively separate facilitation from depletion, strengthening their central argument that syt7 is required for facilitation independent of vesicle depletion.

(3) The proposed model (depicted in Figure 7) is interesting and may reconcile the contradictory roles attributed to syt7, as described by others in the field. Specifically, the authors provide data to address syt7's potential function in facilitation, asynchronous release, and replenishment. However, to further support their model, which argues that "multiple Ca2+ sensors have both unique and overlapping roles in regulating synaptic plasticity," additional experiments are needed (see point 2 below).

Weaknesses:

(1) While the authors use cultures from syt7 knockout mice (and wild-type controls), there are no acute rescue experiments (e.g., syt7 viral transduction in KO cultures) or checks for compensatory changes in other proteins. Previous studies (Bacaj et al., 2013; Jackman et al., 2016) have utilized viral rescues to confirm specificity. Without such experiments, it remains theoretically possible that the chronic loss of syt7 leads to downregulation of another protein essential for facilitation. At a minimum, the authors should perform rescue experiments for at least some of their findings. Additionally, western blots for syt1 and syt7 should be conducted to confirm that their knockout is specific to syt7.

(2) The manuscript acknowledges the possible roles of Doc2a and syt3 but fails to address them experimentally. Recent work (Wu et al., 2024; Weingarten et al., 2024) has identified Doc2a as the primary sensor for asynchronous release. Even if its expression in cortical cultures remains unconfirmed (as claimed by the authors), they should, at the very least, perform Western blots for Doc2a and syt3 in both wild-type (to determine basal expression levels) and syt7 knockout cultures. Without analyzing the levels of these proteins, the mechanism/model behind the "remaining" asynchronous release remains speculative. Is it possible that these other calcium sensors are upregulated in their syt7 KO cultures and could instead explain their results?

Reviewer #2 (Public review):

Summary:

In this elegant study, the authors employ live iGluSnFR-based imaging of glutamate release from cortical boutons to dissect the distinct roles of the Ca²⁺ sensor synaptotagmin-7 (Syt7) in synaptic transmission. Although multiple functions have been attributed to Syt7 over the years, the field remains conflicted. The authors argue that one major obstacle for resolving some of these discrepancies lies in a fundamental limitation of electrophysiological recordings, which aggregate signals across all synapses to yield averaged readouts, dominated by strong, high-release-probability synapses. By using a live glutamate imaging approach combined with sensitive detection of action potential-evoked activity across different stimulation regimes, and a dedicated analysis pipeline, the authors confirm a role for Syt7 in facilitating synchronous release and in regulating the magnitude of asynchronous release. In contrast, they find no evidence that Syt7 contributes to the facilitation of asynchronous release, do not find evidence for a role for Syt7 in synaptic vesicle replenishment during AP trains, and provide evidence suggesting that the maintenance of facilitation by Syt7 may occur independently of vesicle depletion.

Strengths:

This study offers a fresh perspective on a debated issue, using a new experimental approach that the authors previously explored in the context of Synaptotagmin 1 (Mendonca et al. 2022). The authors record the response to a series of pair-pulse stimulations, followed by an AP train. By carefully quantifying individual events and by sorting events based on their efficacy, the authors extract quantitative information that they assign to different properties of synaptic function. They also devised an interesting approach for monitoring aspects of facilitation, in which they isolate PPR events where the first response did not elicit detectable release (thus regarding the release in response to the second AP as facilitating), and compare them with successful events. Together, the authors provide semi-quantitative descriptions of synchronous and asynchronous release during single, paired, and AP trains, yielding a weighted estimate of Syt7's contribution to distinct features of synaptic vesicle release that are independent of postsynaptic readouts. A major strength of the study is the confirmation of two principal proposed functions of Syt7: facilitation of synchronous release and regulation of the magnitude of asynchronous release.

Weaknesses:

The experimental approach presented here is elegant and well-executed. However, a principal limitation lies in translating electrophysiological terminology to imaging-based measurements. For instance, interpreting signals persisting beyond 10 ms as a proxy for asynchronous release relies on assumptions that would be good to experimentally justify. Could such signals arise from iGluSnFR saturation, or be affected by desensitization?. Moreover, the quantification of asynchronous release is based on very small signals that represent only a fraction of the already small synchronous release component, raising concerns about signal-to-noise limitations. A key issue is that failures to evoke glutamate release may arise from AP failures, such that the second response in a PPR does not necessarily represent facilitation. Given that many of the findings largely confirm existing literature, the study might have benefited from a different framing, for example, as an additional validation of the correspondence between electrophysiological measures and the authors' imaging-based readouts. Another point concerns the analysis of synaptic vesicle replenishment following depletion, which would ideally be addressed using alternative stimulation protocols, such as quantifying the response/success rate to single APs at varying time points after a train. Although the authors are appropriately cautious in their conclusions (e.g., with respect to Figure 5b), this limitation remains. Finally, the use of heterogeneous cortical neuronal cultures is likely to introduce substantial variability, as the authors themselves acknowledge, which may arise from the co-expression of multiple Ca²⁺ sensors across diverse cell types.

In summary, the authors were able to confirm previously-described changes in neurotransmission properties upon the loss of Syt7 using live imaging of glutamate release at the level of single boutons. They also present preliminary evidence for the interdependence of Syt7 function, synaptic vesicle replenishment, and the facilitation of asynchronous release, although these results will need to be substantiated in future studies using alternative stimulation protocols and complementary methodologies. Taken together with the group's prior work on synaptotagmin-1, this study illustrates that live imaging of glutamate release offers an alternative approach that recapitulates some elements detectable via electrophysiological analysis, while possibly revealing new insights into the function of synaptic proteins. As a whole, taking a live imaging approach may be a broadly accessible way forward to analyze synaptic function. The potential of studying synaptic proteins in diverse cell types that are difficult to access with patch-clamp electrophysiology is particularly compelling.

Reviewer #3 (Public review):

In this manuscript, the authors examine the role of Syt7 in the plasticity of synchronous and asynchronous release in cultured neurons. The experimental approach is the imaging of SF-iGluSnFR.A184V expressed in cultured neurons while delivering stimulation through whole-cell patch clamping of single neurons in the culture. In this manner, they could examine the optical signature of glutamate release in single presynaptic terminals, while separating the release events into synchronous (<10ms) and asynchronous (>10ms) while delivering both paired pulses or trains of stimuli (at 20 Hz, 50 ms between stimuli).

This manuscript employs techniques previously reported by the research group in their Mendoca et al., Nat Comms 2022 paper. This paper uses this approach to specifically examine the role of Syt7. The use of iGluSnFR in this manner provides significant rigor to the paper. The most significant weakness is that some of the events the authors discuss in this manuscript are rare, and the strength of the conclusions regarding those is somewhat unclear.

The main novel contribution of this manuscript is that single-bouton high-frequency imaging allowed them to examine paired-pulse plasticity in boutons that had not released neurotransmitter during the first pulse (failure-based analysis), thus separating between the effects of vesicle depletion and facilitation of the release machinery. This approach also allowed them to segregate their observations according to bouton-specific release efficacy. Both examinations are unavailable when performing cell-level analysis of neurotransmitter release, as is reported by most electrophysiological approaches.

The authors conclude that Syt7 contributes specifically to facilitation of synchronous release, not asynchronous release, while reducing the magnitude of the asynchronous component. Finally, the authors suggest segregation of synchronous and asynchronous release, either by differential use of calcium sensors or spatial segregation of the vesicles contributing to both modes of release.

This report contributes significantly to the discussion of the control of synaptic plasticity by different molecular players. It is not the first to examine Syt7, but its contribution to the examination of this protein is significant.

I find this report to be well executed and reasoned. In my opinion, the authors could improve the manuscript by clarifying the description of several methodological and experimental sections. Furthermore, in my opinion, some of the conclusions are overstated.

The authors state: "Because boutons along a single axon originate from the same presynaptic neuron, they are expected to share broadly similar molecular components of the vesicular release machinery and experience comparable presynaptic action potential waveforms." The authors should address the idea that presynaptic terminals from the same neuron on different postsynaptic targets can differ in the molecular components, as well as in the presynaptic side. There is ample evidence for differences between synapses onto glutamatergic and GABAergic neurons of the same neuron.

The authors used 4ms-long frames, but the stimuli are delivered at 20Hz (50ms apart). Therefore, in paired pulse stimulation, isn't there going to be a difference between the first and second stimuli regarding the timing of the frames relative to the stimulus? Isn't the deconvolution sensitive to such an offset?

A 10ms threshold for defining synchronous vs. asynchronous release full in-between frames. Doesn't this increase the chance of assigning borderline events to the wrong category?

On page 11 of the conclusion, the authors state that "Our data indicate that in our conditions during paired-pulse protocol Syt7 primarily enhances release probability rather than increasing the RRP size." While I understand the reasoning behind this statement, it should be toned down. The authors did not directly address the RRP size.

In failure-based analysis, the number of failure events in high-efficiency boutons is expected to be low. How does this affect the conclusions of the authors concerning the effects of Syt7 deletion on facilitation in high-efficiency boutons?<br /> SourceData.xlsx was not available to me, as far as I could tell.

How can the conclusions of the authors on the differential molecular composition of vesicles contributing to synchronous and asynchronous release be related to the reported effect of strontium on the nature of release? (see 10.1523/JNEUROSCI.20-12-04414.2000)

Is this the first use of failure-based analysis? If not, the authors should cite precedents. In 10.1016/s0896-6273(00)80338-4, failure of release during the 1st AP was presented, with facilitation during the 2nd, although no formal analysis was performed.

Reviewer #1 (Public review):

Summary:

This preprint investigates the molecular mechanism by which warm temperature induces female-to-male sex reversal in the ricefield eel (Monopterus albus), a protogynous hermaphroditic fish of significant aquacultural value in China. The study identifies Trpv4 - a temperature-sensitive Ca²⁺ channel - as a putative thermosensor linking environmental temperature to sex determination. The authors propose that Trpv4 causes Ca²⁺ influx, leading to activation of Stat3 (pStat3). pStat3 then transcriptionally upregulates the histone demethylase Kdm6b (aka Jmjd3), leading to increased dmrt1 gene expression and ovo-testes development. This work aims to bridge ecological cues with molecular and epigenetic regulators of sex change and has potential implications for sex control in aquaculture.

Strengths:

(1) This study proposes the first mechanistic pathway linking thermal cues to natural sex reversal in adult ricefield eel, extending the temperature-dependent sex determination paradigm beyond embryonic reptiles and saltwater fish

(2) The findings could have applications for aquaculture, where skewed sex ratios apparently limit breeding efficiency

Weaknesses:

Although the revised manuscript represents an improvement over the original version, substantial weaknesses remain.

Scientific Concerns

(1) Western blot normalization and exposure: The loading controls (GAPDH) in Fig. S3C appear overexposed, as do several Foxl2 blots. Because these signals are likely outside the linear range, I am not convinced that normalization is reliable. This raises concerns about the validity of the quantified results.

(2) Antibody validation and referencing (Line 776): The authors need to refer explicitly to figures demonstrating antibody validation. At present, these data are provided only as a supplementary file that is not cited in the manuscript. In addition, the Sox9a antibody appears to yield indistinguishable signals in control and RNAi conditions, suggesting that it may not recognize eel Sox9a. This issue is not addressed by the authors. Furthermore, antibody validation Western blots should be quantified.

