Reviewer #1 (Public review):

Summary:

Howard-Spink et al. investigated how older chimpanzees changed their behavior regarding stone tool use for nutcracking over a period of 17 years, from late adulthood to old age. This behavior is cognitively demanding, and it is a good target for understanding aging in wild primates. They used several factors to follow the aging process of five individuals, from attendance at the nut-cracking outdoor laboratory site to time to select tools and efficiency in nut-cracking to check if older chimpanzee changed their behavior.

Indeed, older chimpanzees reduced their visits to the outdoor lab, which was not observed in the younger adults. The authors discuss several reasons for that; the main ones being physiological changes, cognitive and physical constraints, and changes in social associations. Much of the discussion is hypothetical, but a good starting point, as there is not much information about senescence in wild chimpanzees.

The efficiency for nut-cracking was variable, with some individuals taking a long time to crack nuts while others showed little variance. As this is not compared with the younger individuals and the sample is small (only five individuals), it is difficult to be sure if this is also partly a normal variance caused by other factors (ecology) or is only related to senescence.

Strengths:

(1) 17 years of longitudinal data in the same setting, following the same individuals.

(2) Using stone tool use, a cognitively demanding behavior, to understand the aging process.

Weaknesses:

A lack of comparison of the stone tool use behavior with younger individuals in the same period, to check if the changes observed are only related to age or if it is an overall variance. The comparison with younger chimpanzees was only done for one of the variables (attendance).

Comments on Revised Version (from BRE):

The authors have now added to the manuscript that they did not have sufficient data to compare additional variables to younger chimpanzees, and therefore compared intra-individual variation across field seasons. They have also explained that nut hardness, although not measured, was largely controlled for due to the experimental nature of the 'outdoor laboratory' whereby only nuts of a suitable maturity (and hardness) are provided to the chimpanzees. The discussion now also includes mention of other ecological variables and their potential influence on the results.

Reviewer #2 (Public review):

Summary:

Primates are a particularly important and oft-applied model for understanding the evolution of, e.g., life history and senescence in humans. Although there is a growing body of work on aging in primates, there are three components of primate senescence research that have been underutilized or understudied: (1) longitudinal datasets, (2) wild populations, and (3) (stone) tool-use behaviors. Therefore, the goal of this study was to (1) use a 17-year longitudinal dataset (2) of wild chimpanzees in the Bossou forest, (3) visiting a site for field experiments on nut-cracking. They sampled and analyzed data from five field seasons for five chimpanzees of old age. From this sample, Howard-Spink and colleagues noted a decline in tool-use and tool-use efficiency in some individuals, but not in others. The authors then conclude that there is a measurable effect of senescence on chimpanzee behavior, but that it varies individually. The study has major intellectual value as a building block for future research, but there are several major caveats.

Strengths:

With this study, Howard-Spink and colleagues make a foray into a neglected topic of research: the impact of the physiological and cognitive changes due to senescence on stone tool use in chimpanzees. Based on novelty alone, this is a valuable study. The authors cleverly make use of a longitudinal record covering 17 years of field data, which provides a window into long-term changes in the behavior of wild chimpanzees, which I agree cannot be understood through cross-sectional comparisons.

The metrics of 'efficiency' (see caveats below) are suitable for measuring changes in technological behavior over time, as specifically tailored to the nut-cracking (e.g., time, number of actions, number of strikes, tool changes). The ethogram and the coding protocol are also suitable for studying the target questions and objectives. I would recommend, however, the inclusion of further variables that will assist in improving the amount of valid data that can be extrapolated (see also below).

With this pilot, Howard-Spink and colleagues have established a foundation upon which future research can be designed, including further investigation with the Bossou dataset and other existing video archives, but especially future targeted data collection, which can be designed to overcome some of the limits and confounds that can be identified in the current study.

Weaknesses:

Although I agree with the reasoning behind conducting this research and understand that, as the authors state, there are logistical considerations that have to be made when planning and executing such a study, there are a number of methodological and theoretical shortcomings that either need to be more explicitly stated by the authors or would require additional data collection and analysis.

One of the main limitations of this study is the small sample size. There are only 5 of the old-aged individuals, which is not enough to draw any inferences about aging for chimpanzees more generally. Howard-Spink and colleagues also study data from only five of the 17 years of recorded data at Bossou. The selection of this subset of data requires clarification: why were these intervals chosen, why this number of data points, and how do we know that it provides a representative picture of the age-related changes of the full 17 years?

With measuring and interpreting the 'efficiency' of behaviors, there are in-built assumptions about the goals of the agents and how we can define efficiency. First, it may be that efficiency is not an intentional goal for nut-cracking at all, but rather, e.g., productivity as far as the number of uncrushed kernels (cf. Putt 2015). Second, what is 'efficient' for the human observer might not be efficient for the chimpanzee who is performing the behavior. More instances of tool-switching may be considered inefficient, but it might also be a valid strategy for extracting more from the nuts, etc. Understanding the goals of chimpanzees may be a difficult proposition, but these are uncertainties that must be kept in mind when interpreting and discussing 'decline' or any change in technological behaviors over time.

For the study of the physiological impact of senescence of tool use (i.e., on strength and coordination), the study would benefit from the inclusion of variables like grip type and (approximate) stone size (Neufuss et al., 2016). The size and shape of stones for nut-cracking have been shown to influence the efficacy and 'efficiency' of tool use (i.e., the same metrics of 'efficiency' implemented by Howard-Spink et al. in the current study), meaning raw material properties are a potential confound that the authors have not evaluated.

Similarly, inter- and intraspecific variation in the properties of nuts being processed is another confound (Falótico et al., 2022; Proffitt et al., 2022). If oil palm nuts were varying year-to-year, for example, this would theoretically have an effect on the behavioral forms and strategies employed by the chimpanzees, and thus, any metric of efficiency being collected and analyzed. Further, it is perplexing that the authors analyze only one year where the coula nuts were provided at the test site, but these were provided during multiple field seasons. It would be more useful to compare data from a similar number of field seasons with both species if we are to study age-related changes in nut processing over time (one season of coula nut-cracking certainly does not achieve this).

Both individual personality (especially neophilia versus neophobia; e.g., Forss & Willems, 2022) and motivation factors (Tennie & Call, 2023) are further confounds that can contribute to a more valid interpretation of the patterns found. To draw any conclusions about age-related changes in diet and food preferences, we would need to have data on the overall food intake/preferences of the individuals and the food availability in the home range. The authors refer briefly to this limitation, but the implications for the interpretation of the data are not sufficiently underlined (e.g., for the relevance of age-related decline in stone tool-use ability for individual survival).

Generally speaking, there is a lack of consideration for temporal variation in ecological factors. As a control for these, Howard-Spink and colleagues have examined behavioral data for younger individuals from Bossou in the same years, to ostensibly show that patterns in older adults are different from patterns in younger adults, which is fair given the available data. Nonetheless, they seem to focus mostly on the start and end points and not patterns that occur in between. For example, there is a curious drop in attendance rate for all individuals in the 2008 season, the implications of which are not discussed by the authors.

As far as attendance, Howard-Spink and colleagues also discuss how this might be explained by changes in social standing in later life (i.e., chimpanzees move to the fringes of the social network and become less likely to visit gathering sites). This is not senescence in the sense of physiological and cognitive decline with older age. Instead, the reduced attendance due to changes in social standing seems rather to exacerbate signs of aging rather than be an indicator of it itself. The authors also mention a flu-like epidemic that caused the death of 5 individuals; the subsequent population decline and related changes in demography also warrant more discussion and characterization in the manuscript.

Understandably, some of these issues cannot be evaluated or corrected with the presented dataset. Nonetheless, these undermine how certain and/or deterministic their conclusions can really be considered. Howard-Spink et al. have not strongly 'demonstrated' the validity of relationships between the variables of the study. If anything, their cursory observations provide us with methods to apply and hypotheses to test in future studies. It is likely that with higher-resolution datasets, the individual variability in age-related decline in tool-use abilities will be replicated. For now, this can be considered a starting point, which will hopefully inspire future attempts to research these questions.

Falótico, T., Valença, T., Verderane, M. & Fogaça, M. D. Stone tools differences across three capuchin monkey populations: food's physical properties, ecology, and culture. Sci. Rep. 12, 14365 (2022).<br /> Forss, S. & Willems, E. The curious case of great ape curiosity and how it is shaped by sociality. Ethology 128, 552-563 (2022).<br /> Neufuss, J., Humle, T., Cremaschi, A. & Kivell, T. L. Nut-cracking behaviour in wild-born, rehabilitated bonobos (Pan paniscus): a comprehensive study of hand-preference, hand grips and efficiency. Am. J. Primatol. 79, e22589 (2016).<br /> Proffitt, T., Reeves, J. S., Pacome, S. S. & Luncz, L. V. Identifying functional and regional differences in chimpanzee stone tool technology. R. Soc. Open Sci. 9, 220826 (2022).<br /> Putt, S. S. The origins of stone tool reduction and the transition to knapping: An experimental approach. J. Archaeol. Sci.: Rep. 2, 51-60 (2015).<br /> Tennie, C. & Call, J. Unmotivated subjects cannot provide interpretable data and tasks with sensitive learning periods require appropriately aged subjects: A Commentary on Koops et al. (2022) "Field experiments find no evidence that chimpanzee nut cracking can be independently innovated". ABC 10, 89-94 (2023).

Comments on Revised Version (from BRE):

The authors have revised their methods to clarify why certain field seasons were chosen and have clarified aspects of their analysis relevant to this reviewer's concerns. The coula nut cracking data and results which were of a single season have now been restricted to the Supplementary. The revised discussion now includes a much more detailed limitations section including both ecological factors but also the effects of social aging. Stone tool size, grip and other factors are also acknowledged as being potentially important for measuring efficiency but the authors were unable to include in this study due to the nature of the dataset.

Reviewer #1 (Public review):

G. Squiers et al. analyzed a previously reported CRISPR genetic screening dataset of engineered GLUT4 cell-surface presentation and identified the Commander complex subunit COMMD3 as being required for endosomal recycling of specific cargo protein, transferrin receptor (TfR), to the cell surface. Through comparison of COMMD3-KO and other Commander subunit-KO cells, they demonstrated that the role of COMMD3 in mediating TfR recycling is independent of the Commander complex. Structural analysis and co-immunoprecipitation followed by mass spectrometry revealed that TfR recycling by COMMD3 relies on ARF1. COMMD3 interacts with ARF1 through its N-terminal domain (NTD) to stabilize ARF1. A mutation in the NTD of COMMD3 failed to rescue cell surface TfR in COMMD3-KO cells. In conclusion, the authors assert that COMMD3 stabilizes ARF1 in a Commander complex-independent manner, which is essential for recycling specific cargo proteins from endosomes to the plasma membrane.