(3) Unclear sample sizes (N values): Sample sizes remain unclear for several figures:

(a) Fig. 3F - No N value is provided. Each graph shows three data points; does this indicate that only three samples were quantified? If ten samples were collected, why were all not quantified?

(b) Fig. 4 - No N values are reported.

(c) Fig. 5A - Again, only three data points are shown per group, despite the apparent availability of twelve samples. The rationale for this discrepancy is not explained.

(4) qRT-PCR normalization: The manuscript does not specify the reference gene(s) used for qRT-PCR normalization. Although expression levels are reported as "relative," neither the identity of the reference gene(s) nor the justification for their selection is provided.

(5) Specificity of key antibodies: While the authors have made some effort to validate anti-Amh, anti-Sox9, and anti-Dmrt antibodies, the results remain incomplete. The Amh and Dmrt antibodies detect reduced protein levels following knockdown of their respective targets, which is encouraging. However, the Sox9a antibody shows no difference between control and RNAi conditions, suggesting it does not recognize eel Sox9. This is not acknowledged in the manuscript. In addition, no validation data are presented for Foxl2. Antibody validation data must be clearly referenced in the main text and presented in an interpretable and quantitative manner.

(6) Immunofluorescence data quality: The immunofluorescence images remain difficult to interpret. I strongly encourage the authors to enlarge the image panels and to present monochrome images (white signal on black background). The current presentation severely limits interpretability.

(7) Unreferenced supplementary figure: Fig. S4 is included in the submission but is not referenced anywhere in the manuscript text.

(8) Fig. 5B image resolution: The micrographs in Fig. 5B are too small to allow meaningful evaluation of the data.

(9) Unexplained data inclusion (Fig. 5E): Fig. 5E includes a pERK blot that is not mentioned in the Results section. The rationale for including these data is unclear.

(10) Poor blot quality (Fig. S3C): The blots in Fig. S3C exhibit high background and overexposure. I am concerned about the reliability of the quantification shown in panel D.

(11) Poor blot quality (Fig. S5G): The Stat3 blots in Fig. S5G contain numerous white artifacts, raising concerns about their suitability for normalization in panel H.

(12) Missing controls (Fig. 6E): Fig. 6E lacks controls for HO-3867 and Colivelin treatments alone. Without these controls, it is not possible to determine whether the reported effects are meaningful.

(13) Graphical presentation: The use of a light blue-to-pink gradient in bar graphs throughout the manuscript does not aid interpretation. I recommend using more distinct colors (e.g., red, orange, green, blue, purple, gray, black) to improve clarity. In summary, the interpretation of the study remains limited by persistent issues related to data presentation, image quality, and reagent specificity.

Reviewer #1 (Public review):

Summary:

Abdelmageed et al. investigate age-related changes in the subcellular localization of DNA polymerase kappa (POLK) in the brains of mice. POLK has been actively investigated for its role in translesion DNA synthesis and involvement in other DNA repair pathways in proliferating cells, very little is known about POLK in a tissue-specific context or let alone in post-mitotic cells. The authors investigated POLK subcellular distribution in the brains of young, middle-aged, and old mice via immunoblotting of fractioned tissue extracts and immunofluorescence (IF). Immunoblotting revealed a progressive decrease in the abundance of nuclear POLK, while cytoplasmic POLK levels concomitantly increased. Similar findings were present when IF was performed on brain sections. Further IF studies of cingulate cortex (Cg1), motor cortex (M1, M2), and somatosensory (S1) cortical regions all showed an age-related decline in nuclear POLK. Nuclear speckles of POLK decrease in each region, meanwhile the number of cytoplasmic POLK granules decreases in all four regions, but granule size is increasing. The authors report similar findings for REV1, another Y-family DNA polymerase.

The authors then investigate the colocalization of POLK with other DNA damage response (DDR) proteins in either pyramidal neurons or inhibitory interneurons. At 18 months of age, DNA damage marker gH2AX demonstrated colocalization with nuclear POLK, while strong colocalization of POLK and 8-oxo-dG was present in geriatric mice. The authors find that cytoplasmic POLK granules colocalize with stress granule marker G3BP1, suggesting that the accumulated POLK ends up in the lysosome.

Brain regions were further stained to identify POLK patterns in NeuN+ neurons, GABAergic neurons, and other non-neuronal cell types present in the cortex. Microglia associated with pyramidal neurons or inhibitory interneurons were found to have higher abundance of cytoplasmic POLK. The authors also report that POLK localization can be regulated by neuronal activity induced by Kainic acid treatment. Lastly, the authors suggest that POLK could serve as an aging clock for brain tissue, but POLK deserves further characterization and correlation to functional changes before being considered for a biomarker.

Strengths:

Investigation of TLS polymerases in specific tissues and in post-mitotic cells is largely understudied. The potential changes in sub cellular localization of POLK and potentially other TLS polymerases opens up many questions about DNA repair and damage tolerance in the brain and how it can change with age.

Weaknesses:

The work is quite novel and interesting, and the authors do suggest some potentially interesting roles for POLK in the brain, but these are in of themselves a bit speculative. The majority of the findings of this paper draw upon findings from POLK antibody and its presumed specificity for POLK. However, this antibody has not been fully validated and would benefit from further validation of the different band sizes. More mechanistic investigation is needed before POLK could be considered as a brain aging clock but does not preclude the potential for using POLK as a biological "dating" system for the brain.

Comments on revisions:

The revised manuscript is suitably improved and addresses reviewer comments.

Reviewer #2 (Public review):

Summary:

Abdelmageed et al., demonstrate POLK expression in nervous tissue and focus mainly on neurons. Here, they describe an exciting age-dependent change in POLK subcellular localization, from the nucleus in young tissue to the cytoplasm in old tissue. They argue that the cytosolic POLK associates with stress granules. They also investigate cell-type specific expression of POLK, and quantitate expression changes induced by cell autonomous (activity) and cell nonautonomous (microglia) factors.

Comments on revisions:

Do the authors have any explanation or reason for why they weren't able to achieve a higher knockdown of POLK using siRNA in Figure 1A2? It does not seem statistically different by eye, as all values in the KD overlap with the control. This does not seem like strong evidence that their antibody works.

Reviewer #1 (Public review):

Summary:

GID/CTLH-type RING ligases are huge multi-protein complexes that play an important role in protein ubiquitylation. The subunits of its core complex are distinct and form a defined structural arrangement, but there can be variations in subunit composition, such as exchange of RanBP9 and RanBP10. In this study, van gen Hassend and Schindelin provide new crystal structures of (parts of) key subunits and use those structures to elucidate the molecular details of the pairwise binding between those subunits. They identify key residues that mediate binding partner specificity. Using in vitro binding assays with purified protein, they show that altering those residues can switch specificity to a different binding partner.

Strengths:

This is a technically demanding study that sheds light on an interesting structural biology problem in residue-level detail. The combination of crystallization, structural modeling, and binding assays with purified mutant proteins is elegant and, in my eyes, convincing.

Weaknesses:

I mainly have some suggestions for further clarification, especially for a broad audience beyond the structural biology community.

(1) The authors establish what they call an 'engineering toolkit' for the controlled assembly of alternative compositions of the GID complex. The mutagenesis results are great for the specific questions asked in this manuscript. It would be great if they could elaborate on the more general significance of this 'toolkit' - is there anything from a technical point of view that can be generalized? Is there a biological interest in altering the ring composition for functional studies?

(2) Along the same lines, the mutagenesis required to rewire Twa1 binding was very complex (8 mutations). While this is impressive work, the 'big picture conclusion' from this part is not as clear as for the simpler RanBP9/10. It would be great if the authors could provide more context as to what this is useful for (e.g., potential for in vivo or in vitro functional studies, maybe even with clinical significance?)

(3) For many new crystal structures, the authors used truncated, fused, or otherwise modified versions of the proteins for technical reasons. It would be helpful if the authors could provide reasoning why those modifications are unlikely to change the conclusions of those experiments compared to the full-length proteins (which are challenging to work with for technical reasons). For instance, could the authors use folding prediction (AlphaFold) that incorporates information of their resolved structures and predicts the impact of the omitted parts of the proteins? The authors used AlphaFold for some aspects of the study, which could be expanded.

Reviewer #2 (Public review):

Summary:

This is a very interesting study focusing on a remarkable oligomerization domain, the LisH-CTLH-CRA module. The module is found in a diverse set of proteins across evolution. The present manuscript focuses on the extraordinary elaboration of this domain in GID/CTLH RING E3 ubiquitin ligases, which assemble into a gigantic, highly ordered, oval-shaped megadalton complex with strict subunit specificity. The arrangement of LisH-CTLH-CRA modules from several distinct subunits is required to form the oval on the outside of the assembly, allowing functional entities to recruit and modify substrates in the center. Although previous structures had shown that data revealed that CTLH-CRA dimerization interfaces share a conserved helical architecture, the molecular rules that govern subunit pairing have not been explored. This was a daunting task in protein biochemistry that was achieved in the present study, which defines this "assembly specificity code" at the structural and residue-specific level.

The authors used X-ray crystallography to solve high-resolution structures of mammalian CTLH-CRA domains, including RANBP9, RANBP10, TWA1, MAEA, and the heterodimeric complex between RANBP9 and MKLN. They further examined and characterized assemblies by quantitative methods (ITC and SEC-MALS) and qualitatively using nondenaturing gels. Some of their ITC measurements were particularly clever and involved competitive titrations and titrations of varying partners depending on protein behavior. The experiments allowed the authors to discover that affinities for interactions between partners is exceptionally tight, in the pM-nM range, and to distill the basis for specificity while also inferring that additional interactions beyond the LisH-CTLH-CRA modules likely also contribute to stability. Beyond discovering how the native pairings are achieved, the authors were able to use this new structural knowledge to reengineer interfaces to achieve different preferred partnerings.

Strengths:

Nearly everything about this work is exceptionally strong.

(1) The question is interesting for the native complexes, and even beyond that, has potential implications for the design of novel molecular machines.

(2) The experimental data and analyses are quantitative, rigorous, and thorough.

(3) The paper is a great read - scholarly and really interesting.

(4) The figures are exceptional in every possible way. They present very complex and intricate interactions with exquisite clarity. The authors are to be commended for outstanding use of color and color-coding throughout the study, including in cartoons to help track what was studied in what experiments. And the figures are also outstanding aesthetically.

Weaknesses:

There are no major weaknesses of note, but I can make a few recommendations for editing the text.

Reviewer #3 (Public review):

Summary:

Protein complexes, like the GID/CTLH-type E3 ligase, adopt a complex three-dimensional structure, which is of functional importance. Several domains are known to be involved in shaping the complexes. Structural information based on cryo-EM is available, but its resolution does not always provide detailed information on protein-protein interactions. The work by van gen Hassend and Schindelin provides additional structural data based on crystal structures.

Strengths:

The work is solid and very carefully performed. It provides high-resolution insights into the domain architecture, which helps to understand the protein-protein interactions on a detailed molecular level. They also include mutant data and can thereby draw conclusions on the specificity of the domain interactions. These data are probably very helpful for others who work on a functional level with protein complexes containing these domains.

Weaknesses:

The manuscript contains a lot of useful, very detailed information. This information is likely very helpful to investigate functional and regulatory aspects of the protein complexes, whose assembly relies on the LisH-CTLH-CRA modules. However, this goes beyond the scope of this manuscript.

Reviewer #1 (Public review):

Summary:

This study investigates the molecular mechanisms allowing the KSM mite to infest tea plants, a host that is toxic to the closely related TSSM mite due to high concentrations of phenolic catechins. The authors utilize a comparative approach involving tea-adapted KSM, non-adapted KSM, and TSSM to assess behavioral avoidance and physiological tolerance to catechins. The main finding is that tea-adapted KSM possesses a specific detoxification mechanism mediated by an enzyme, TkDOG15, which was acquired via horizontal gene transfer. The study demonstrates that adaptation is a two-step process: (1) structural refinement of the TkDOG15 enzyme through amino acid substitutions that enhance enzymatic efficiency against catechins, and (2) significant transcriptional upregulation of this gene in response to tea feeding. This enzymatic adaptation allows the mites to cleave and detoxify tea catechins, enabling survival on a toxic host plant.

Strengths:

A multiomics approach (transcriptomics and proteomics) provided a compelling cross-validation of its findings. Functional bioassays, such as RNAi and recombinant enzyme assays, demonstrated that the adapted mite has higher activity against catechins via TkDOG15. Other methodologies, like feeding assay using a parafilm-covered leaf disc, were effective in avoiding contact chemosensation.

Weaknesses:

Although TkDOG15 is assumed to "detoxify" catechins by ring cleavage, the study doesn't identify or characterize the breakdown metabolic products. If the metabolites are indeed non-toxic compared to the parent catechins, that would strengthen the detoxification hypothesis. Also, the transcriptomic and proteomic analyses identified other potential detoxification enzymes, such as CCEs, UGTs, and ABC (Supplementary Tables 3-1 & 3-2), which were also upregulated. The manuscript focuses almost exclusively on TkDOG15, potentially overlooking a multigenic adaptation mechanism, where these other enzymes might play synergistic roles, although it was mentioned in the discussion section.

Reviewer #2 (Public review):

Summary:

The fascinating topic of the host range of arthropods, including insects, and the detoxification of host secondary metabolites has been elucidated through studies of the host specificity of two closely related species. The discovery that key genes were acquired from fungi through horizontal gene transfer (HGT) is particularly significant.

Strengths:

(1) The discovery that the TkDOG15 enzyme, acquired through HGT from fungi, plays a key role in the detoxification of green tea catechins in the Kanzawa mite, revealing a new mechanism of plant-herbivore interactions, is highly encouraging.

(2) The verification of this finding through various experiments, including behavioral, toxicological, transcriptomic, and proteomic analyses, RNAi-based gene function analysis, and recombinant enzyme activity assays, is also highly commendable.

(3) By proposing a two-step model in which amino acid substitutions and expression regulation of a specific enzyme gene (TkDOG15) enable host adaptive evolution, this study contributes significantly to our understanding of the evolutionary mechanisms of speciation and plant defense overcoming.

Weaknesses:

While transcriptome/proteome analyses reported changes in the expression of other detoxification-related enzymes, including CCEs, UGTs, ABC transporters, DOG1, DOG4, and DOG7, it is regrettable that the contribution of each enzyme, including its interaction with TkDOG15 and the functional analysis of each enzyme within the overall catechin detoxification system, was not investigated.

Reviewer #1 (Public review):

Summary:

This manuscript presents high-resolution cryoEM structures of VPS34-complex II bound to Rab5A at 3.2A resolution. The Williams group previously reported the structure of VPS34 complex II bound to Rab5A on liposomes using tomography, and therefore, the previous structure, although very informative, was at lower resolution.

The first new structure they present is of the 'REIE>AAAA' mutant complex bound to RAB5A. The structure resembles the previously determined one, except that an additional molecule of RAB5A was observed bound to the complex in a new position, interacting with the solenoid of VPS15.

Although this second binding site exhibited reduced occupancy of RAB5A in the structure, the authors determined an additional structure in which the primary binding site was mutated to prevent RAB5A binding ('REIE>ERIR'). In this structure, there is no RAB5A bound to the primary binding site on VPS34, but the RAB5A bound to VPS15 now has strong density. The authors note that the way in which RAB5A interacts with each site is distinct, though both interfaces involve the switch regions. The authors confirm the location of this additional binding site using HDX-MS.

The authors then determine multiple structures of the wild-type complex bound to RAB5A from a single sample, as they use 3D classifications to separate out versions of the complex bound to 0, 1, or 2 copies of RAB5A. Overall, the structure of VPS34-Complex II does not change between the different states, and the data indicate that both RAB5A binding sites can be occupied at the same time.

The authors then design a new mutant form of the complex (SHMIT>DDMIE) that is expected to disrupt the interaction at the secondary site between VPS15 and RAB5A. This mutation had a minor impact on the Kd for RAB5A binding, but when combined with the REIE>ERIR mutation of the primary binding site, RAB5A binding to the complex was abolished.

Comparison of sequences across species indicated that the RAB5A binding site on VPS15 was conserved in yeast, while the RAB5A binding site on VPS34 is not.

The authors tested the impact of a corresponding yeast Vps15 mutation (SHLITY>DDLIEY) predicted to disrupt interaction with yeast Rab5/Vps21, and found that this mutant Vps15 protein was mislocalized and caused defective CPY processing.

The authors then compare these structures of the RAB5A-class II complex to recently published structures from the Hurley group of the RAB1A-class I complex, and find that in both complexes the Rab protein is bound to the VPS34 binding site in a somewhat similar manner. However, a key difference is that the position of VPS34 is slightly different in the two complexes because of the unique ATL14L and UVRAG subunits in the class I and class II complexes, respectively. This difference creates a different RAB binding pocket that explains the difference in RAB specificity between the two complexes.

Finally, the higher resolution structures enable the authors to now model portions of BECLIN1 and UVRAG that were not previously modeled in the cryoET structure.

Strengths:

Overall, I found this to be an interesting and comprehensive study of the structural basis for the interaction of RAB5A with VPS34-complex II. The authors have performed experiments to validate their structural interpretations, and they present a clear and thorough comparative analysis of the Rab binding sites in the two different VPS34 complexes. The result is a much better understanding of how two different Rab GTPases specifically recruit two different, but highly similar complexes to the membrane surface.

Weaknesses:

No significant weaknesses were noted.

Reviewer #2 (Public review):

The work by Spokaite et al describes the discovery of a novel Rab5 binding site present in complex II of class III PI3K using a combination of HDX and Cryo EM. Extensive mutational and sequence analysis define this as the primordial Rab5 interface. The data presented are convincing that this is indeed a biologically relevant interface, and is important in defining mechanistically how VPS34 complexes are regulated.

This paper is a very nice expansion of their previous cryo-ET work from 2021, and is an excellent companion piece on high-resolution cryo-EM of the complex I class III complex bound to Rab1 from the Hurley lab in 2025. Overall, this work is of excellent technical quality and answers important unexplained observations on some unexpected mutational analysis from the previous work.

They used their increased affinity VPS34 mutant to determine the 3.2 ang structure of Rab5 bound to VPS34-CII. Clear density was seen for the original Rab5 interface, but an additional site was observed. Based on this structure, they mutated out the VPS34 interface, allowing for a high-resolution structure of the Rab5 bound at the VPS15 interface.

They extensively validated the VPS15 interface in the yeast variant of VPS34, showing that the Vp215-Rab5 (VPS21) interface identified is critical in controlling complex II VPS34 recruitment.

The major strengths of this paper are that the experiments appear to be done carefully and rigorously, and I have very few experimental suggestions.

Here is what I recommend based on some very minor weaknesses I observed

(1) My main concern has to do a little bit with presentation. My main issue is how the authors use mutant description. They clearly indicate the mutant sequence in the human isoform (for example, see Figure 2A, VPS15 described as 579-SHMIT-583>DDMIE); however, when they shift to the yeast version, they shift to saying VPS15 mutant, but don't define the mutant, Figure 2G). I would recommend they just include the same sequence numbering and WT to mutant replacement every time a new mutant (or species) is described. It is always easier to interpret what is being shown when the authors are jumping between species, when the exact mutant is included. This is particularly important in this paper, where we are jumping between different subunits and different species, so a clear description in the figure/figure legends makes it much easier to read for non-specialists.

(2) The HDX data very clearly shows that Rab5 is likely able to bind at both sites, which back ups the cryo EM data nicely. I am slightly confused by some of the HDX statements described in the methods.

(3) The authors state, "Only statistically significant peptides showing a difference greater than 0.25 Da and greater than 5% for at least two timepoints were kept." This seems to be confusing as to why they required multiple timepoints, and before they also describe that they required a p-value of less than 0.05. It might be clearer to state that significant differences required a 0.25 Da, 5%, and p-value of <0.05 (n=3). Also, what do they mean by kept? Does this mean that they only fully processed the peptides with differences?

(4) They show peptide traces for a selection in the supplement, but it would be ideal to include the full set of HDX data as an Excel file, including peptides with no differences, as there is a lot of additional information (deuteration levels for everything) that would be useful to share, as recommended from the Masson et al 2019 recommendations paper. This may be attached, but this reviewer could not see an example of it in the shared data dropbox folder.

Reviewer #3 (Public review):

Summary:

The manuscript of Spokaite et al. focuses on the Vps34 complex involved in PI3P production. This complex exists in two variants, one (class I) specific for autophagy, and a second one (class II) specific for the endocytic system. Both differ only in one subunit. The authors previously showed that the Vps34 complexes interact with Rab GTPases, Rab1 or Rab5 (for class II), and the identified site was found at Vps34. Now, the authors identify a conserved and overlooked Rab5 binding site in Vps15, which is required for the function of the Class II complex. In support of this, they show cryo-EM data with a second Rab5 bound to Vps15, identify the corresponding residues, and show by mutant analysis that impaired Rab5 binding also results in defects using yeast as a model system.

Overall, this is a most complete study with little to criticize. The paper shows convincingly that the two Rab5 binding sites are required for Vps34 complex II function, with the Vps15 binding site being critical for endosomal localization. The structural data is very much complete. What I am missing are a few controls that show that the mutations in Vps15 do not affect autophagy. I also found the last paragraph of the results section a bit out of place, even though this is a nice observation that the N-terminal part of BECLIN has these domains. However, what does it add to the story?

Joint Public review:

Summary

This interesting work by Shuhao Li and colleagues suggests that developmental sleep and feeding behavior in larval flies is genetically programmed to prepare the animal for adult contingencies, such as in the case of flies living in harsh ecological environments, such as deserts. Thus, the work proposes that desert-dwelling flies such as Drosophila mojavensis sleep less and feed more than D. melanogaster as larvae, which allows them to feed less and sleep more as adults in the harsh desert conditions where they live. The authors argue that this is evidence for developmental sleep reallocation, which helps the adult flies survive in the desert. In general, their results support this compelling hypothesis, so this work provides a new perspective on how sleep might be differentially programmed across developmental stages according to the requirements of an ecological niche. This work is particularly innovative for several reasons. First, it extends the Drosophila sleep field beyond D. melanogaster and directly addresses questions about the evolution of sleep that remain largely unexplored. Second, it investigates the possibility that changes in sleep across development may be adaptive, rather than sleep being a static trait. Overall, this work opens new avenues of research, effectively bridges the fields of sleep biology and evolutionary ecology, and should be of broad interest to a general readership. The manuscript is scientifically sound and clearly written for a generalist audience.

There are, however, two important weaknesses that should be addressed. The first is the implicit assumption that all observed behavioral differences are adaptive; this would benefit from a more cautious framing. Second, the manuscript would be strengthened by a more detailed discussion, and potentially additional data, regarding the ecological differences experienced by D. mojavensis and D. melanogaster at distinct life-cycle stages.