The conclusions of this paper are generally supported by data, but some validation experiments should be included to strengthen the study.

(1) Specific role of ARF1 to COMMD3:<br /> The authors don't think KO/KD of ARF1 is appropriate to address its specificity to COMMD3 cargo selection, so they focused on the COMMD3 NTD mutant. Though the mutant failed to rescue COMMD3 cargo TfR recycling, they did not examine the Commander cargo ITGA6. In addition, they cannot validate that the mutant interrupts the interaction between NTD and ARF1. These missing results and validation make their claim that ARF1 is specific to the COMMD3's Commander-independent function less convincing.

Reviewer #2 (Public review):

Summary:

The Commander complex is a key player in endosomal recycling which recruits cargo proteins and facilitates the formation of tubulo-vesicular carriers. Squiers et al found COMMD3, a subunit of the Commander complex, could interact directly with ARF1 and regulate endosomal recycling.

Strengths:

Overall, this is a nice study that provides some interesting knowledge on the function of the Commander complex.

Comments on revisions:

The authors have addressed all my previous concerns

Reviewer #3 (Public review):

Summary:

The study by Squiers and colleagues reveals a novel, Commander-independent role for COMMD3 in endosomal recycling. Through unbiased genetic screens, the authors identified COMMD3 as a regulator of GLUT4-SPR trafficking and validated its function using knockout experiments, which demonstrated its impact on endosomal morphology and trafficking independent of the Commander complex. Importantly, they mapped the interaction between the N-terminal domain (NTD) of COMMD3 and the GTPase Arf1, and through structure-guided mutagenesis, established that this interaction is essential for COMMD3's Commander-independent activity. The manuscript provides compelling evidence supporting this newly identified function of COMMD3, and I find the authors' interpretations well-justified. This is an excellent and intriguing study.

Comments on revisions:

The authors addressed all comments. Congratulations on this exciting work.

Reviewer #1 (Public review):

Summary:

Ngo et. al use several computational methods to determine and characterize structures defining the three major states sampled by the human voltage-gated potassium channel hERG: the open, closed and inactivated state. Specifically, they use AlphaFold and Rosetta to generate conformations that likely represent key features of the open, closed and inactivated states of this channel. Molecular dynamics simulations confirm that ion conduction for structure models of the open but not the inactivated state. Moreover, drug docking in silico experiments show differential binding of drugs to the conformation of the three states; the inactivated one being preferentially bound by many of them. Docking results are then combined with a Markov model to get state-weighted binding free energies that are compared with experimentally measured ones.

Strengths:

The study uses state-of-the-art modeling methods to provide detailed insights into the structure-function relationship of an important human potassium channel. AlphaFold modeling, MD simulations and Markov modeling are nicely combined to investigate the impact of structural changes in the hERG channel on potassium conduction and drug binding.

Weaknesses:

(1) Selection of inactivated conformations based on AlphaFold modeling seems a bit biased.<br /> The authors base their initial selection of the "most likely" inactivated conformation on the expected flipping of V625 and the constriction at G626 carbonyls. This follows a bit the "Streetlight effect". It would be better to have selection criteria that are independent of what they expect to find for the inactivated state conformations. Using cues that favour sampling/modeling of the inactivated conformation, such as the deactivated conformation of the VSD used in the modeling of the closed state, would be more convincing. There may be other conformations that are more accurately representing the inactivated state. In addition, I am not sure whether pLDDT is a good selection criterion. It reports on structural confidence, but that may not relate to functional relevance.

(2) The comparison of predicted and experimentally measured binding affinities lacks of appropriate controls. Using binding data from open-state conformations only is not the best control. A much better control is the use of alternative structures predicted by AlphaFold for each state (e.g. from the outlier clusters or not considered clusters) in the docking and energy calculations. Importantly, labels for open, closed and inactivated state should be randomized to check robustness of the findings. Such a control would strengthen the overall findings significantly.

(3) Figures where multiple datapoints are compared across states generally lack assessment of the statistical significance of observed trends (e,g. Figure 3d).

The authors have successfully achieved their goal of providing new insights into the structural details of the three major conformational states sampled by the human voltage-gated potassium channel hERG, and linking these states to changes in drug-binding affinities. However, the study would benefit from more robust controls and orthogonal validation. Additionally, the generalizability of the approach remains to be demonstrated.

Reviewer #2 (Public review):

Summary:

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

Strengths:

Ngo et al. employ various computational methods to enhance AlphaFold2's prediction capabilities for the human voltage-gated potassium channel hERG. They guide AlphaFold2 to explore different protein conformations and states, including its open, closed, and inactivated forms, using targeted templates. Additionally, they applied the Rosetta FastRelax protocol with an implicit membrane to refine the conformation of each residue in the predictions and address steric clashes, along with molecular dynamics (MD) simulations to account for membrane-pore flexibility. The methodology is well-described, and the figures are clear and descriptive.

The authors have addressed some of the concerns raised during the first round of reviews. For instance, to mitigate potential bias in selecting the inactivated conformation, they evaluated conformational variability via backbone dihedral angles at specific residues in the selectivity filter and the drug binding sites. They also evaluated the top representative model from inactivated-state-sampling Cluster 3 (termed "AF ic3"), which was initially excluded. This model is now included in the revised manuscript as Figure S9a, b. MD simulations confirmed that this state could be a potential alternative open-state conformation. The authors also acknowledged the limitation of their study by not incorporating other enhanced sampling methods and AF3.

In the revised manuscript, the authors provided more extensive explanations of their methods. For example, they explained that their approach to template selection was guided by their experience-AlphaFold2 with larger templates often overly constraining predictions to the input structure, reducing its flexibility to explore alternative conformations. In contrast, smaller, targeted fragments increase the likelihood that AlphaFold2 will incorporate the desired structural features while predicting the rest of the protein. They also noted that pLDDT scores are not always reliable for selecting new or alternative conformations, citing proper references. They included a model from cluster 3 of the inactivated-state sampling process, which exhibited lower pLDDT scores to illustrate this further.

Another point raised by the reviewers was the exclusion of the N-terminal PAS domain due to GPU memory limitations and its impact on the study. This omission may overlook the PAS domain's potential roles in gating kinetics and allosteric effects on drug binding. The authors acknowledged these limitations in the main text and highlighted the need for future studies to explore these regions in greater detail. They also alluded to potential future research to address these points. Additionally, they have made some of their analysis scripts and tools available on GitHub as a community resource.

Weakness:

The primary issue with the study is the lack of a general pipeline or strategy that can be universally applied to any system, even if limited to ion channels or membrane proteins. A related paper assessed the conformational variability in voltage-sensing domains (VSDs) by applying both the default MSA depth and a range of reduced MSA depths to enhance conformational diversity (please see https://doi.org/10.1101/2025.03.12.642934). They generated 600 models for 32 members of the voltage-gated cation channel superfamily and demonstrated that AlphaFold2 can predict a range of diverse structures of the VSDs, representing activated, deactivated, and intermediate conformations, with more diversity observed for some VSDs compared to others.

The authors have addressed one of the reviewer's concerns about generalizability by including an example in Figure S14 of the modified text, showing how their approach can be applied to model another ion channel system. However, some outstanding questions remain: Is this method better suited for ion channels or membrane proteins with already solved structures and extensive research available? Can this pipeline be applied to other systems as well? Additionally, how does this method compare to other methods using MSA subsampling and other enhanced AF-based techniques to generate alternative conformations of proteins?

Joint Public Review:

Summary:

The authors identify a novel relationship between exosome secretion and filopodia formation in cancer cells and neurons. They observe that multivesicular endosomes (MVE)-plasma membrane (PM) fusion is associated with filopodia formation in HT1080 cells and that MVEs are present on filopodia in primary neurons. Using overexpression and knockdown (KD) of Rab27/HRS in HT1080 cells, melanoma cells and/or primary rat neurons, they find that decreasing exosome secretion reduces filopodia formation, while Rab27 overexpression leads to the opposite result. Furthermore, the decreased filopodia formation is rescued in the Rab27a/HRS KD melanoma cells by the addition of small extracellular vesicles (EVs) but not large EVs purified from control cells. The authors identify endoglin as a protein unique to small EVs secreted by cancer cells when compared to large EVs. KD of endoglin reduces filopodia formation and this is rescued by the addition of small EVs from control cells and not by small EVs from endoglin KD cells. Based on the role of filopodia in cancer metastasis, the authors then investigate the role of endoglin in cancer cell metastasis using a chick embryo model. They find that injection of endoglin KD HT1080 cells into chick embryos gives rise to less metastasis compared to control cells - a phenotype that is rescued by the co-injection of small EVs from control cells. Using quantitative mass spectrometry analysis, they find that thrombospondin type 1 domain containing 7a protein (THSD7A) is down regulated in small EVs from endoglin KD melanoma cells compared to those from control cells. They also report that THSD7A is more abundant in endoglin KD cell lysate compared to control HT1080 cells and less abundant in small EVs from endoglin KD cells compared to control cells, indicating a trafficking defect. Indeed, using immunofluorescence microscopy, the authors observe THSD7A-mScarlet accumulation in CD63-positive structures in endoglin KD HT1080 cells, compared to control cells. Finally, the authors determine that exosome-secreted THSD7A induces filopodia formation in a Cdc42-dependent mechanism.

Strengths:

Through proteomic analysis, the authors revealed that endoglin is an important player in the effective trafficking of THSD7A within exosomes. This study offers interesting insights into the dynamic interplay between exosome-mediated protein trafficking and essential cellular processes, emphasizing its significant relevance in both cancer progression and neural function. The authors communicated their findings clearly and effectively.

(1) While exosomes are known to play a role in cell migration and autocrine signaling, the relationship between exosome secretion and the formation of filopodia is novel.

(2) The authors identify an exosomal cargo protein, THSD7A, which is essential for regulating this function.

(3) The data presented provide strong evidence of a role for endoglin in the trafficking of THSD7A in exosomes.

(4) The authors associate this process with functional significance in cancer cell metastasis and neurological synapse formation, both of which involve the formation of filopodia.

(5) The data are presented clearly, and their interpretation appropriately explains the context and significance of the findings.