Strengths:

(1) The study astutely uses desert Drosophila species as models to understand how sleep is optimized in a challenging environment. The manuscript is rigorous, experiments are well controlled, the work is very clearly presented, and the results support the main conclusions, which are quite exciting.

(2) The manuscript examines previously unexplored sleep differences in a non-melanogaster species.

(3) The study provides evidence that selective pressure can be restricted to specific developmental stages.

(4) This work offers evolutionary insights into the trade-offs between sleep and feeding across development.

Weaknesses

(1) The authors should soften interpretations so that it is not assumed that any observed difference between mojavensis and melanogaster is necessarily adaptive, or evolved due to food availability or temperature stress.

(2) The study relies on comparisons and correlations. While it seems likely that the observed differences in sleep explain the increased food consumption and energy storage in the larvae of desert flies, demonstrating this through sleep manipulation would strengthen the authors' conclusions.

(3) The question arises regarding whether transiently quiescent larvae are always really sleeping, and whether it is appropriate to treat sleep as a stochastic population-level phenomenon rather than as an individual trait.

(4) The manuscript would benefit from comparative analysis beyond mojavensis and melanogaster.

(5) A deeper discussion of the ecological differences between the 2 Drosophila species would place the results in a broader context.

(6) The feeding parameters used in adults and larvae measure different aspects of feeding, confounding comparisons.

Reviewer #1 (Public review):

Summary:

Despite accumulating prior studies on the expressions of AVP and AVPR1a in the brain, a detailed, gender-specific mapping of AVP/AVPR1a neuronal nodes has been lacking. Using RNAscope, a cutting-edge technology that detects single RNA transcripts, the authors created a comprehensive neuroanatomical atlas of Avp and Avpr1a in male and female brains.

Strengths:

This well-executed study provides valuable new insights into gender differences in the distribution of Avp and Avpr1a. The atlas is an important resource for the neuroscience community.

The authors have adequately addressed all of my concerns. I have no further questions or concerns.

Reviewer #2 (Public review):

Summary:

The authors conducted a brain-wide survey of Avp (arginine vasopressin) and its Avpr1a gene expression in the mouse brain using RNAscope, a high-resolution in situ hybridization method. Overall, the findings are useful and important because they identify brain regions that express the Avpr1a transcript. A comprehensive overview of Avpr1a expression in the mouse brain could be highly informative and impactful. The authors used RNAscope (a proprietary in situ hybridization method) to assess transcript abundance of Avp and one of its receptors, Avpr1a. The finding of Avp-expressing cells outside the hypothalamus and the extended amygdala is novel and is nicely demonstrated by new photomicrographs in the revised manuscript. The Avpr1a data suggest expression in numerous brain regions. In the revised manuscript, reworked figures make the data easier to interpret.

Strengths:

A survey of Avpr1a expression in the mouse brain is an important tool for exploring vasopressin function in the mammalian brain and for developing hypotheses about cell- and circuit-level function.

Future considerations:

The work contained in the manuscript is substantial and informative. Some questions remain and would be addressed in the current manuscript. How many cells are impacted? Are transcripts spread across many cells or only present in a few cells? Is density evenly distributed through a brain region or compacted into a subfield?

Reviewer #1 (Public review):

Summary:

In this manuscript, the authors describe the generation of a Drosophila model of RVCL-S by disrupting the fly TREX1 ortholog cg3165 and by expressing human TREX1 transgenes (WT and the RVCL-S-associated V235Gfs variant). They evaluate organismal phenotypes using OCT-based cardiac imaging, climbing assays, and lifespan analysis. The authors show that loss of cg3165 compromises heart performance and locomotion, and that expression of human TREX1 partially rescues these phenotypes. They further report modest differences between WT and mutant hTREX1 under overexpression conditions. The study aims to establish Drosophila as an in vivo model for RVCL-S biology and future therapeutic testing.

Strengths:

(1) The manuscript addresses an understudied monogenic vascular disease where animal models are scarce.

(2) The use of OCT imaging to quantify fly cardiac performance is technically strong and may be useful for broader applications.

(3) The authors generated both cg3165 null mutants and humanized transgenes at a defined genomic landing site.

(4) The study provided initial in vivo evidence that human TREX1 truncation variants can induce functional impairments in flies.

Weaknesses:

(1) Limited mechanistic insight.

RVCL-S pathogenesis is strongly linked to mislocalization of truncated TREX1, DNA damage accumulation, and endothelial/podocyte cellular senescence. The current manuscript does not examine any cellular, molecular, or mechanistic readouts - e.g. DNA damage markers, TREX1 subcellular localization in fly tissues, oxidative stress, apoptosis, or senescence-related pathways. As a result, the model remains largely phenotypic and descriptive.

To strengthen the impact, the authors should provide at least one mechanistic assay demonstrating that the humanized TREX1 variants induce expected molecular consequences in vivo.

(2) The distinction between WT and RVCL-S TREX1 variants is modest.

In the cg3165 rescue experiments, the authors do not observe differences between hTREX1 and the V235Gfs variant (e.g., Figure 3A-B). Phenotypic differences only emerge under ubiquitous overexpression, raising two issues:

(i) It is unclear whether these differences reflect disease-relevant biology or artifacts of strong Act5C-driven expression.

(ii) The authors conclude that the model captures RVCL-S pathogenicity, yet the data do not robustly separate WT from mutant TREX1 under physiological expression levels.

The authors should clarify these limitations and consider additional data or explanations to support the claim that the model distinguishes WT vs RVCL-S variants.

(3) Heart phenotypes are presented as vascular defects without sufficient justification.

RVCL-S is a small-vessel vasculopathy, but the Drosophila heart is a contractile tube without an endothelial lining. The authors refer to "vascular integrity restoration," but the Drosophila heart lacks vasculature.

The manuscript would benefit from careful wording and from a discussion of how the fly heart phenotypes relate to RVCL-S microvascular pathology.

(4) General absence of tissue-level or cellular imaging.

No images of fly hearts, brains, eyes, or other tissues are shown. TREX1 nuclear mislocalization is a hallmark of RVCL-S, yet no localization studies are included in this manuscript.

Adding one or two imaging experiments demonstrating TREX1 localization or tissue pathology would greatly enhance confidence in the model.

Reviewer #2 (Public review):

Summary:

The authors used the Drosophila heart tube to model Retinal vasculopathy with the goal of building a model that could be used to identify druggable targets and for testing chemical compounds that might target the disease. They generated flies expressing human TREX1 as well as a line expressing the V235G mutation that causes a C-terminal truncation that has been linked to the disease. In humans, this mutation is dominant. Heart tube function was monitored using OCM; the most robust change upon overexpression of wild-type or mutant TREX1was heart tube restriction, and this effect was similar for both forms of TREX1. Lifespan and climbing assays did show differential effects between wt and mutant forms when they were strongly and ubiquitously expressed by an actin-Gal4 driver. Unfortunately, these types of assays are less useful as drug screening tools. Their conclusion that the primary effect of TREX is on neuronal function is inferential and not directly supported by the data.

Strengths:

The authors do not show that CG3165 is normally expressed in the heart. Further fly heart tube function was similarly restricted in response to expression of either wild-type or mutant TREX1. The fact that expression of any form of human TREX1 had deleterious effects on heart function suggests that TREX1 serves different roles in flies compared to humans. Thus, in the case of this gene, it may not be a useful model to use to identify targets or use it as a drug screening tool.

The significant effects on lifespan and climbing that did show differential effects required ubiquitous overexpression using an actin-gal4 driver that does not allow the identification of tissue-specific effects. Thus, their assertion that the results suggested a strong positive correlation between Drosophila neuromotor regulation and transgenic hTREX1 presence and a negative impact from hTREX1 V235G" is not supported by these data. Also worrisome was the inability to identify the mutant TREX1 protein by Western blot despite the enhanced expression levels suggested by qPCR analysis. Mutant TREX1 cannot exert a dominant effect on cell function if it isn't present.

There are also some technical problems. The lifespan assays lack important controls, and the climbing assays do not appear to have been performed correctly. It is unclear what the WT genetic background is in Figure 1-3, so it is unclear if the appropriate controls have been used. Finally, the lack of information on the specific statistical analyses used for each graph makes it difficult to judge the significance of the data. Overall, the current findings establish the Retinal vasculopathy disease model platform, but with only incremental new data and without any mechanistic insights.

Reviewer #1 (Public review):

Summary:

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.

Strengths:

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.

Weaknesses:

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 importance 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 might be considered. For example, 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.

Reviewer #2 (Public review):

Summary:

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 in wake bout number, while males show a gene effect. Similarly, gene effects on NREM bout number seem 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:

The weaknesses are summarized below and are viewed as "addressable".

(1) The term insomnia. Insomnia is defined as a subjective dissatisfaction with sleep, which 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. It 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.

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 the 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, the quantification, and the figure presentation could be substantially improved. I detail some of my concerns below.

Strengths:

The 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.

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 of the accuracy and interpretability of 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, a point to note is that this finding is not new.

Figure 3 heatmaps lack color bars and units. 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 a cooler color (not clear what range and what the interpretation is) mean shorter sleep bout in female mice? The authors should clearly mark the frequency ranges that support their claims. In this figure, there is a question mark following the theta/delta range. The authors should avoid speculation and state their claims based on facts. They should 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 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 is known to have synchronous theta-gamma relationships.

Reviewer #1 (Public review):

While the revised manuscript includes additional methodological details and a supplementary comparison with conventional NMF, it would be great if the authors could add the point below as limitations in the manuscript or change the title and abstract accordingly, since core issues remain:

(1) The study claims to evaluate rehabilitation outcomes without demonstrating that patients actually improved functionally

(2) The comparison with existing methods lacks the quantitative rigor needed to establish superiority

(3) The added value of this complex framework over much simpler alternatives has not been demonstrated

The strength of evidence supporting the main claims remains incomplete. I would encourage the authors to consider discussing these points

(1) including or adding a limitation section about functional outcome measures that go beyond clinical scale scores, (2) providing/discussing quantitative benchmarks showing their method outperforms alternatives on specific, predefined metrics, and (3) clarifying the clinical pathway by which these biomarkers would inform treatment decisions.

There are specific, relatively minor points, that require attention

The authors write: "we did not focus on such complementary evidence in this study." This is a weakness for a paper claiming to provide "biomarkers of therapeutic responsiveness." The FMA-UE threshold defines responders, but there's no independent validation that patients actually functioned better in daily life. Can you please clarify?

Maybe I missed the exact point about this, but with the added NMF plot, the authors list 'lower dimensionality' among their framework's advantages, but the basis for this claim is not clear because given that 12 network components were extracted compared to 11 "conventional" synergies. Can you please clarify, as it is not clear. You claim 'lower dimensionality' as an advantage of the proposed framework (in the Supplementary Materials), yet you extracted 12 components (5 redundant + 7 synergistic networks) compared to 11 synergies from the conventional NMF approach, which does not support a clinical / outcome advantage of this method. Please clarify.

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.

I thank the authors for improving the clarity of the Methods section; the newly added Figure 5 is very helpful.

One minor suggestion is that the authors should avoid overloading the notation "m" for both the EEG measurement and the matrix of II values (Eq. 1.1), which I now realise was the source of some of my initial confusion. I suggest that the authors use separate notation for these two quantities.

Reviewer #1 (Public review):

Summary:

The study by Wu et al. uses endogenous bruchpilot expression in a cell-type-specific manner to assess synaptic heterogeneity in adult Drosophila melanogaster mushroom body output neurons. The authors performed genomic on locus tagging of the presynaptic scaffold protein bruchpilot (brp) with one part of splitGFP (GFP11) using the CRISPR/Cas9 methodology and co-expressed the other part of splitGFP (GFP1-10) using the GAL4/UAS system. Upon expression of both parts of splitGFP, fluorescent GFP is assembled at the C-terminus of brp, exactly where brp is endogenously expressed in active zones. For manageable analysis, a high-throughput pipeline was developed. This analysis evaluated parameters like location of brp clusters, volume of clusters, and cluster intensity as a direct measure of the relative amount of brp expression levels on site using publicly available 3D analysis tools that are integrated in Fiji. Analysis was conducted for different mushroom body cell types in different mushroom body lobes using various specific GAL4 drivers. Further validation was provided by extending analysis to R8 photoreceptors that reside in the fly medulla. To test this new method of synapse assessment, Wu et al. performed an associative learning experiment in which an odor was paired with an aversive stimulus and found that in a specific time frame after conditioning, the new analysis solidly revealed changes in brp levels at specific synapses that are associated with aversive learning. Additionally, brp levels were assessed in R8 photoreceptor terminals upon extended exposure to light.

Strengths:

Expression of splitGFP bound to brp enables intensity analysis of brp expression levels as exactly one GFP molecule is expressed per brp. This is a great tool for synapse assessment. This tool can be widely used for any synapse as long as driver lines are available to co-express the other part of splitGFP in a cell-type-specific manner. As neuropils and thus brp label can be extremely dense, the analysis pipeline developed here is very useful and important. The authors have chosen an exceptionally dense neuropil - the mushroom bodies - for their analysis and compellingly show that brp assessment can be achieved even with such densely packed active zones. The result that brp levels change upon associative learning in an experiment with odor presentation paired with punishment is likewise compelling and strongly suggests that the tool and pipeline developed here can be used in an in vivo context. Thus, the tool and its uses have the potential to fundamentally advance protein analysis not only at the synapse but especially there.

Weaknesses:

The weaknesses I perceived originally were satisfactorily explained and refuted.

Reviewer #2 (Public review):

Summary:

The authors developed a cell-type-specific fluorescence-tagging approach using a CRISPR/Cas9 induced spilt-GFP reconstitution system to visualize endogenous Bruchpilot (BRP) clusters at presynaptic active zones (AZ) in specific cell types of the mushroom body (MB) in the adult Drosophila brain. This AZ profiling approach was implemented in a high-throughput quantification process allowing to compare synapse profiles within single cells, cell-types, MB compartments and between different individuals. Aim is to in more detail analyze neuronal connectivity and circuits in this center of associative learning, notoriously difficult to investigate due to the density of cells and structures within the cells. The authors detect and characterize cell-type specific differences in BRP-dependent profiling of presynapses in different compartments of the MB, while intracellular AZ distribution was found to be stereotyped. Next to the descriptive part characterizing various AZ profiles in the MB, the authors apply an associative learning assay and Rab3 knock-down and detected consequent AZ reorganization.

Strengths:

The strength of this study lies in the outstanding resolution of synapse profiling in the extremely dense compartments of the MB. This detailed analysis will serve as an entry point for many future studies of synapse diversity in connection with functional specificity to uncover the molecular mechanisms underlying learning and memory formation and neuronal network logic. Therefore, this approach is of high importance to the scientific community and represents a valuable tool to investigate and correlate AZ architecture and synapse function in the CNS.

Weaknesses:

The results and conclusions presented in this study are conclusively and well supported by the data presented and appropriate controls. As a comment that could possibly aid and strengthen the manuscript (but not required for acceptance of the manuscript): The experiments in the study are based on spilt-GFP lines (BRP:GFP11 and UAS-GFP1-10). The authors clearly validate the new on-locus construct with a genomic GFP insertion (qPCR, confocal and STED imaging of the brain with anti-BRP (Nc82), MB morphology and memory formation). It would be important to comment on the significant overall intensity decrease of anti-BRP (Nc82) in Fig. S1B (R57C10>BRP::rGFP) and possibly a Western Blot with a correlative antibody staining against BRP might help to show that BRP protein level are not affected. Additionally, it would be important to state, at least in the Materials and Methods section, that the flies are not homozygous viable (and to offer an explanation) and to state that all experiments were performed with heterozygous flies.

Reviewer #3 (Public review):

Summary:

The authors develop a tool for marking presynaptic active zones in Drosophila brains, dependent on the GAL4 construct used to express a fragment of GFP, which will incorporate with a genome-engineered partial GFP attached to the active zone protein bruchpilot - signal will be specific to the GAL4 expressing neuronal compartment. They then use various GAL4s to examine innervation onto the mushroom bodies to dissect compartment specific differences in the size and intensity of active zones. After a description of these differences, they induce learning in flies with classic odour/electric shock pairing and observe changes after conditioning that are specific to the paired conditioning/learning paradigm.

Strengths:

The imaging and analysis appears strong. The tool is novel and exciting.

Weaknesses:

I feel that the tool could do with a little more characterisation. It is assumed that the puncta observed are AZs with no further definition or characterisation. It is not resolved if the AZs visualised here simply tagged, or are the constructs incorporated to be an active functional part of the AZ.

Comments on revisions:

Apologies, I should have thought of this in the first round of review. An experiment I would suggest (and it is not a difficult one) to address the functionality of the marker: It is mentioned that the genetically tagged half of the construct is homozygous lethal. Can this be placed in trans to a brp null, with a neuronal UAS-expression of the other half of Brp-GFP - Are the animals then 1) alive, and 2) able to fly (brp mutants can't fly, hence the name 'crashpilot') - a rescue would suggest (and that is all that would be needed here) that the reconstituted brp-GFP has function.

On another note, the paper keeps switching between different DAN-GAL4 lines. In 1H, 2Band 4A, there are informative cartoons showing the extension of the neurons for PPL1, APL and DPM neurons - could these be incorporated into figures 5, 6 and 7, and the supplementary figures to help orient the reader. Ideally they would refer to a figure (in Fig 1?) -to refer to the groups of DANs in the adult brain that are known to innervate the MBs (e.g. Fig1 in Mao and Davis, Front in Neural Circuits 2009). I suggest this because I feel that this tool will be widely used, and if non-MB aficionados can follow what's being done here I feel it will be more widely accepted.

Reviewer #1 (Public review):

Summary:

This study focuses on characterizing the EEG correlates of item-specific proportion congruency effects. Two types of learned associations are characterized, one being associations between stimulus features and control states (SC), and the other being stimulus features and responses (SR). Decoding methods are used to identify time-resolved SC and SR correlates, which are used to test properties of their dynamics.

The conclusion is reached that SC and SR associations can independently and simultaneously guide behavior. This conclusion is based on results showing SC and SR correlates are: (1) not entirely overlapping in cross-decoding; (2) simultaneously observed on average over trials in overlapping time bins; (3) independently correlate with RT; and (4) have a positive within-trial correlation.

Strengths:

Fearless, creative use of EEG decoding to test tricky hypotheses regarding latent associations.

Nice idea to orthogonalize ISPC condition (MC/MI) from stimulus features.

Weaknesses:

I still have my concern from the first round that the decoders are overfit to temporally structured noise. As I wrote before, the SC and SR classes are highly confounded with phase (chunk of session). I do not see how the control analyses conducted in the revision adequately deal with this issue.

In the figures, there are several hints that these decoders are biased. Unfortunately, the figures are also constructed in such a way that hides or diminishes the salience of the clues of bias. This bias and lack of transparency discourage trust in the methods and results.

I have two main suggestions:

(1) Run a new experiment with a design that properly supports this question.

I don't make this suggestion lightly, and I understand that it may not be feasible to implement given constraints; but I feel that this suggestion is warranted. The desired inferences rely on successful identification of SC and SR representations. Solidly identifying SC and SR representations necessitates an experimental design wherein these variables are sufficiently orthogonalized, within-subject, from temporally structured noise. The experimental design reported in this paper unfortunately does not meet this bar, in my opinion (and the opinion of a colleague I solicited).

An adequate design would have enough phases to properly support "cross-phase" cross-validation. Deconfounding temporal noise is a basic requirement for decoding analyses of EEG and fMRI data (see e.g., leave-one-run-out CV that is effectively necessary in fMRI; in my experience, EEG is not much different, when the decoded classes are blocked in time, as here). In a journal with a typical acceptance-based review process, this would be grounds for rejection.

Please note that this issue of decoder bias would seem to weaken the rest of the downstream analyses that are based on the decoded values. For instance, if the decoders are biased, in the within-trial correlation analysis, how can we be sure that co-fluctuations along certain dimensions within their projected values are driven by signal or noise? A similar issue clouds the LMM decoding-RT correlations.

(2) Increase transparency in the reporting of results throughout main text.

Please do not truncate stimulus-aligned timecourses at time=0. Displaying the baseline period is very useful to identify bias, that is, to verify that stimulus-dependent conditions cannot be decoded pre-stimulus. Bias is most expected to be revealed in the baseline interval when the data are NOT baseline-corrected, which is why I previously asked to see the results omitting baseline correction. (But also note that if the decoders are biased, baseline-correcting would not remove this bias; instead, it would spread it across the rest of the epoch, while the baseline interval would, on average, be centered at zero.)

Please use a more standard p-value correction threshold, rather than Bonferroni-corrected p<0.001. This threshold is unusually conservative for this type of study. And yet, despite this conservativeness, stimulus-evoked information can be decoded from nearly every time bin, including at t=0. This does not encourage trust in the accuracy of these p-values. Instead, I suggest using permutation-based cluster correction, with corrected p<0.05. This is much more standard and would therefore allow for better comparison to many other studies.

I don't think these things should be done as control analyses, tucked away in the supplemental materials, but instead should be done as a part of the figures in the main text -- including decoding, RSA, cross-trial correlations, and RT correlations.

Other issues:

Regarding the analysis of the within-trial correlation of RSA betas, and "Cai 2019" bias:

The correction that authors perform in the revision -- estimating the correlation within the baseline time interval and subtracting this estimate from subsequent timepoints -- assumes that the "Cai 2019" bias is stationary. This is a fairly strong assumption, however, as this bias depends not only on the design matrix, but also on the structure of the noise (see the Cai paper), which can be non-stationary. No data were provided in support of stationarity. It seems safer and potentially more realistic to assume non-stationarity.

This analysis was included in the supplemental material. However, given that the correlation analysis presented in the Results is subject to the "Cai 2019" bias, it would seem to be more appropriate to replace that analysis, rather than supplement it.

Regardless, this seems to be a moot issue, given that the underlying decoders seem to be overfit to temporally structured noise (see point above regarding weakening of downstream analyses based on decoder bias).

Outliers and t-values:

More outliers with beta coefficients could be because the original SD estimates from the t-values are influenced more by extreme values. When you use a threshold on the median absolute deviation instead of mean +/-SD, do you still get more outliers with beta coefficients vs t-values?

Random slopes:

Were random slopes (by subject) for all within-subject variables included in the LMMs? If not, please include them, and report this in the Methods.