Weaknesses:

While the authors showed the important role of exosomal cargo protein THSD7A in neurons, it will be interesting to conduct any in vivo studies to determine whether THSD7A plays a similar role in promoting filopodia and synapse formation in vivo. Some of the comments of the reviewers were not fully addressed, such as rigorous analysis and quantification through Live-cell imaging through TIRF microscopy tracking labeled THSD7A and filopodia formation, which would provide more clarity in timing and strengthen causality of this relationship. The authors need to consider fully characterizing the role of Cdc42. If the authors would like to fully elaborate on the role of Cdc42 in another manuscript, it is better not to mention at all the role of Cdc42 in filopodia formation in this paper.

Reviewer #2 (Public review):

Summary:

Ito and Toyoizumi present a computational model of context-dependent action selection. They propose a "hippocampus" network that learns sequences based on which the agent chooses actions. The hippocampus network receives both stimulus and context information from an attractor network that learns new contexts based on experience. The model is consistent with a variety of experiments, both from the rodent and the human literature, such as splitter cells, lap cells, and the dependence of sequence expression on behavioral statistics. Moreover, the authors suggest that psychiatric disorders can be interpreted in terms of over-/under-representation of context information.

Strengths:

This ambitious work links diverse physiological and behavioral findings into a self-organizing neural network framework. All functional aspects of the network arise from plastic synaptic connections: Sequences, contexts, and action selection. The model also nicely links ideas from reinforcement learning to neuronally interpretable mechanisms, e.g., learning a value function from hippocampal activity.

Weaknesses:

The presentation, particularly of the methodological aspects, needs to be majorly improved. Judgment of generality and plausibility of the results is hampered, but is essential, particularly for the conclusions related to psychiatric disorders. In its present form, it is unclear whether the claims and conclusions made are justified. Also, the lack of clarity strongly reduces the impact of the work in the larger field.

More specifically:

(1) The methods section is impenetrable. The specific adaptations of the model to the individual use cases of the model, as well as the posthoc analyses of the simulations, did not become clear. Important concepts are only defined in passing and used before they are introduced. The authors may consider a more rigorous mathematical reporting style. They also may consider making the methods part self-contained and moving it in front of the results part.

(2) The description of results in the main text remains on a very abstract level. The authors may consider showing more simulated neural activity. It remains vague how the different stimuli and contexts are represented in the network. Particularly, the simulations and related statistical analyses underlying the paradigms in Figure 4 are incompletely described.

(3) The literature review can be improved (laid out in the specific recommendations).

(4) Given the large range of experimental phenomenology addressed by the manuscript, it would be helpful to add a Discussion paragraph on how much the results from mice and humans can be integrated, particularly regarding the nature of the context selection network.

(5) As a minor point, the hippocampus is pretty much treated as a premotor network. Also, a Discussion paragraph would be helpful.

Reviewer #1 (Public review):

Summary:

The manuscript by Ito and Toyozumi proposes a new model for biologically plausible learning of context-dependent sequence generation, which aims to overcome the predefined contextual time horizon of previous proposals. The model includes two interacting models: an Amari-Hopfield network that infers context based on sensory cues, with new contexts stored whenever sensory predictions (generated by a second hippocampal module) deviate substantially from actual sensory experience, which then leads to hippocampal remapping. The hippocampal predictions themselves are context-dependent and sequential, relying on two functionally distinct neural subpopulations. On top of this state representation, a simple Rescola-Wagner-type rule is used to generate predictions for expected reward and to guide actions. A collection of different Hebbian learning rules at different synaptic subsets of this circuit (some reward-modulated, some purely associative, with occasional additional homeostatic competitive heterosynaptic plasticity) enables this circuit to learn state representations in a set of simple tasks known to elicit context-dependent effects.

Strengths:

The idea of developing a circuit-level model of model-based reinforcement learning, even if only for simple scenarios, is definitely of interest to the community. The model is novel and aims to explain a range of context-dependent effects in the remapping of hippocampal activity.

Weaknesses:

The link to model-based RL is formally imprecise, and the circuit-level description of the process is too algorithmic (and sometimes discrepant with known properties of hippocampus responses), so the model ends up falling in between in a way that does not fully satisfy either the computational or the biological promise. Some of the problems stem from the lack of detail and biological justification in the writing, but the loose link to biology is likely not fully addressable within the scope of the current results. The attempt at linking poor functioning of the context circuit to disease is particularly tenuous.

Reviewer #3 (Public review):

Summary:

This paper develops a model to account for flexible and context-dependent behaviors, such as where the same input must generate different responses or representations depending on context. The approach is anchored in the hippocampal place cell literature. The model consists of a module X, which represents context, and a module H (hippocampus), which generates "sequences". X is a binary attractor RNN, and H appears to be a discrete binary network, which is called recurrent but seems to operate primarily in a feedforward mode. H has two types of units (those that are directly activated by context, and transition/sequence units). An input from X drives a winner-take-all activation of a single unit H_context unit, which can trigger a sequence in the H_transition units. When a new/unpredicted context arises, a new stable context in X is generated, which in turn can trigger a new sequence in H. The authors use this model to account for some experimental findings, and on a more speculative note, propose to capture key aspects of contextual processing associated with schizophrenia and autism.

Strengths:

Context-dependency is an important problem. And for this reason, there are many papers that address context-dependency - some of this work is cited. To the best of my knowledge, the approach of using an attractor network to represent and detect changes in context is novel and potentially valuable.

Weaknesses:

The paper would be stronger, however, if it were implemented in a more biologically plausible manner - e.g., in continuous rather than discrete time. Additionally, not enough information is provided to properly evaluate the paper, and most of the time, the network is treated as a black box, and we are not shown how the computations are actually being performed.

Reviewer #1 (Public review):

In this study, Hama et al. investigated the molecular regulatory mechanisms underlying the formation of the ULK1 complex in mammalian cells. Their results showed that in mammalian cells, ULK1, ATG13, and FIP200 form a complex with a stoichiometry of 1:1:2. These predicted interaction regions were validated through both in vivo and in vitro experiments, providing deeper insight into the molecular basis of ULK1 complex assembly in mammalian cells.

The revised manuscript has addressed the majority of my concerns, and I have no further questions. Overall, this is a solid and impactful study that significantly advances our understanding of how the ULK1 complex is formed.

Reviewer #2 (Public review):

Summary:

This is important work that helps to uncover how the process of autophagy is initiated - via structural analyses of the initiating ULK1 complex. High resolution structural details and a mechanistic insight of this complex have been lacking and understanding how it assembles and functions is a major goal of a field that impacts many aspects of cell and disease biology. While we know components of the ULK1 complex are essential for autophagy, how they physically interact is far from clear. The work presented makes use of AlphaFold2 to structurally predict interaction sites between the different subunits of the ULK1 complex (namely ULK1, ATG13 and FIP200). Importantly, the authors go on to experimentally validate that these predicted sites are critical for complex formation by using site-directed mutagenesis and then go on to show that the three-way interaction between these components is necessary to induce autophagy in cells.

Strengths:

The data are very clear. Each binding interface of ATG13 (ATG13 with FIP300/ATG13 with ULK1) is confirmed biochemically with ITC and IP experiments from cells. Likewise, IP experiments with ULK1 and FIP200 also validate interaction domains. A real strength of the work is in the analyses of the consequences of disrupting ATG13's interactions in cells. The authors make CRISPR KI mutations of the binding interface point mutants. This is not a trivial task and is the best approach as everything is monitored under endogenous conditions. Using these cells the authors show that ATG13's ability to interact with both ULK1 and FIP200 is essential for a full autophagy response.

Weaknesses:

I think a main weakness here is the failure to acknowledge and compare results with an earlier preprint that shows essentially the same thing (https://doi.org/10.1101/2023.06.01.543278). Arguably, this earlier work is much stronger from a structural point of view as it relies not only on AlphaFold2 but also actual experimental structural determinations (and takes the mechanisms of autophagy activation further by providing evidence for a super complex between the ULK1 and VPS34 complexes). That is not to say that this work is not important, as in the least it independently helps to build a consensus for ULK1 complex structure. Another weakness is that the downstream "functional" consequences of disrupting the ULK1 complex are only minimally addressed. The authors perform a Halotag-LC3 autophagy assay, which essentially monitors the endpoint of the process. There are a lot of steps in between, knowledge of which could help with mechanistic understanding. Not in the least is the kinase activity of ULK1 - how is this altered by disrupting its interactions with ATG13 and/or FIP200?

Update:

I feel the authors have addressed my concerns in their revised manuscript

Reviewer #3 (Public review):

In this study, the authors employed the protein complex structure prediction tool AlphaFold-Multimer to obtain a predicted structure of the protein complex composed of ULK1-ATG13-FIP200 and validated the structure using mutational analysis. This complex plays a central role in the initiation of autophagy in mammals. The results obtained in this study reveal extensive binary interactions between ULK1 and ATG13, between ULK1 and FIP200, and between ATG13 and FIP200, and pinpoint the critical residues at each interaction interface. Mutating these critical residues led to the loss of binary interactions. Interestingly, the authors showed that the ATG13-ULK1 interaction and the ATG13-FIP200 interaction are partially redundant for maintaining the complex. The experimental data presented by the authors are of high quality and convincing. The revised manuscript offers enhanced details about the prediction procedure and results, along with additional experimental findings, significantly increasing the scientific value of this paper.

Reviewer #1 (Public review):

Summary:

Recent work has demonstrated that the hummingbird hawkmoth, Macroglossum stellatarum, like many other flying insects, use ventrolateral optic flow cues for flight control. However, unlike other flying insects, the same stimulus presented in the dorsal visual field, elicits a directional response. Bigge et al., use behavioral flight experiments to set these two pathways in conflict in order to understand whether these two pathways (ventrolateral and dorsal) work together to direct flight and if so, how. The authors characterize the visual environment (the amount of contrast and translational optic flow) of the hawkmoth and find that different regions of the visual field are matched to relevant visual cues in their natural environment and that the integration of the two pathways reflects a prioritization for generating behavior that supports hawkmoth safety rather than the prevalence for a particular visual cue that is more prevalent in the environment.

Strengths:

This study creatively utilizes previous findings that the hawkmoth partitions their visual field as a way to examine parallel processing. The behavioral assay is well-established and the authors take the extra steps to characterize the visual ecology of the hawkmoth habitat to draw exciting conclusions about the hierarchy of each pathway as it contributes to flight control.