Reviewer #2 (Public review):

Summary:

In this EEG study, Huang et al. investigated the relative contribution of two accounts to the process of conflict control, namely the stimulus-control association (SC), which refers to the phenomenon that the ratio of congruent vs. incongruent trials affects the overall control demands, and the stimulus-response association (SR), stating that the frequency of stimulus-response pairings can also impact the level of control. The authors extended the Stroop task with novel manipulation of item congruencies across blocks in order to test whether both types of information are encoded and related to behaviour. Using decoding and RSA they showed that the SC and SR representations were concurrently present in voltage signals and they also positively co-varied. In addition, the variability in both of their strengths was predictive of reaction time. In general, the experiment has a sold design and the analyses are appropriate for the research questions.

Strength:

(1) The authors used an interesting task design that extended the classic Stroop paradigm and is effective in teasing apart the relative contribution of the two different accounts regarding item-specific proportion congruency effect.

(2) Linking the strength of RSA scores with behavioural measure is critical to demonstrating the functional significance of the task representations in question.

Weakness:

(1) The distinction between Phase 2 and Phase 1&3 behavioral results, specifically the opposite effect of MC/MI in congruent trials raises some concerns with regard to the effectiveness of the ISPC manipulation. Why do RTs and error rates under MC congruent condition in Phase 2 seem to be worse than MI congruent? Could there be other factors at play here, e.g. order effect? How does this potentially affect the neural analyses where trials from different phases were combined? Also, the manuscript does not mention whether there is counterbalancing for the color groups across participants, so far as I can tell.

Reviewer #1 (Public review):

Summary:

Using high-precision eyetracking, the authors measure foveolar sensitivity modulations before, during, and after instructed microsaccades to a centrally cued orientation stimulus.

Strengths:

The article is clearly written, and the stimulus presentation method is sophisticated and well-established. The data provide interesting insights that will be useful for comparisons between trans-saccadic and trans-microsaccadic sensitivity modulations.

Weaknesses:

Nonetheless, I have major concerns regarding the interpretation of the measured time courses (in particular, inconsistencies in distinguishing enhancement from suppression), the attempt to disentangle these effects from endogenous attention shifts, and the overstatement of the findings' novelty.

(1) Overstatement of novelty

The authors motivate their study by stating that "the temporal dynamics of these pre-microsaccadic modulations remain unknown" (l. 55-56). However, Shelchkova & Poletti (2020) already report a microsaccade-aligned sensitivity time course. I understand that the present study uses shorter target durations and thus provides a more resolved estimate. Nonetheless, a fairer characterization of the study's novelty would be that observers' discrimination performance is continuously measured across the pre-, intra-, and post-movement interval, within the same observers and experimental design. Relatedly, the authors state that it is unclear whether pre-microsaccadic sensitivity modulations reflect "suppression at the non-foveated location, enhancement at the microsaccade target, or both" (l. 70). Guzhang et al. (2024) examined the spatial spread of pre-microsaccadic sensitivity modulations by measuring performance at the PRL, the movement target, and several other equidistant locations. They report that "whereas fine spatial vision is enhanced at the microsaccade goal location, it drops at the very center of gaze". The current authors' reasoning seems to be that performances at locations that are neither the target nor the PRL may behave differently. Why would that be the case? If my understanding is correct, I would recommend incorporating these clarifications into the motivation paragraph, so that readers less familiar with the literature do not overestimate the novelty of the findings. Moreover, and related to point 3, I am unsure if the current analyses provide decisive evidence to distinguish enhancement from suppression, as claimed by the authors.

(2) Distinction from endogenous attention

To "rule out the possible influence of covert attention" (l. 232), the authors compute a cue-aligned in addition to the movement-aligned performance time course. A difference in alignment cannot rule out the influence of a certain mechanism; it can only dilute it. Just like endogenous attention may contribute to the movement-aligned time course, movement preparation will necessarily contribute to the cue-aligned time course, since these timelines are intrinsically correlated: as the trial progresses, observers will be in later and later stages of saccade preparation. For this and several additional reasons, an effect in the cue-aligned time course is in fact expected-and, in my view, clearly present (see below). As the authors themselves note, endogenous attention has been shown to operate within the foveola and should therefore be engaged in the present experiment in addition to movement-related attentional shifts (unless the authors believe that specific design features, e.g., stimulus timing, preclude its involvement?). Regardless of the theoretical considerations, the empirical data show a pronounced, near-linear increase in performance at the target location, with d′ doubling from approximately 1 to 2. Although the interaction between condition and time does not reach significance (p = 0.09), this result should not be taken as conclusive evidence against a plausible and perhaps expected contribution of endogenous attention. I suggest an additional analysis that could more directly address these issues. In previous work (Rolfs & Carrasco, 2012; Kroell & Rolfs, 2025; see Figure 3), the relative contributions of cue-alinged influences and pre-saccadic attention were disentangled by reweighting each data point according to its position on both the cue-locked and saccade-locked timelines. Applied to the present study, the authors could compute, for each cue-to-target offset bin, its proportional contribution to each pre-movement time bin. Microsaccade-locked sensitivities could then be reweighted based on these proportions. As a result, each movement-locked time bin would contain equal contributions from all cue-locked time bins, effectively isolating the effect of microsaccade preparation.

(3) Interpretation and analysis of the time course

(3.1) Discrimination before microsaccade onset<br /> In lines 151-153, the author state "While the enhancement at the target location did not reach significance relative to baseline, the impairment at the non-target location did", suggesting that pre-movement sensitivity advantages for information presented at the target location are due to a decrease in performance at the non-target location and not an enhancement at the target location per se. After analyzing the difference between the two locations, the authors state, "These results show that approximately 100 milliseconds before microsaccade onset, discrimination rapidly improved at the intended target location while decreasing at the non-target location." (l. 159-161). How is the statement that discrimination performance rapidly improved (which is repeated throughout the manuscript) justified by the results?

More generally, the authors may benefit from applying bootstrapping or permutation-based analyses to their data. Such approaches would, for example, allow direct comparisons between congruent and incongruent conditions at every individual time point in Figure 3B and may be more sensitive to temporally confined sensitivity variations while requiring fewer assumptions than analyses based on manually segregated temporal bins and aggregate measures. If enhancement at the target location does not reach significance even in these analyses, all corresponding statements should be removed throughout the manuscript. The term "enhancement" should then be rephrased as "detection advantage" or "relative performance benefit" to emphasize the contrast to enhancement effects classically associated with pre-saccadic attention shifts.

Relatedly, the authors state that pre-microsaccadic enhancement peaks around 70 ms before microsaccade onset, which is earlier than sensitivity enhancements preceding large-scale saccades that often increase monotonically up until movement onset. The authors suggest potential reasons for this in the Discussion, yet an additional one seems conceivable based on Figure 3B. Performances at both the cue-congruent and incongruent location decrease leading up to the movement, reaching values even below their early baselines around 100 ms and 25 ms before movement onset for the incongruent and congruent location, respectively. A spatially non-specific decline that drives sensitivities toward a common absolute minimum may thus dictate the time course of detection advantages. In other words, a spatially widespread decrease in foveolar sensitivity likely contributes to both "suppression" at the non-target location and the decrease in "enhancement" at the target location. If this general decrease is due to saccadic suppression, as the authors suggest, it appears to exert a much more pronounced influence on sensitivity modulations than it does before large-scale saccades (which is interesting). Are there other findings suggesting an increased magnitude of micro-saccadic (as compared to saccadic) suppression? Another potentially related phenomenon is the decrease in pre-saccadic foveal detection performances reported twice before (Hanning & Deubel, 2022; Kroell & Rolfs, 2022). It is possible that whatever mechanism triggers this decrease is engaged by the preparation of microsaccadic and saccadic motor programs alike. In any case, I would ask the authors to acknowledge this general decrease early on to clarify that any currently significant advantage for the target location relies on varied degrees of suppression, and not on true enhancement similar to pre-saccadic attention shifts.

Moreover, in Figure 3C, the final 25 ms before microsaccade onset are excluded from the aggregate measure, presumably since including this interval substantially reduces the effect size. Since the last 25 ms before movement onset is the interval most commonly associated with saccadic suppression, I think that this choice can be justified. Nonetheless, it should be mentioned explicitly in the main text. On a minor note, the authors state that "Performance (evaluated as percent of correct responses) was averaged within a 50 millisecond sliding window, advancing in 1 ms steps (with 24 ms overlap)". Why is the overlap not 49 ms?

(3.2) Discrimination during the microsaccade:<br /> The authors state that "in the "during" trials the target must be presented during the peak speed of the microsaccade." Since the target was presented for 50 ms and the average microsaccade duration was around 60 ms, this implies that the intra-microsaccadic condition includes many trials in which the target overlapped with the pre- or post-movement fixation interval. Were there not enough trials to isolate purely intra-microsaccadic presentations? Are the results descriptively comparable?

(4) Additional analyses

Several additional analyses could strengthen the authors' conclusions. If there are enough trials in which observers erroneously saccaded to the uncued (i.e., wrong) location, these trials could experimentally isolate the influence of pre-microsaccadic attention, assuming that endogenous attention went to the cued location. In addition, the authors speculate whether differences in saccadic and microsaccadic movement latencies may underlie the differences in perceptual time courses. The latency distributions provided in the manuscript look sufficiently broad, such that intra-individual variation could be harnessed to explore this question. Do sensitivity time courses differ before microsaccades with shorter vs. longer latencies?

(5) Clarifications regarding the design

At 50 ms, the duration of the to-be discriminated stimulus, although shorter than in previous investigations, is still rather long. What is the reason for this? I would encourage the authors to state in the main text that the duration of the analyzed/plotted time bins is often shorter than the stimulus duration (i.e., there is some overlap between bins that likely introduces smoothing). In Figure 3A, it would be helpful to plot raw data points computed from non-overlapping bins on top of the moving-window estimates, to allow readers to assess the degree of smoothing and potential temporal delays introduced by this analysis. Moreover, I wonder whether the abrupt onset of the target unmasked by flickering noise masks might induce saccadic inhibition, which would manifest as a transient dip in saccade execution probability. The distributions shown in Figure 2B appear too smoothed or fitted to clearly reveal such a dip. How exactly are all distributions in the manuscript computed (e.g., binning, smoothing, fitting procedures)? Finally, on a minor note, explicitly stating on line 105 that two different orientations can be presented at the cued and non-cued location would help avoid potential confusion.

Reviewer #2 (Public review):

Summary and overall evaluation:

The authors assessed how visual discrimination of stimuli in the foveola changes before, during, and after small instructed eye movements (in the "micro" range). Consistent with (and advancing) related prior work, their main finding regards a pre-saccadic modulation of visual performance at the saccade target vs. the opposite location. This pre-saccadic modulation in foveal vision peaks ~70 ms prior to the instructed small saccade.

Strengths:

The study uses an impressive, technically advanced set-up and zooms in on peri-saccadic modulations in visual acuity at the micro scale. The findings build on related prior findings from the literature on smaller and larger eye movements and add temporal granularity over prior work from the same lab. The writing is easy to follow, and the figures are clear.

Weaknesses:

At the same time, the findings remain relatively empirical in nature and do not profoundly advance theoretical understanding beyond adding valuable granularity to existing knowledge. Relevant prior literature could be better introduced and acknowledged. In addition, there remain concerns regarding potential cue-driven attentional influences that may confound the reported effects (leaving the possibility that the reported effects may be related to cue-driven attention, rather than saccade planning/execution per se). There are also some issues regarding specific statistical inferences. I detail these points below.