Reviewer #2 (Public review):

Summary

Bigge and colleagues use a sophisticated free-flight setup to study visuo-motor responses elicited in different parts of the visual field in the hummingbird hawkmoth. Hawkmoths have been previously shown to rely on translational optic flow information for flight control exclusively in the ventral and lateral parts of their visual field. Dorsally presented patterns, elicit a formerly completely unknown response - instead of using dorsal patterns to maintain straight flight paths, hawkmoths fly, more often, in a direction aligned with the main axis of the pattern presented (Bigge et al, 2021). Here, the authors go further and put ventral/lateral and dorsal visual cues into conflict. They found that the different visuomotor pathways act in parallel, and they identified a 'hierarchy': the avoidance of dorsal patterns had the strongest weight and optic flow-based speed regulation the lowest weight. The authors linked their behavioral results to visual scene statistics in the hawkmoths' natural environment. The partition of ventral and dorsal visuomotor pathways is well in line with differences in visual cue frequencies. The response hierarchy, however, seems to be dominated by dorsal features, that are less frequent, but presumably highly relevant for the animals' flight safety.

Strengths

The data are very interesting and unique. The manuscript provides a thorough analysis of free-flight behavior in a non-model organism that is extremely interesting for comparative reasons (and on its own). These data are both difficult to obtain and very valuable to the field.

Weaknesses

While the present manuscript clearly goes beyond Bigge et al, 2021, the advance could have perhaps been even stronger with a more fine-grained investigation of the visual responses in the dorsal visual field. Do hawkmoths, for example, show optomotor responses to rotational optic flow in the dorsal visual field?

I find the majority of the data, which are also the data supporting the main claims of the paper, compelling. However, the measurements of flight height are less solid than the rest and I think these data should be interpreted more carefully.

Reviewer #3 (Public review):

The authors have significantly improved the paper in revising to make its contributions distinct from their prior paper. They have also responded to my concerns about quantification and parameter dependency of the integration conclusion. While I think there is still more that could be done in this capacity, especially in terms of the temporal statistics and quantification of the conflict responses, they have a made a case for the conclusions as stated. The paper still stands as an important paper with solid evidence a bit limited by these concerns.

Reviewer #1 (Public review):

Summary:

In a previous work Prut and colleagues had shown that during reaching, high frequency stimulation of the cerebellar outputs resulted in reduced reach velocity. Moreover, they showed that the stimulation produced reaches that deviated from a straight line, with the shoulder and elbow movements becoming less coordinated. In this report they extend their previous work by addition of modeling results that investigate the relationship between the kinematic changes and torques produced at the joints. The results show that the slowing is not due to reductions in interaction torques alone, as the reductions in velocity occur even for movements that are single joint. More interestingly, the experiment revealed evidence for decomposition of the reaching movement, as well as an increase in the variance of the trajectory.

Strengths:

This is a rare experiment in a non-human primate that assessed the importance of cerebellar input to the motor cortex during reaching.

Weaknesses:

None

Reviewer #2 (Public review):

This manuscript asks an interesting and important question: what part of 'cerebellar' motor dysfunction is an acute control problem vs a compensatory strategy to the acute control issue? The authors use a cerebellar 'blockade' protocol, consisting of high frequency stimuli applied to the cerebellar peduncle which is thought to interfere with outflow signals. This protocol was applied in monkeys performing center out reaching movements and has been published from this laboratory in several preceding studies. I found the take-home-message broadly convincing and clarifying - that cerebellar block reduces muscle activation acutely particularly in movements that involve multiple joints and therefore invoke interaction torques, and that movements progressively slow down to in effect 'compensate' for these acute tone deficits. The manuscript was generally well written, data were clear, convincing and novel. The key strengths are differentiating acute from sub-acute (within session but not immediate) kinematic consequences of cerebellar block.

Reviewer #3 (Public review):

Summary:

In their revised manuscript, Sinha and colleagues aim to identify distinct causes of motor impairments seen when perturbing cerebellar circuits. This goal is an important one, given the diversity of movement related phenotypes in patients with cerebellar lesion or injury, which are especially difficult to dissect given the chronic nature of the circuit damage. To address this goal, the authors use high-frequency stimulation (HFS) of the superior cerebellar peduncle in monkeys performing reaching movements. HFS provides an attractive approach for transiently disrupting cerebellar function previously published by this group. First, they find a reduction in hand velocities during reaching, which was more pronounced for outward versus inward movements. By modeling inverse dynamics, they find evidence that shoulder muscle torques are especially affected. Next, the authors examine the temporal evolution of movement phenotypes over successive blocks of HFS trials. Using this analysis, they find that in addition to the acute, specific effects on torques in early HFS trials, there was an additional progressive reduction in velocity during later trials, which they interpret as an adaptive response to the inability to effectively compensate for interaction torques during cerebellar block. Finally, the authors examine movement decomposition and trajectory, finding that even when low velocity reaches are matched to controls, HFS produces abnormally decomposed movements and higher than expected variability in trajectory.

Strengths:

Overall, this work provides important insight into how perturbation of cerebellar circuits can elicit diverse effects on movement across multiple timescales.

The HFS approach provides temporal resolution and enables analysis that would be hard to perform in the context of chronic lesions or slow pharmacological interventions. Thus, this study describes an important advance over prior methods of circuit disruption in the monkey, and their approach can be used as a framework for future studies that delve deeper into how additional aspects of sensorimotor control are disrupted (e.g., response to limb perturbations).

In addition, the authors use well-designed behavioral approaches and analysis methods to distinguish immediate from longer-term adaptive effects of HFS on behavior. Moreover, inverse dynamics modeling provides important insight into how movements with different kinematics and muscle dynamics might be differentially disrupted by cerebellar perturbation.

Remaining comments:

The argument that there are acute and adaptive effects to perturbing cerebellar circuits is compelling, but there seems to be a lost opportunity to leverage the fast and reversible nature of the perturbations to further test this idea and strengthen the interpretation. Specifically, the authors could have bolstered this argument by looking at the effects of terminating HFS - one might hypothesize that the acute impacts on joint torques would quickly return to baseline in the absence of HFS, whereas the longer-term adaptive component would persist in the form of aftereffects during the 'washout' period. As is, the reversible nature of the perturbation seems underutilized in testing the authors' ideas. While this experimental design was not implemented here, it seems like a good opportunity for future work using these approaches.

The analysis showing that there is a gradual reduction in velocity during what the authors call an adaptive phase is convincing. While it is still not entirely clear why disruption of movement during the adaptive phase is not seen for inward targets, despite the fact that many of the inward movements also exhibit large interaction torques, the authors do raise potential explanations in the Discussion.

Reviewer #1 (Public review):

Summary:

Flowers et al describe an improved version of qFit-ligand, an extension of qFit. qFit and qFit-ligand seek to model conformational heterogeneity of proteins and ligands, respectively, cryo-EM and X-ray (electron) density maps using multiconformer models-essentially extensions of the traditional alternate conformer approach in which substantial parts of the protein or ligand are kept in place. By contrast, ensemble approaches represent conformational heterogeneity through a superposition of independent molecular conformations.

The authors provide a clear and systematic description of the improvements made to the code, most notably the implementation of a different conformer generator algorithm centered around RDKit. This approach yields modest improvements in the strain of the proposed conformers (meaning that more physically reasonable conformations are generated than with the "old" qFit-ligand) and real space correlation of the model with the experimental electron density maps, indicating that the generated conformers also better explain the experimental data then before. In addition, the authors expand the scope of ligands that can be treated, most notably allowing for multi conformer modeling of macrocyclic compounds.

Strengths:

The manuscript is well written, provides a thorough analysis, and represents a needed improvement of our collective ability to model small-molecule binding to macromolecules based on cryo-EM and X-ray crystallography, and can therefore has a positive impact on both drug discovery and general biological research.

Weaknesses:

Weaknesses were addressed during review. Overall, the demonstrated performance gains are modest.

Specific comments:

(1) The accuracy of initial placement may be critical. At the same time, in my experience ambiguous cases are quite common, for example with flat ligands with a few substituents sticking out or with ligands with highly mobile tails. There remain some questions regarding sensitivity to initial ligand placement, which individual users should check for.

Reviewer #3 (Public review):

Summary:

The manuscript by Flowers et al. aimed to enhance the accuracy of automated ligand model building by refining the qFit-ligand algorithm. Recognizing that ligands can exhibit conformational flexibility even when bound to receptors, the authors developed a bioinformatic pipeline to model alternate ligand conformations while improving fitting and more energetically favorable conformations.

Strengths:

The authors present a computational pipeline designed to automatically model and fit ligands into electron density maps, identifying potential alternative conformations within the structures.

Weaknesses:

Ligand modeling, particularly in cases of poorly defined electron density, remains a challenging task. The procedure presented in this manuscript exhibits limitations in low-resolution electron density maps (lower than 2.0 Å) and low-occupancy scenarios. Considering that the maps used to establish the operational bounds of qFit-ligand were synthetically generated, it's likely that the resolution cutoff will be even stricter when applied to real-world data.

Reviewer #1 (Public review):

Summary:

In this study, the authors re-analyzed a public dataset (Rademaker et al, 2019, Nature Neuroscience) which includes fMRI and behavioral data recorded while participants held an oriented grating in visual working memory (WM) and performed a delayed recall task at the end of an extended delay period. In that experiment, participants were pre-cued on each trial as to whether there would be a distracting visual stimulus presented during the delay period (filtered noise or randomly-oriented grating). In this manuscript, the authors focused on identifying whether the neural code in retinotopic cortex for remembered orientation was 'stable' over the delay period, such that the format of the code remained the same, or whether the code was dynamic, such that information was present, but encoded in an alternative format. They identify some timepoints - especially towards the beginning/end of the delay - where the multivariate activation pattern fails to generalize to other timepoints, and interpret this as evidence for a dynamic code. Additionally, the authors compare the representational format of remembered orientation in the presence vs absence of a distracting stimulus, averaged over the delay period. This analysis suggested a 'rotation' of the representational subspace between distracting orientations and remembered orientations, which may help preserve simultaneous representations of both remembered and viewed stimuli. Intriguingly, this rotation was a bit smaller for Expt 2, in which the orientation distractor had a greater behavioral impact on the participants' behavioral working memory recall performance, suggesting that more separation between subspaces is critical for preserving intact working memory representations.

Strengths:

(1) Direct comparisons of coding subspaces/manifolds between timepoints, task conditions, and experiments is an innovative and useful approach for understanding how neural representations are transformed to support cognition

(2) Re-use of existing dataset substantially goes beyond the authors' previous findings by comparing geometry of representational spaces between conditions and timepoints, and by looking explicitly for dynamic neural representations

(3) Simulations testing whether dynamic codes can be explained purely by changes in data SNR are an important contribution, as this rules out a category of explanations for the dynamic coding results observed

Weaknesses:

(1) Primary evidence for 'dynamic coding', especially in early visual cortex, appears to be related to the transition between encoding/maintenance and maintenance/recall, but the delay period representations seem overall stable, consistent with some previous findings. However, given the simulation results, the general result that representations may change in their format appears solid, though the contribution of different trial phases remains important for considering the overall result.

(2) Converting a continuous decoding metric (angular error) to "% decoding accuracy" serves to obfuscate the units of the actual results. Decoding precision (e.g., sd of decoding error histogram) would be more interpretable and better related to both the previous study and behavioral measures of WM performance.

Comments on revised version:

The authors have addressed all my previous concerns.

Reviewer #1 (Public review):

Summary:

A whole-organism drug screen was performed to identify molecules that decrease Apolipoprotein B (ApoB) as a target for agents to reduce atherosclerosis. Kelpsch et al. used a zebrafish reporter line, LipoGlo, which is a fusion of the Nano-luciferase protein to the ApoB protein as a proxy for the presence of ApoB-containing lipoproteins (B-lps) in larval stages. The LipoGlo line was screened against a well-characterized drug library and identified 49 hits from their primary screen. Follow-up studies further refined this list to 19 molecules that reproducibly reduced B-lps significantly. The authors focused their studies on enoxolone, a licorice root extract, and showed that larvae treated with this agent can reduce the production of B-lps. As enoxolone has been reported to suppress Hepatocyte Nuclear factor 4a (HNF4a), the authors investigated whether loss-of-hnf4a or pharmacological inhibition of hnf4a in zebrafish also produced similar phenotypes as enoxolone treatment. Their studies showed that this was the case. Transcriptomic studies after enoxolone treatment resulted in altered expression of genes involved in cholesterol biosynthesis and in glucose/insulin signaling pathways. This study highlights the utility of a zebrafish whole-organism chemical screen for modifiers of B-lps production and/or its clearance. A significant finding is that enoxolone inhibits hnf4a in zebrafish to reduce B-lps production and supports targeting HNF4a as a therapeutic means to reduce the emergence of atherosclerosis.

Strengths:

The authors performed a whole-organism chemical screen with over 3000 agents. Such screens are challenging, and the authors used strict criteria for determining hits. The conclusions of this study are well supported by the presented data.

Weaknesses:

There are areas within the study and writing that can be improved and extended, specifically within the gene expression studies.

Reviewer #2 (Public review):

Summary:

The authors aimed to develop a large-scale drug screen to identify B-lp modulators in a vertebrate whole-animal system. Using the zebrafish LipoGlo system that the authors had previously published and validated, the authors screened 2762 drug candidates to generate 49 hits and ultimately validated 19 drugs as genuine ApoB-lowering drugs. Using LipoGlo-Electrophoresis, the authors are able to obtain insights into the ApoB-lipoprotein size/subclass distribution. The authors further validate and study the mechanism of a strong hit, Enoxolone, known as also known as 18β-Glycyrrhetinic acid, which has previously been reported to modulate lipid metabolism. The authors also show that Enoxolone effects are mediated through HNF4⍺, which has been previously shown in the mouse system, but this is the first time it has been shown in the zebrafish.

Strengths:

The study was methodical and robust, using a published and well-validated zebrafish LipoGlo model. The authors validated the hits from the screen independently and considered the possibility that some drugs may have been detected as false positive results due to effects on the enzymatic activity of NanoLuciferase; only one hit, verteporfin, was shown to be a false positive. Using LipoGlo-Electrophoresis, the authors are able to obtain extra insights into the ApoB-lipoprotein size/subclass distribution. They showed that while enoxolone treatment reduces total B-lps, there are no overt changes in B-lp size distribution compared to vehicle-treated animals, other than a slight increase in the zero mobility (ZM) fraction, which contains very large particles and/or tissue aggregates. In contrast, the positive control, lomitapide, does show a change in B-lp size distribution compared to vehicle-treated animals - an increase in frequency of LDLs (low-density lipoprotein), but a decrease in VLDLs (very low-density lipoprotein). This study also assesses the LipoGlo-Electrophoresis profile of HNF4⍺ inhibitors. Work in the zebrafish larvae means that the effect on overall development and an entire vertebrate organism can also be assessed. Finally, the authors applied a thorough statistical measure to define a hit, using the Strictly Standardized Mean Difference (SSMD) method.

Weaknesses:

While the screen was thorough and well-validated, the authors missed a chance to provide a lot of extra significance to a wide range of readership. While the hits were thoroughly validated and displayed, the authors could have also presented the LipoGlo-Electrophoresis for all validated hits or at least a number of them. This would hugely increase the insights into these compounds. Also, the authors chose to validate and follow up a mechanism for Enoxolone, yet this hit was already known to modulate lipid metabolism through HNF4⍺, therefore, hugely limiting the impact of the paper. So what the authors have shown that is novel is only subtly added to this - consistent in vertebrate models, RNA sequencing of pathways, further validation of the HNF4⍺ pathway, and a profile of resulting B-lp size distribution. It seemed an easy way out to pick such a candidate, and they could have followed up by validating more thoroughly a completely novel drug. Also, the authors' prior paper showing the methodology also depicted complementary EM and LipoGlo-microscopy approaches. The microscopy especially, would have been an easy complementary add-on to the screen to really give extra insights into B-lp metabolism in a whole organism for all candidates. This felt like a missed opportunity.

Reviewer #3 (Public review):

Summary:

In "A‬‭ whole-animal‬‭ phenotypic‬‭ drug‬‭ screen‬‭ identifies‬‭ suppressors‬‭ of‬‭ atherogenic‬ lipoproteins", Kelpsch et al seek to identify new, chemically targetable pathways that regulate ApoB function and could ultimately serve as treatments for elevated lipid disorders and/or cardiovascular disease. Given the interconnected nature of lipid regulation in the whole organism with interdependent organs and secreted components (i.e. lipoproteins), they use the vertebrate model zebrafish to screen a large library of ~3000 compounds for their ability to lower the important ApoB-containing lipoproteins. They find 49 hits with 19 compounds passing a higher level of scrutiny, and focus on the role of enoxolone in modulating B-Ip levels at least partly through the HNF4alpha transcription factor and, putatively, through downstream cholesterol/lipid biosynthetic pathways.

Strengths:

The study uses a well-validated in vivo stain (LipoGlo) for measuring lipoproteins in the context of a developing whole organism with a quantitative read-out on a high-throughput platform, allowing for screening of thousands of compounds altering the complex metabolic/physiologic functions necessary for lipoprotein production.

The use of genetic mutant HNF4alpha to assign the mechanism of action to the prime candidate compound studied (enoxolone) is a powerful approach for this challenging aspect of chemical genetics studies. See caveats in weaknesses.

Weaknesses:

As shown in Figure 5A, the HNF4alpha mutant homozygous -/- already lowers lipoproteins. Is it just that the mutant level is already at a minimum in this homozygous mutant (and thus enoxolone can not induce even lower lipoprotein levels), or is it true that the enoxolone molecule is primarily acting through this TF (i.e. HNF4alpha homozygous mutant is truly epistatic to enoxolone function) as favored in the text.

While it is definitely interesting to study enoxolone effects during whole embryo development, the link to HNF4alpha had previously been described in the literature, as pointed out by the authors. The generalizability of the approach to identify truly novel pathways remains to be fully realized, but sharing this available screen data to date will invite further inquiry and be very valuable to the community.

Figure 5 - The same allele of HNF4alpha loss of function/hypomorph (rdu14) is used in both 5A and 5B, but labeled differently in each subpanel. This is explained in the figure legend, but could be updated to use the same nomenclature in both panels to clarify the Figure presentation.

Reviewer #1 (Public review):

This manuscript reports a descriptive study of changes in gene expression after knockdown of the nuclear envelope proteins lamin A/C and Nesprin2/SYNE2 in human U2OS cells. The readout is RNA-seq, which is analyzed at the level of gene ontology and focused investigation of isoform variants and non-coding RNAs. In addition, the mobility of telomeres is studied after these knockdowns, although the rationale in relation to the RNA-seq analyses is rather unclear.

RNA-seq after knockdown of lamin proteins has been reported many times, and the current study does not provide significant new insights that help us to understand how lamins control gene expression. This is particularly because the vast majority of the observed effects on gene expression appear to occur in regions that are not bound by lamin A. It seems likely that these effects are indirect. There is also virtually no overlap between genes affected by laminA/C and by SYNE2, which remains unexplained; for example, it would be good to know whether laminA/C and SYNE2 bind to different genomic regions. The claim in the Title and Abstract that LMNA governs gene expression / acts through chromatin organization appears to be based only on an enrichment of gene ontology terms "DNA conformation change" and "covalent chromatin conformation" in the RNA-seq data. This is a gross over-interpretation, as no experimental data on chromatin conformation are shown in this study. The analyses of transcript isoform switching and ncRNA expression are potentially interesting but lack a mechanistic rationale: why and how would these nuclear envelope proteins regulate these aspects of RNA expression? The effects of lamin A on telomere movements have been reported before; the effects of SYNE2 on telomere mobility are novel (to my knowledge), but should be discussed in the light of previously documented effects of SUN1/2 on the dynamics of dysfunctional telomeres (Lottersberger et al, Cell 2015).

As indicated below, I have substantial concerns about the experimental design of the knockdown experiments.

Altogether, the results presented here are primarily descriptive and do not offer a significant advance in our understanding of the roles of LaminA and SYNE2 in gene regulation or chromatin biology, because the results remain unexplained mechanistically and functionally. Furthermore, the RNAseq datasets should be interpreted with caution until off-target effects of the shRNAs can be ruled out.

Specific comments:

(1) Knockdowns were only monitored by qPCR. Efficiency at the protein level (e.g., Western blots) needs to be determined.

(2) For each knockdown, only a single shRNA was used. shRNAs are infamous for off-target effects; therefore, multiple shRNAs for each protein, or an alternative method such as CRISPR deletion or degron technology, must be tested to rule out such off-target effects.

(3) It is not clear whether the replicate experiments are true biological replicates (i.e., done on different days) or simply parallel dishes of cells done in a single experiment (= technical replicates). The extremely small standard deviations in the RT-qPCR data suggest the latter, which would not be adequate.

Reviewer #2 (Public review):

Summary:

This study focused on the roles of the nuclear envelope proteins lamin A and C, as well as nesprin-2, encoded by the LMNA and SYNE2 genes, respectively, on gene expression and chromatin mobility. It is motivated by the established role of lamins in tethering heterochromatin to the nuclear periphery in lamina-associated domains (LADs) and modulating chromatin organization. The authors show that depletion of lamin A, lamin A and C, or nesprin-2 results in differential effects of mRNA and lncRNA expression, primarily affecting genes outside established LADs. In addition, the authors used fluorescent dCas9 labeling of telomeric genomic regions combined with live-cell imaging to demonstrate that depletion of either lamin A, lamin A/C, or nesprin-2 increased the mobility of chromatin, suggesting an important role of lamins and nesprin-2 in chromatin dynamics.