Major Points:

(1) Novelty framing and introduction of relevant prior literature

At times, this study is introduced as if no prior study explored the time course of changes in visual perception surrounding small (micro) saccades. Yet, it appears that a prior study from the same lab, using a very similar task, already showed a time course (Figure 5 in Shelchkova & Poletti, 2020). While this study is discussed in the introduction, it is not mentioned that at least some pre-saccade time course was already reported there, albeit a more crude one than the one in the current article. Moreover, the 2013 study by Hafed also specifically looked at "peri-microsaccade modulation in visual perception" and also already showed a temporal modulation that peaked ~50 ms before microsaccade onset. I appreciate how the current study differs in a number of ways (focusing on visual acuity in the foveola), but I was nevertheless surprised to see the first reference to this relevant prior finding in the discussion (and without any elaboration). Though more recent, the same could be argued for the 2025 study by Bouhnik et al. on pre-microsaccade modulations in visual processing in V1, which, like the Hafed study, is first mentioned only in the discussion. Perhaps these studies could be introduced in the paragraph starting at line 48, or in the next paragraph, to do better justice to the existing literature on this topic when motivating the study. This would likely also help to better point out the major advances provided by the current study.

Relatedly, in Shelchkova & Poletti (PNAS, 2020), an apparently similar congruency effect on performance was reported >200 ms milliseconds before saccade onset, as evident from Fig 5 in that article. How should readers rhyme this with the current findings? Ideally, the authors would not only acknowledge that such a time course was already reported previously, but also discuss the discrepancies between these findings further: why may the performance effects appear much earlier in this prior study compared to in the current study, where the congruency effect emerges only ~100 ms prior to the instructed small saccade?

(2) Saccade- or cue-driven? (assumption that attention is unaltered in failed saccade trials)

Because the authors used a cue to instruct saccade direction, it remains a possibility that the reported modulations in visual performance may be driven directly by the spatial cue (cue-related attentional allocation), rather than the instructed small saccade per se. While the authors are clearly aware of this potential confound, questions remain regarding the convincingness of the presented control analyses. In my view, a more compelling control would require an additional experiment.

The central argument against a cue-locked (purely attentional) modulation is the absence of a performance modulation in so-called "failed" saccade trials. However, a key assumption here is that putative cue-driven attention was unaltered in these trials. This is never verified and, in my opinion, highly unlikely. Rather, trials with failed microsaccades could very well be the result of failing to process the cue in the first place (indeed, if the task is to make a saccade to the cue, failure to make a saccade equates failure to perform the task). In such trials, any putative cue-driven influences over spatial attention would also be expected to be substantially reduced. Accordingly, just because failed saccade trials show little performance modulation does not rule out cue-driven attention effects, because attention may also have "failed" in these failed saccade trials. The control for potential cue-driven attention effects would be more convincing if the authors included a condition with the same cues, where participants are simply not instructed to make any saccades to the cues. Unfortunately, such an experimental condition appears not to have been included here. The author may still consider adding such a control experiment.

Another argument against a cue-driven effect is that the authors found no interaction with time in the cue-locked data, whereas they did find such an interaction in the saccade-locked data. However, the lack of significance in the cue-locked data but significance in the saccade-locked data is not strong evidence against a cue-driven influence. Statistically, there is no direct comparison here, and more importantly, with longer delays, the cue-locked data may also start to show a dip (this could potentially be tested by the authors if they have enough trials available to extend their cue-locked analysis further in time). Indeed, exogenous attention, that may have been automatically evoked by the spatial cue, is known to be transient and to eventually even reverse after a brief initial facilitation (see e.g., Klein TiCS, 2000).

Finally, the authors consistently refer to "endogenous" attention (starting at line 221) when addressing potential cue-driven attention confounds. However, because the cue is not predictive, but is a spatial cue that differs in a bottom-up manner between left and right cues, "exogenous" attention is a more likely confound here in my view. Specifically, the spatial cue may automatically trigger attention in the direction of the target location it points to (and such exogenous effects would be expected even for unpredictive cues).

(3) Benefit and cost, or just cost?

Line 151 states that no statistically significant benefit for the saccade target was found compared to the neutral baseline. Yet, the claim throughout the article is distinct, such as in line 159: "These results show that approximately 100 milliseconds before microsaccade onset, discrimination rapidly improved at the intended target location". I do not question the robustness of the congruency effect, but the authors should be more careful when inferring "improved" perception at the target location because, as far as I could tell (as well as in the authors' own writing in line 151), this is not substantiated statistically when compared to the neutral baseline.

Related to this point, in Figure 3B, it would be informative to also see the average performance in the neutral cue condition (for example, as a straight line as in some other figures). This would help to better appreciate the relative benefits and/or costs compared to the neutral condition, also in the time-resolved data.

(4) Statistical inference for the comparison between failed and non-failed trials

Currently, the lack of modulation in the failed saccade trials hinges on a null effect. It would be stronger to support the claims with a significant difference in the congruency effect between failed and non-failed trials. Indeed, lack of significance in failed saccade trials does by itself not constitute valid evidence that the congruency effect is larger in saccade compared to failed saccade trials. For this, a significant interaction between saccade-trial-type (failed/non-failed) and congruency (congruent/incongruent) should be established (see e.g., Nieuwenhuis et al., Nat Neurosci, 2011).

(5) Time window justification

While the authors nicely depict their data across the full time axis, all statistics are currently performed on data extracted from specific time windows. How exactly were these time windows determined and justified? Likewise, how were the specific times picked for visualizing and statistically quantifying the data in e.g., Figures 3D and E? It would be reassuring to add justification for these specific time windows and/or to verify (using follow-up analyses) that the presented results are robust when different time windows are chosen.

(6) Microsaccade definition

Microsaccades are explicitly defined as being below half a degree. This appears rather arbitrary and rigid. Does the size of saccades not ultimately depend on the task and stimulus (e.g., Otero-Millan et al., PNAS, 2013) rather than being a fixed biological property? Perhaps this could be stated less rigidly, such as by stating how microsaccades are often observed below 0.5 degrees.

(Relatedly, one may wonder whether the type of instructed saccades that the authors studied here involves the same type of eye movements as the type of fixational microsaccades that have been the focus of ample prior studies. However, I recognize that this specific reflection may open a debate that is beyond the scope of this article.

Reviewer #1 (Public review):

Review of the revised submission:

I thank the authors for their detailed consideration of my comments and for the additional data, analyses, and clarifications they have incorporated. The new behavioral experiments, quantification of targeted manipulations, and expanded methodological details strengthen the manuscript and address many of my initial concerns. While some questions remain for future work, the authors' careful responses and the additional evidence provided help resolve the main issues I raised, and I am generally satisfied with the revisions.

Review of original submission:

Summary

In this article, Kawanabe-Kobayashi et al., aim to examine the mechanisms by which stress can modulate pain in mice. They focus on the contribution of noradrenergic neurons (NA) of the locus coeruleus (LC). The authors use acute restraint stress as a stress paradigm and found that following one hour of restraint stress mice display mechanical hypersensitivity. They show that restraint stress causes the activation of LC NA neurons and the release of NA in the spinal cord dorsal horn (SDH). They then examine the spinal mechanisms by which LC→SDH NA produces mechanical hypersensitivity. The authors provide evidence that NA can act on alphaA1Rs expressed by a class of astrocytes defined by the expression of Hes (Hes+). Furthermore, they found that NA, presumably through astrocytic release of ATP following NA action on alphaA1Rs Hes+ astrocytes, can cause an adenosine-mediated inhibition of SDH inhibitory interneurons. They propose that this disinhibition mechanism could explain how restraint stress can cause the mechanical hypersensitivity they measured in their behavioral experiments.

Strengths:

(1) Significance. Stress profoundly influences pain perception; resolving the mechanisms by which stress alters nociception in rodents may explain the well-known phenomenon of stress-induced analgesia and/or facilitate the development of therapies to mitigate the negative consequences of chronic stress on chronic pain.

(2) Novelty. The authors' findings reveal a crucial contribution of Hes+ spinal astrocytes in the modulation of pain thresholds during stress.

(3) Techniques. This study combines multiple approaches to dissect circuit, cellular, and molecular mechanisms including optical recordings of neural and astrocytic Ca2+ activity in behaving mice, intersectional genetic strategies, cell ablation, optogenetics, chemogenetics, CRISPR-based gene knockdown, slice electrophysiology, and behavior.

Weaknesses:

(1) Mouse model of stress. Although chronic stress can increase sensitivity to somatosensory stimuli and contribute to hyperalgesia and anhedonia, particularly in the context of chronic pain states, acute stress is well known to produce analgesia in humans and rodents. The experimental design used by the authors consists of a single one-hour session of restraint stress followed by 30 min to one hour of habituation and measurement of cutaneous mechanical sensitivity with von Frey filaments. This acute stress behavioral paradigm corresponds to the conditions in which the clinical phenomenon of stress-induced analgesia is observed in humans, as well as in animal models. Surprisingly, however, the authors measured that this acute stressor produced hypersensitivity rather than antinociception. This discrepancy is significant and requires further investigation.

(2) Specifically, is the hypersensitivity to mechanical stimulation also observed in response to heat or cold on a hotplate or coldplate?

(3) Using other stress models, such as a forced swim, do the authors also observe acute stress-induced hypersensitivity instead of stress-induced antinociception?

(4) Measurement of stress hormones in blood would provide an objective measure of the stress of the animals.

(5) Results:

(a) Optical recordings of Ca2+ activity in behaving rodents are particularly useful to investigate the relationship between Ca2+ dynamics and the behaviors displayed by rodents.

(b) The authors report an increase in Ca2+ events in LC NA neurons during restraint stress: Did mice display specific behaviors at the time these Ca2+ events were observed such as movements to escape or orofacial behaviors including head movements or whisking?

(c) Additionally, are similar increases in Ca2+ events in LC NA neurons observed during other stressful behavioral paradigms versus non-stressful paradigms?

(d) Neuronal ablation to reveal the function of a cell population.

(e) The proportion of LC NA neurons and LC→SDH NA neurons expressing DTR-GFP and ablated should be quantified (Figures 1G and J) to validate the methods and permit interpretation of the behavioral data (Figures 1H and K). Importantly, the nocifensive responses and behavior of these mice in other pain assays in the absence of stress (e.g., hotplate) and a few standard assays (open field, rotarod, elevated plus maze) would help determine the consequences of cell ablation on processing of nociceptive information and general behavior.

(f) Confirmation of LC NA neuron function with other methods that alter neuronal excitability or neurotransmission instead of destroying the circuit investigated, such as chemogenetics or chemogenetics, would greatly strengthen the findings. Optogenetics is used in Figure 1M, N but excitation of LC→SDH NA neuron terminals is tested instead of inhibition (to mimic ablation), and in naïve mice instead of stressed mice.

(g) Alpha1Ars. The authors noted that "Adra1a mRNA is also expressed in INs in the SDH".

(h) The authors should comprehensively indicate what other cell types present in the spinal cord and neurons projecting to the spinal cord express alpha1Ars and what is the relative expression level of alpha1Ars in these different cell types.

(i) The conditional KO of alpha1Ars specifically in Hes5+ astrocytes and not in other cell types expressing alpha1Ars should be quantified and validated (Figure 2H).

(j) Depolarization of SDH inhibitory interneurons by NA (Figure 3). The authors' bath applied NA, which presumably activates all NA receptors present in the preparation.

k) The authors' model (Figure 4H) implies that NA released by LC→SDH NA neurons leads to the inhibition of SDH inhibitory interneurons by NA. In other experiments (Figure 1L, Figure 2A), the authors used optogenetics to promote the release of endogenous NA in SDH by LC→SDH NA neurons. This approach would investigate the function of NA endogenously released by LC NA neurons at presynaptic terminals in the SDH and at physiological concentrations and would test the model more convincingly compared to the bath application of NA.