Strengths:

The major strength of this study is the detailed characterization of changes in transcript levels and isoforms resulting from depletion of either lamin A, lamin A/C, or nesprin-2 in human osteosarcoma (U2OS) cells. The authors use a variety of advanced tools to demonstrate the effect of protein depletion on specific gene isoforms and to compare the effects on mRNA and lncRNA levels.

The TIRF imaging of dCas9-labeled telomeres allows for high-resolution tracking of multiple telomeres per cell, thus enabling the authors to obtain detailed measurements of the mobility of telomeres within living cells and the effect of lamin A/C or nesprin-2 depletion.

Weaknesses:

Although the findings presented by the authors overall confirm existing knowledge about the ability of lamins A/C and nesprin to broadly affect gene expression, chromatin organization, and chromatin dynamics, the specific interpretation and the conclusions drawn from the data presented in this manuscript are limited by several technical and conceptual challenges.

One major limitation is that the authors only assess the knockdown of their target genes on the mRNA level, where they observe reductions of around 70%. Given that lamins A and C have long half-lives, the effect at the protein level might be even lower. This incomplete and poorly characterized depletion on the protein level makes interpretation of the results difficult. The description for the shRNA targeting the LMNA gene encoding lamins A and C given by the authors is at times difficult to follow and might confuse some readers, as the authors do not clearly indicate which regions of the gene are targeted by the shRNA, and they do not make it obvious that lamin A and C result from alternative splicing of the same LMNA gene. Based on the shRNA sequences provided in the manuscript, one can conclude that the shLaminA shRNA targets the 3' UTR region of the LMNA gene specific to prelamin A (which undergoes posttranslational processing in the cell to yield lamin A). In contrast, the shRNA described by the authors as 'shLMNA' targets a region within the coding sequence of the LMNA gene that is common to both lamin A and C, i.e., the region corresponding to amino acids 122-129 (KKEGDLIA) of lamin A and C. The authors confirm the isoform-specific effect of the shLaminA isoform, although they seem somewhat surprised by it, but do not confirm the effect of the shLMNA construct. Assessing the effect of the knockdown on the protein level would provide more detailed information both on the extent of the actual protein depletion and the effect on specific lamin isoforms. Similarly, given that nesprin-2 has numerous isoforms resulting from alternative splicing and transcription initiation. In the current form of the manuscript, it remains unclear which specific nesprin-2 isoforms were depleted, and to what extent (on the protein level).

Another substantial limitation of the manuscript is that the current analysis, with the exception of the chromatin mobility measurements, is exclusively based on transcriptomic measurements by RNA-seq and qRT-PCR, without any experimental validation of the predicted protein levels or proposed functional consequences. As such, conclusions about the importance of lamin A/C on RNA synthesis and other functions are derived entirely from gene ontology terms and are not sufficiently supported by experimental data. Thus, the true functional consequences of lamin A/C or nesprin depletion remain unclear. Statements included in the manuscript such as "our findings reveal that lamin A is essential for RNA synthesis, ..." (Lines 79-80) are thus either inaccurate or misleading, as the current data do not show that lamin A is ESSENTIAL for RNA synthesis, and lamin A/C and lamin A deficient cells and mice are viable, suggesting that they are capable of RNA synthesis.

Another substantial weakness is that the data and analysis presented in the manuscript raise some concerns about the robustness of the findings. Given that the 'shLMNA' construct is expected to deplete both lamin A and C, i.e., its effect encompasses the depletion of lamin A, which is achieved by the 'shLaminA' construct, one would expect a substantial overlap between the DEGs in the shLMNA and shLaminA conditions, with the shLMNA depletion producing a broader effect as it targets both lamin A and C. However, the Venn Diagram in Figure 4a, the genomic loci distribution in Figure 4b, and the correlation analysis in Supplementary Figure S2 show little overlap between the shLMNA and shLaminA conditions, which is quite surprising. In the mapping of the DEGs shown in Figure 4b, it is also surprising not to see the gene targeted by the shRNA, LMNA, found on chromosome 1, in the results for the shLMNA and shLamin A depletion.

The correlation analysis in Supplementary Figure S2 raises further questions. The authors use doc-inducible shRNA constructs to target lamin A (shLaminA), lamin A/C (shLMNA), or nesprin-2 (shSYNE2). Thus, the no-dox control (Ctr) for each of these constructs would be expected to be very similar to the non-target scrambled controls (Ctrl.shScramble and Dox.shScramble). However, in the correlation matrix, each of the no-dox controls clusters more closely with the corresponding dox-induced shRNA condition than with the Ctrl.shScramble or Dox.shScramble conditions, suggesting either a very leaky dox-inducible system, strong effects from clonal selection, or substantial batch effects in the processing. Either of these scenarios could substantially affect the interpretation of the findings. For example, differences between different clonal cell lines used for the studies, independent of the targeted gene, could explain the limited overlap between the different shRNA constructs and result in apparent differences when comparing these clones to the scrambled controls, which were derived from different clones.

The manuscript also contains several factually inaccurate or incorrect statements or depictions. For example, the depiction of the nuclear envelope in Figure 1 shows a single bilipid layer, instead of the actual double bi-lipid layer of the inner and outer nuclear membranes that span the nuclear lumen. The depiction further lacks SUN domain proteins, which, together with nesprins, form the LINC complex essential to transmit forces across the nuclear envelope. The statement in line 214 that "Linker of nucleoskeleton and cytoskeleton (LINC) complex component nesprin-2 locates in the nuclear envelope to link the actin cytoskeleton and the nuclear lamina" is not quite accurate, as nesprin-2 also links to microtubules via dynein and kinesin.

The statement that "Our data show that Lamin A knockdown specifically reduced the usage of its primary isoform, suggesting a potential role in chromatin architecture regulation, while other LMNA isoforms remained unaffected, highlighting a selective effect" (lines 407-409) is confusing, as the 'shLaminA' shRNA specifically targets the 3' UTR of lamin A that is not present in the other isoforms. Thus, the observed effect is entirely consistent with the shRNA-mediated depletion, independent of any effects on chromatin architecture.

The premise of the authors that lamins would only affect peripheral chromatin and genes at LADs neglects the fact that lamins A and C are also found in the nuclear interior, where they form stable structure and influence chromatin organization, and the fact that lamins A and C and nesprins additionally interact with numerous transcriptional regulators such as Rb, c-Fos, and beta-catenins, which could further modulate gene expression when lamins or nesprins are depleted.

The comparison of the identified DEGs to genes contained in LADs might be confounded by the fact that the authors relied on the identification of LADs from a previous study (ref #28), which used a different human cell type (human skin fibroblasts) instead of the U2OS osteosarcoma cells used in the present study. As LADs are often highly cell-type specific, the use of the fibroblast data set could lead to substantial differences in LADs.

Another limitation of the current manuscript is that, in the current form, some of the figures and results depicted in the figures are difficult to interpret for a reader not deeply familiar with the techniques, based in part on the insufficient labeling and figure legends. This applies, for example, to the isoform use analysis shown in Figure 3d or the GenometriCorr analysis quantifying spatial distance between LADs and DEGs shown in Figure 4c.

Overall appraisal and context:

Despite its limitations, the present study further illustrates the important roles the nuclear envelope proteins lamin A, lamin C, and nesprin-2 have in chromatin organization, dynamics, and gene expression. It thus confirms results from previous studies (not always fully acknowledged in the current manuscript) previously reported for lamin A/C depletion. For example, the effect of lamin A/C depletion on increasing mobility of chromatin had already been demonstrated by several other groups, such as Bronshtein et al. Nature Comm 2015 (PMID: 26299252) and Ranade et al. BMC Mol Cel Biol 2019 (PMID: 31117946). Additionally, the effect of lamin A/C depletion on gene and protein expression has already been extensively studied in a variety of other cell lines and model systems, including detailed proteomic studies (PMIDs 23990565 and 35896617).

The finding that that lamin A/C or nesprin depletion not only affects genes at the nuclear periphery but also the nuclear interior is not particularly surprising giving the previous studies and the fact that lamins A and C are also founding within the nuclear interior, where they affect chromatin organization and dynamics, and that lamins A/C and nesprins directly interact with numerous transcriptional regulators that could further affect gene expression independent from their role in chromatin organization.

The authors provide a detailed analysis of isoform switching in response to lamin A/C or nesprin depletion, but the underlying mechanism remains unclear. Similarly, their analysis of the genomic location of the observed DEGs shows the wide-ranging effects of lamin A/C or nesprin depletion, but lets the reader wonder how these effects are mediated. A more in-depth analysis of predicted regulator factors and their potential interaction with lamins A/C or nesprin would be beneficial in gaining more mechanistic insights.

Reviewer #3 (Public review):

Summary:

This manuscript describes DOX inducible RNAi KD of Lamin A, LMNA coded isoforms as a group, and the LINC component SYNE2. The authors report on differentially expressed genes, on differentially expressed isoforms, on the large numbers of differentially expressed genes that are in iLADs rather than LADs, and on telomere mobility changes induced by 2 of the 3 knockdowns.

Strengths:

Overall, the manuscript might be useful as a description for reference data sets that could be of value to the community.

Weaknesses:

The results are presented as a type of data description without formulation of models or explanations of the questions being asked and without follow-up. Thus, conceptually, the manuscript doesn't appear to break new ground.

Not discussed is the previous extensive work by others on the nucleoplasmic forms of LMNA isoforms. Also not discussed are similar experiments- for instance, gene expression changes others have seen after lamin A knockdowns or knockouts, or the effect of lamina on chromatin mobility, including telomere mobility - see, for example, a review by Roland Foisner (doi.org/10.1242/jcs.203430) on nucleoplasmic lamina. The authors need to do a thorough search of the literature and compare their results as much as possible with previous work.

The authors don't seem to make any attempt to explore the correlation of their findings with any of the previous data or correlate their observed differential gene expression with other epigenetic and chromatin features. There is no attempt to explore the direction of changes in gene expression with changes in nuclear positioning or to ask whether the genes affected are those that interact with nucleoplasmic pools of LMNA isoforms. The authors speculate that the DEG might be related to changing mechanical properties of the cells, but do not develop that further.

The technical concerns include: 1) Use of only one shRNA per target. Use of additional shRNAs would have reduced concern about possible off-target knockdown of other genes; 2) Use of only one cell clone per inducible shRNA construct. Here, the concern is that some of the observed changes with shRNA KDs might show clonal effects, particularly given that the cell line used is aneuploid. 3) Use of a single, "scrambled" control shRNA rather than a true scrambled shRNA for each target shRNA.

Reviewer #1 (Public review):

Summary:

PRMT1 overexpression is linked to poor survival in cancers, including acute megakaryocytic leukemia (AMKL). This manuscript describes the important role of PRMT1 in the metabolic reprograming in AMKL. In a PRMT1-driven AMKL model, only cells with high PRMT1 expression induced leukemia, which was effectively treated with the PRMT1 inhibitor MS023. PRMT1 increased glycolysis, leading to elevated glucose consumption, lactic acid accumulation, and lipid buildup while downregulating CPT1A, a key regulator of fatty acid oxidation. Treatment with 2-deoxy-glucose (2-DG) delayed leukemia progression and induced cell differentiation, while CPT1A overexpression rescued cell proliferation under glucose deprivation. Thus, PRMT1 enhances AMKL cell proliferation by promoting glycolysis and suppressing fatty acid oxidation.

Strengths:

This study highlights the clinical relevance of PRMT1 overexpression with AMKL, identifying it as a promising therapeutic target. A key novel finding is the discovery that only AMKL cells with high PRMT1 expression drive leukemogenesis, and this PRMT1-driven leukemia can be effectively treated with the PRMT1 inhibitor MS023. The work provides significant metabolic insights, showing that PRMT1 enhances glycolysis, suppresses fatty acid oxidation, downregulates CPT1A, and promotes lipid accumulation, which collectively drive leukemia cell proliferation. The successful use of the glucose analogue 2-deoxy-glucose (2-DG) to delay AMKL progression and induce cell differentiation underscores the therapeutic potential of targeting PRMT1-related metabolic pathways. Furthermore, the rescue experiment with ectopic Cpt1a expression strengthens the mechanistic link between PRMT1 and metabolic reprogramming. The study employs robust methodologies, including Seahorse analysis, metabolomics, FACS analysis, and in vivo transplantation models, providing comprehensive and well-supported findings. Overall, this work not only deepens our understanding of PRMT1's role in leukemia progression but also opens new avenues for targeting metabolic pathways in cancer therapy.

Comments on revisions:

The reviewer's questions were adequately addressed.

Reviewer #2 (Public review):

Summary:

The manuscript explores the role of PRMT1 in AMKL, highlighting its overexpression as a driver of metabolic reprogramming. PRMT1 overexpression enhances the glycolytic phenotype and extracellular acidification by increasing lactate production in AMKL cells. Treatment with the PRMT1 inhibitor MS023 significantly reduces AMKL cell viability and improves survival in tumor-bearing mice. Intriguingly, PRMT1 overexpression also increases mitochondrial number and mtDNA content. High PRMT1-expressing cells demonstrate the ability to utilize alternative energy sources dependent on mitochondrial energetics, in contrast to parental cells with lower PRMT1 levels.

Strengths:

This is a conceptually novel and important finding as PRMT1 has never been shown to enhance glycolysis in AMKL, and provides a novel point of therapeutic intervention for AMKL.

Comments on revisions:

The author has responded satisfactorily to the review comments and revised the manuscript accordingly.

Reviewer #1 (Public review):

Summary:<br /> The article entitled "Pu.1/Spi1 dosage controls the turnover and maintenance of microglia in zebrafish and mammals" by Wu et al., identifies a role for the master myeloid developmental regulator Pu.1 in the maintenance of microglial populations in the adult. Using a non-homologous end joining knock-in strategy, the authors generated a pu.1 conditional allele in zebrafish, which reports wildtype expression of pu.1 with EGFP and truncated expression of pu.1 with DsRed after Cre mediated recombination. When crossed to existing pu.1 and spi-b mutants, this approach allowed the authors to target a single allele for recombination and induce homozygous loss-of-function microglia in adults. This identified that although there is no short-term consequence to loss of pu.1, microglia lacking any functional copy of pu.1 are depleted over the course of months, even when spi-b is fully functional. The authors go on to identify reduced proliferation, increased cell death, and higher expression of tp53 in the pu.1 deficient microglia, as compared to the wildtype EGFP+ microglia. To extend these findings to mammals, the authors generated a conditional Pu.1 allele in mice and performed similar analyses, finding that loss of a single copy of Pu.1 resulted in similar long-term loss of Pu.1-deficient microglia. The conclusions of this paper are overall well supported by the data.

Strengths:<br /> The genetic approaches here for visualizing recombination status of an endogenous allele are very clever, and by comparing the turnover of wildtype and mutant cells in the same animal the authors can make very convincing arguments about the effect of chronic loss of pu.1. Likely this phenotype would be either very subtle or non-existent without the point of comparison and competition with the wildtype cells.

Using multiple species allows for more generalizable results, and shows conservation of the phenomena at play.

The demonstration of changes to proliferation and cell death in concert with higher expression of tp53 is compelling evidence for the authors argument.

Weaknesses:<br /> This paper is very strong. It would benefit from further investigating the specific relationship between pu.1 and tp53 specifically. Does pu.1 interact with the tp53 locus? Specific molecular analysis of this interaction would strengthen the mechanistic findings.<br /> Recommendations for the authors It would be useful to investigate the relationship between pu.1 and tp53. The data presented here show that pu.1 deficient cells have higher expression of tp53, but this could be an indirect effect. However, since pu.1 has known DNA binding motifs, it would be worthwhile to investigate if there are any direct interactions between pu.1 and the tp53 locus -- does pu.1 directly bind and repress tp53 expression? This could be directly investigated with Cut & Run or an EMSA.

The paper would likely also benefit from more in-depth discussion of the relationship of the zebrafish alleles and their relationship to mammalian Pu.1 -- as presented here, the authors are implicitly arguing that zebrafish pu.1 and spi-b are both more closely related to mammalian Pu.1 than to mammalian Spi-b. Clear argument, perhaps backed up by sequence alignment and homology matching, would help readers, especially those less familiar with zebrafish genome duplications.

Comments on Revised Version (from BRE):

The authors performed in silico analyses to support a regulatory relationship between Pu.1 and Tp53. They identified three putative Pu.1 binding sites within the zebrafish tp53 promoter region. Furthermore, they cite prior evidence demonstrating a similar interaction between PU.1 and members of the P53 family through direct DNA binding.

Reviewer #2 (Public review):

Summary:<br /> In the presented work by Wu et al. the authors investigate the role of the transcription factor Pu.1 in the survival and maintenance of microglia, the tissue resident macrophage population in the brain. To this end they generated a sophisticated new conditional pu.1 allele in zebrafish using CRISPR mediated genome editing which allows visual detection of expression of the mutant allele through a switch from GFP to dsRed after Cre-mediated recombination. Using EdU pulse-chase labelling, they first estimate the daily turnover rate of microglia in the adult zebrafish brain which was found to be higher than rates previously estimated for mice and humans. After conditional deletion of pu.1 in coro1a positive cells, they do not find a difference in microglia number at 2 and 8 days or 1 month post injection of Tamoxifen. However, at 3 month post injection, a strong decrease in mutant microglia could be detected. While no change in microglia number was detected at 1mpi, an increase in apoptotic cells and decreased proliferation as observed. RNA-seq analysis of WT and mutant microglia revealed an upregulation of tp53, which was shown to play a role in the depletion of pu.1 mutant microglia as deletion in tp53-/- mutants did not lead to a decrease in microglia number at 3mpi. Through analysis of microglia number in pU.1 mutants, the authors further show that the depletion of microglia in the conditional mutants is dependent on the presence of WT microglia. To show that the phenomenon is conserved between species, similar experiments were also performed in mice.

This work expands on previous in vitro studies using primary human microglia. The majority of conclusions are well supported by the data, addition of controls and experimental details would strengthen the conclusions and rigor of the paper.

Strengths:

Generation of an elegantly designed conditional pu.1 allele in zebrafish that allows for the visual detection of expression of the knockout allele.<br /> The combination of analysis of pu.1 function in two model systems, zebrafish and mouse, strengthens the conclusions of the paper.<br /> Confirmation of the functional significance of the observed upregulation of tp53 in mutant microglia through double mutant analysis provides some mechanistic insight.

Weaknesses:

(1) The presented RNA-Seq analysis of mutant microglia is underpowered and details on how the data was analyzed is missing. Only 9-15 cells were analyzed in total (3 pools of 3-5 cells each). Further the variability in relative gene expression of ccl35b.1, which was used as a quality control and inclusion criterion to define pools consisting of microglia, is extremely high (between ~4 and ~1600, Fig. S7A).

(2) The authors conclude that the reduction of microglia observed in the adult brain after cKO of pu.1 in the spi-b mutant background is due to apoptosis (Lines 213-215). However, they only provide evidence of apoptosis in 3-5 dpf embryos, a stage at which loss of pu.1 alone does lead to a complete loss of microglia (Fig.2E). A control of pu.1 KI/d839 mutants treated with 4-OHT should be added to show that this effect is indeed dependent on the loss of spi-b. In addition, experiments should be performed to show apoptosis in the adult brain after cKO of pu.1 in spi-b mutants as there seems to be a difference in requirement of pu.1 in embryonic and adult stages.

Comments on Revised Version (from BRE):

The authors have elaborated on the details of the RNA-Seq procedure and clarified the distinct phenotypes observed with global versus condition pu.1 knockout. In addition, the authors' proposed collaborative relationship between Pu.1 and Spi-b has been expanded in the revised manuscript. The authors have addressed all the minor concerns raised by the reviewer.

Reviewer #1 (Public review):

Summary:<br /> Tubert C. et al. investigated the role of dopamine D5 receptors (D5R) and their downstream potassium channel, Kv1, in the striatal cholinergic neuron pause response induced by thalamic excitatory input. Using slice electrophysiological analysis combined with pharmacological approaches, the authors tested which receptors and channels contribute to the cholinergic interneuron pause response in both control and dyskinetic mice (in the L-DOPA off state). They found that activation of Kv1 was necessary for the pause response, while activation of D5R blocked the pause response in control mice. Furthermore, in the L-DOPA off state of dyskinetic mice, the absence of the pause response was restored by the application of clozapine. The authors claimed that 1) the D5R-Kv1 pathway contributes to the cholinergic interneuron pause response in a phasic dopamine concentration-dependent manner, and 2) clozapine inhibits D5R in the L-DOPA off state, which restores the pause response.

Strengths:<br /> The electrophysiological and pharmacological approaches used in this study are powerful tools for testing channel properties and functions. The authors' group has well-established these methodologies and analysis pipelines. Indeed, the data presented were robust and reliable.