(l) As for other experiments, the proportion of Hes+ astrocytes that express hM3Dq, and the absence of expression in other cells, should be quantified and validated to interpret behavioral data.

(m) Showing that the effect of CNO is dose-dependent would strengthen the authors' findings.

(n) The proportion of SG neurons for which CNO bath application resulted in a reduction in recorded sIPSCs is not clear.

(o) A1Rs. The specific expression of Cas9 and guide RNAs, and the specific KD of A1Rs, in inhibitory interneurons but not in other cell types expressing A1Rs should be quantified and validated.

(6) Methods:

It is unclear how fiber photometry is performed using "optic cannula" during restraint stress while mice are in a 50ml falcon tube (as shown in Figure 1A).

Reviewer #2 (Public review):

Summary:

This study investigates the role of spinal astrocytes in mediating stress-induced pain hypersensitivity, focusing on the LC (locus coeruleus)-to-SDH (spinal dorsal horn) circuit and its mechanisms. The authors aimed to delineate how LC activity contributes to spinal astrocytic activation under stress conditions, explore the role of noradrenaline (NA) signaling in this process, and identify the downstream astrocytic mechanisms that influence pain hypersensitivity.

The authors provide strong evidence that 1-hour restraint stress-induced pain hypersensitivity involves the LC-to-SDH circuit, where NA triggers astrocytic calcium activity via alpha1a adrenoceptors (alpha1aRs). Blockade of alpha1aRs on astrocytes-but not on Vgat-positive SDH neurons-reduced stress-induced pain hypersensitivity. These findings are rigorously supported by well-established behavioral models and advanced genetic techniques, uncovering the critical role of spinal astrocytes in modulating stress-induced pain.

However, the study's third aim-to establish a pathway from astrocyte alpha1aRs to adenosine-mediated inhibition of SDH-Vgat neurons-is less compelling. While pharmacological and behavioral evidence is intriguing, the ex vivo findings are indirect and lack a clear connection to the stress-induced pain model. Despite these limitations, the study advances our understanding of astrocyte-neuron interactions in stress-pain contexts and provides a strong foundation for future research into glial mechanisms in pain hypersensitivity.

Strengths:

The study is built on a robust experimental design using a validated 1-hour restraint stress model, providing a reliable framework to investigate stress-induced pain hypersensitivity. The authors utilized advanced genetic tools, including retrograde AAVs, optogenetics, chemogenetics, and subpopulation-specific knockouts, allowing precise manipulation and interrogation of the LC-SDH circuit and astrocytic roles in pain modulation. Clear evidence demonstrates that NA triggers astrocytic calcium activity via alpha1aRs, and blocking these receptors effectively reduces stress-induced pain hypersensitivity.

Weaknesses:

The study offers mainly indirect evidence for astrocyte-released adenosine acting on SDH-VGAT neurons. The potential contributions of astrocyte-derived D-serine and adenosine to different spinal neuron subtypes, as well as the transient "dip" in astrocytic calcium following LC optostimulation, merit further clarification in future work once appropriate tools become available.

Comments on revisions:

The authors have thoroughly addressed my previous comments, resolving most of the points I raised except those noted in the "Weaknesses" section above. I understand that some of these aspects will require future tool development.

Reviewer #3 (Public review):

Summary

This is an exciting and timely study addressing the role of descending noradrenergic systems in nocifensive responses. While it is well-established that spinally released noradrenaline (aka norepinephrine) generally acts as an inhibitory factor in spinal sensory processing, this system is highly complex. Descending projections from the A6 (locus coeruleus, LC) and the A5 regions typically modulate spinal sensory processing and reduce pain behaviours, but certain subpopulations of LC neurons have been shown to mediate pronociceptive effects, such as those projecting to the prefrontal cortex (Hirshberg et al., PMID: 29027903).

The study proposes that descending cerulean noradrenergic neurons potentiate touch sensation via alpha-1 adrenoceptors on Hes5+ spinal astrocytes, contributing to mechanical hyperalgesia. This finding is consistent with prior work from the same group (dd et al., PMID:). However, caution is needed when generalising about LC projections, as the locus coeruleus is functionally diverse, with differences in targets, neurotransmitter co-release, and behavioural effects. Specifying the subpopulations of LC neurons involved would significantly enhance the impact and interpretability of the findings.

Strengths

The study employs state-of-the-art molecular, genetic, and neurophysiological methods, including precise CRISPR and optogenetic targeting, to investigate the role of Hes5+ astrocytes. This approach is elegant and highlights the often-overlooked contribution of astrocytes in spinal sensory gating. The data convincingly support the role of Hes5+ astrocytes as regulators of touch sensation, coordinated by brain-derived noradrenaline in the spinal dorsal horn, opening new avenues for research into pain and touch modulation.

Furthermore, the data support a model in which superficial dorsal horn (SDH) Hes5+ astrocytes act as non-neuronal gating cells for brain-derived noradrenergic (NA) signalling through their interaction with substantia gelatinosa inhibitory interneurons. Locally released adenosine from NA-stimulated Hes5+ astrocytes, following acute restraint stress, may suppress the function of SDH-Vgat+ inhibitory interneurons, resulting in mechanical pain hypersensitivity. However, the spatially restricted neuron-astrocyte communication underlying this mechanism requires further investigation in future studies.

Comments on revisions:

One important point remains insufficiently resolved. In Figure S4C, two of the three visible neurons in the A5 example appear to show a white "halo" at the cell border, suggesting a merge of eGFP (green) and TH (magenta) and therefore possible transgene positivity. To draw a confident conclusion about the specificity of the approach for the A6 (LC) population, the authors are kindly asked to provide high-resolution images of several representative A5 sections, presented both as merged and as separate colour channels. Ideally, quantification across multiple rostrocaudal sections of A5, A6 and A7 should be provided. This is essential for determining whether any transgene expression occurs within the A5 nucleus, particularly given its several-millimetre rostrocaudal extent. As the behavioural phenotype arises from manipulation of only a small subset of A6 neurons, ruling out any contribution from A5 (or A7) is critical for validating pathway specificity, especially in light of prior reports showing that similar approaches can label A5 fibres.

Reviewer #1 (Public review):

Summary:

In this study, Lamberti et al. investigate how translation initiation and elongation are coordinated at the single-mRNA level in mammalian cells. The authors aim to uncover whether and how cells dynamically adjust initiation rates in response to elongation dynamics, with the overarching goal of understanding how translational homeostasis is maintained. To this end, the study combines single-molecule live-cell imaging using the SunTag system with a kinetic modeling framework grounded in the Totally Asymmetric Simple Exclusion Process (TASEP). By applying this approach to custom reporter constructs with different coding sequences, and under perturbations of the initiation/elongation factor eIF5A, the authors infer initiation and elongation rates from individual mRNAs and examine how these rates covary.

The central finding is that initiation and elongation rates are strongly correlated across a range of coding sequences, resulting in consistently low ribosome density ({less than or equal to}12% of the coding sequence occupied). This coupling is preserved under partial pharmacological inhibition of eIF5A, which slows elongation but is matched by a proportional decrease in initiation, thereby maintaining ribosome density. However, a complete genetic knockout of eIF5A disrupts this coordination, leading to reduced ribosome density, potentially due to changes in ribosome stalling resolution or degradation.

Strengths:

A key strength of this work is its methodological innovation. The authors develop and validate a TASEP-based Hidden Markov Model (HMM) to infer translation kinetics at single-mRNA resolution. This approach provides a substantial advance over previous population-level or averaged models and enables dynamic reconstruction of ribosome behavior from experimental traces. The model is carefully benchmarked against simulated data and appropriately applied. The experimental design is also strong. The authors construct matched SunTag reporters differing only in codon composition in a defined region of the coding sequence, allowing them to isolate the effects of elongation-related features while controlling for other regulatory elements. The use of both pharmacological and genetic perturbations of eIF5A adds robustness and depth to the biological conclusions. The results are compelling: across all constructs and conditions, ribosome density remains low, and initiation and elongation appear tightly coordinated, suggesting an intrinsic feedback mechanism in translational regulation. These findings challenge the classical view of translation initiation as the sole rate-limiting step and provide new insights into how cells may dynamically maintain translation efficiency and avoid ribosome collisions.

Assessment of Goals and Conclusions:

The authors successfully achieve their stated aims: they quantify translation initiation and elongation at the single-mRNA level and show that these processes are dynamically coupled to maintain low ribosome density. The modeling framework is well suited to this task, and the conclusions are supported by multiple lines of evidence, including inferred kinetic parameters, independent ribosome counts, and consistent behavior under perturbation.

Impact and Utility:

This work makes a significant conceptual and technical contribution to the field of translation biology. The modeling framework developed here opens the door to more detailed and quantitative studies of ribosome dynamics on single mRNAs and could be adapted to other imaging systems or perturbations. The discovery of initiation-elongation coupling as a general feature of translation in mammalian cells will likely influence how researchers think about translational regulation under homeostatic and stress conditions.

The data, models, and tools developed in this study will be of broad utility to the community, particularly for researchers studying translation dynamics, ribosome behavior, or the effects of codon usage and mRNA structure on protein synthesis.

Context and Interpretation:

This study contributes to a growing body of evidence that translation is not merely controlled at initiation but involves feedback between elongation and initiation. It supports the emerging view that ribosome collisions, stalling, and quality control pathways play active roles in regulating initiation rates in cis. The findings are consistent with recent studies in yeast and metazoans showing translation initiation repression following stalling events. However, the mechanistic details of this feedback remain incompletely understood and merit further investigation, particularly in physiological or stress contexts.

In summary, this is a thoughtfully executed and timely study that provides valuable insights into the dynamic regulation of translation and introduces a modeling framework with broad applicability. It will be of interest to a wide audience in molecular biology, systems biology, and quantitative imaging.

Reviewer #2 (Public review):

Summary:

This manuscript uses single-molecule run-off experiments and TASEP/HMM models to estimate biophysical parameters, i.e., ribosomal initiation and elongation rates. Combining inferred initiation and elongation rates, the authors quantify ribosomal density. TASEP modeling was used to simulate the mechanistic dynamics of ribosomal translation, and the HMM is used to link ribosomal dynamics to microscope intensity measurements. The authors' main conclusions and findings are:

- Ribosomal elongation rates and initiation rates are strongly coordinated.

- Elongation rates were estimated between 1 and 4.5 aa/sec. Initiation rates were estimated between 1 and 2 ribosomes/min. These values agree with previously reported ones.

- Ribosomal density was determined to be below 12% for all constructs and conditions.

- eIF5A-perturbations (GC7 inhibition) resulted in non-significant changes in translational bursting and ribosome density.

- eIF5A perturbations affected both elongation and initiation rates.

Strengths:

This manuscript presents an interesting scientific hypothesis to study ribosome initiation and elongation concurrently. This topic is relevant for the field. The manuscript presents a novel quantitative methodology to estimate ribosomal initiation rates from Harringtonine run-off assays. This is relevant because run-off assays have been used to estimate, exclusively, elongation rates.

Comments on revisions:

The authors have addressed my concerns. Specifically, they have expanded the discussion on unexpected eIF5A perturbation results, calculated CAI values for all constructs, and made code and data publicly available via GitHub and Zenodo. The mathematical notation is now consistent, and all variables are properly defined.