The authors addressed all concerns I raised. Presented data are convincing and support their claims.

Reviewer #2 (Public review):

Summary:<br /> This manuscript by Tubert et al. presents the role of D5 receptors (D5R) in regulating the striatal cholinergic interneuron (CIN) pause response through D5R-cAMP-Kv1 inhibitory signaling. Their findings provide a compelling model explaining the "on/off" switch of the CIN pause, driven by the distinct dopamine affinities and the balance of D2R and D5R. Furthermore, the study bridges their previous finding of CIN hyperexcitability (Paz et al., Movement Disorder 2022) with the loss of the pause response in LID mice and demonstrates the restore of the pause through D1/D5 inverse agonist clozapine.

Strengths:<br /> The study presents solid findings, and the writing is logically structured and easy to follow. The experiments are well-designed, properly combining ex vivo electrophysiology recording, optogenetics, and pharmacological treatment to dissect / rule out most, if not all, alternative mechanisms in their model.

Weaknesses (fixed in this revision):<br /> In this round of revision, the authors have included additional experiments examining the role of D2R, and the possible clozapine effects on serotonin receptors in the LID off -L-DOPA ex vivo slices. Although, to our surprise, D2R agonism using quinpirole and sumanirole failed to restore the CIN pause, this study still provides new insights into the balance between D2R and D5R in modulating CIN pause.

Overall, the authors' response adequately addressed concerns raised in the previous revision.

Reviewer #3 (Public review):

The authors have addressed all of my concerns. Congratulations!

Reviewer #1 (Public review):

The article provides a timely and well-written examination of how group identification influences collective behaviors and performance using fNIRs and behavioral data.

Strengths:

(1) Timeliness and Relevance:<br /> The topic is highly relevant, particularly in today's interconnected and team-oriented work environments. Triadic hyperscanning is important to understand group dynamics, but most previous work has been limited to dyadic work.

(2) Comprehensive Analysis:<br /> The authors have conducted extensive analyses, offering valuable insights into how group identification affects collective behaviors.

(3) Clear Writing:<br /> The manuscript is well-written and easy to follow, making complex concepts accessible.

Comments on previous revisions:

Most reviewer concerns have been addressed in the revised manuscript, but some limitations persist with respect to core aspects of study design, such as the long block durations and lack of counter-balancing.

Reviewer #1 (Public review):

Summary:

Prior research indicates that NaV1.2 and NaV1.6 have different compartmental distributions, expression timelines in development, and roles in neuron function. The lack of subtype-specific tools to control Nav1.2 and Nav1.6 activity however has hampered efforts to define the role of each channel in neuronal behavior. The authors attempt to address the problem of subtype specificity here by using aryl sulfonamides (ASCs) to stabilize channels in the inactivated state in combination with mice carrying a mutation that renders NaV1.2 and/or NaV1.6 genetically resistant to the drug. Using this innovative approach, the authors find that action potential initiation is controlled by NaV1.6 while both NaV1.2 and NaV1.6 are involved in back-propagation of the action potential to the soma, corroborating previous findings. Additionally, NaV1.2 inhibition paradoxically increases firing rate, as has also been observed in genetic knockout models. Finally, the potential anticonvulsant properties of ASCs were tested. NaV1.6 inhibition but not NaV1.2 inhibition was found to decrease action potential firing in prefrontal cortex layer 5b pyramidal neurons in response to current injections designed to mimic inputs during seizure. This result is consistent with studies of loss-of-function Nav1.6 models and knockdown studies showing that these animals are resistant to certain seizure types. These results lend further support for the therapeutic promise of activity-dependent, NaV1.6-selective, inhibitors for epilepsy.

Strengths:

(1) The chemogenetic approaches used to achieve selective inhibition of NaV1.2 and NaV1.6 are innovative and help to resolve long-standing questions regarding the role of Nav1.2 and Nav1.6 in neuronal electrogenesis.

(2) The experimental design is overall rigorous, with appropriate controls included.

(3) The assays to elucidate the effects of channel inactivation on typical and seizure-like activity were well selected.

Weaknesses:

(1) As discussed in the revised manuscript, the fact that channels are only partially blocked by the ASC and that ASCs act in a use-dependent manner complicates the interpretation of the effects of NaV1.2 versus NaV1.6 on neuronal activity.

(2) The idea that use-dependent VGSC-acting drugs may be effective antiseizure medications is well established. Additional discussion of the existing, widely used, use-dependent VGSC drugs (e.g. Carbamazepine, Lamotrigine, Phenytoin) would improve the manuscript. Also, the idea that targeting NaV1.6 may be effective for seizures is established by studies using genetic models, knockdown, and partially selective pharmacology (e.g. NBI-921352). Additional discussion of how the results reported here are consistent with or differ from studies using these alternative approaches would improve the discussion.

Reviewer #2 (Public review):

The authors used a clever and powerful approach to explore how Nav1.2 and Nav1.6 channels, which are both present in neocortical pyramidal neurons, differentially control firing properties of the neurons. Overall, the approach worked very well, and the results show very interesting differences when one or the other channel is partially inhibited. The experimental data is solid and the experimental data is very nicely complemented by a computational model incorporating the different localization of the two types of sodium channels.

The revised manuscript has re-organized figures that make the results and interpretation easier to follow.

Reviewer #1 (Public review):

In this study, Acosta-Bayona et al. aim to better understand how environmental conditions could have influenced specific gene functions that may have been selected for during the domestication of teosinte parviglumis into domesticated maize. The authors are particularly interested in identifying the initial phenotypic changes that led to the original divergence of these two subspecies. They selected heavy metal (HM) stress as the condition to investigate. While the justification for this choice remains speculative, paleoenvironmental data would add value; the authors hypothesize that volcanic activity near the region of origin could have played a role.

The authors exposed both maize and teosinte parviglumis to a fixed dose of copper and cadmium, representing an essential and a non-essential element, respectively. They assessed shoot and root phenotypic traits at a defined developmental stage in plants exposed to HM stress versus controls. They then focused on three genes already known to help plants manage HM stress: ZmHMA1, ZmHMA7, and ZmSKUs5. Two of these genes are located in a genomic region linked to traits selected during domestication. A closer examination of nucleotide variability in the coding and flanking regions of these genes provided evidence of selective pressure among teosinte parviglumis, maize, and the outgroup Tripsacum dactyloides.

They further generated a null mutant for ZmHMA1 and showed, for the first time in maize, a pleiotropic phenotype reminiscent of traits associated with the domestication syndrome. Finally, using qPCR, they reported increased expression of the domestication gene Teosinte branched1 (tb1) in teosinte parviglumis under HM stress. Comparative studies focusing on teosinte parviglumis and the genes ZmHMA1, ZmHMA7, and ZmSKUs5 under HM stress are limited; thus, this phenotypic characterization provides a promising starting point for further understanding the genetic basis of the response.

The dataset is of good quality, but the conclusions are not sufficiently supported by the data. Analyses should be expanded, and additional experiments included to strengthen the findings.

(1) Although the paper presents some interesting findings, it is difficult to distinguish which observations are novel versus already known in the literature regarding maize HM stress responses. The rationale behind focusing on specific loci is often lacking. For example, a statistically significant region identified via LOD score on chromosome 5 contains over 50 genes, yet the authors focus on three known HM-related genes without discussing others in the region. It is unclear why ZmHMA1 was selected for mutagenesis over ZmHMA7 or ZmSKUs5.

(2) The idea that HM stress impacted gene function and influenced human selection during domestication is of interest. However, the data presented do not convincingly link environmental factors with human-driven selection or the paleoenvironmental context of the transition. While lower nucleotide diversity values in maize could suggest selective pressure, it is not sufficient to infer human selection and could be due to other evolutionary processes. It is also unclear whether the statistical analysis was robust enough to rule out bias from a narrow locus selection. Furthermore, the addition of paleoclimate records (Paleoenvironmental Data Sources as a starting point) or conducting ecological niche modeling or crop growth models incorporating climate and soil scenarios would strengthen the arguments.

(3) Despite the interest in examining HM stress in maize and the presence of a pleiotropic phenotype, the assessment of the impact of gene expression is limited. The authors rely on qPCR for two ZmHMA genes and the locus tb1, known to be associated with maize architecture. A transcriptomic analysis would be necessary to 1- strengthen the proposed connection and 2- identify other genes with linked QTLs, such as those in the short arm of chromosome 5.

Reviewer #2 (Public review):

Summary:

This work explores the phenotypic developmental traits associated with Cu and Cd responses in teosinte parviglumis, a species evolutionary related to extant maize crops. Cu and Cd could serve as a proxy for heavy metals present in the soils. The manuscript explores potential genetic loci associated with heavy metal responses and domestication identified in previous studies. This includes heavy metal transporters, which are unregulated during stress. To study that, the authors compare the plant architecture of maize defective in ZmHMA1 and speculate on its association with domestication.

Strengths:

Very few studies covered the responses of teosintes to heavy metal stress. The physiological function of ZmHMA1 in maize also gives some novelty in this study. The idea and speculation section is interesting and well-implemented.

Weaknesses:

The authors explored Cu/Cd stress but not a more comprehensive panel of heavy metals, making the implications of this study quite narrow. Some techniques used, such as end-point RT-PCR and qPCR, are substandard for the field. The phenotypic changes explored are not clearly connected with the potential genetic mechanisms associated with them, with the exception of nodal roots. If teosintes in response to heavy metal have phenotypic similarity with modern landraces of maize, then heavy metal stress might have been a confounding factor in the selection of maize and not a potential driving factor. Similar to the positive selection of ZmHMA1 and its phenotypic traits. In that sense, there is no clear hypothesis of what the authors are looking for in this study, and it is hard to make conclusions based on the provided results to understand its importance. The authors do not provide any clear data on the potential influence of heavy metals in the field during the domestication of maize. The potential role of Tb-1 is not very clear either.

Reviewer #1 (Public review):

The authors build on their previous study that showed the midgut microbiome does not oscillate in Drosophila. Here, they focus on metabolites and find that these rhythms are in fact microbiome-dependent. Tests of time-restricted feeding, a clock gene mutant, and diet reveal additional regulatory roles for factors that dictate the timing and rhythmicity of metabolites. The study is well-written and straightforward, adding to a growing body of literature that shows the time of food consumption affects microbial metabolism which in turn could affect the host.

Some additional questions and considerations remain:

(1) The main finding that the microbiome promotes metabolite rhythms is very interesting. Which microbiota are likely to be responsible for these effects? Future work could be done to link specific microbiota linked to some of the metabolic pathways investigated.

(2) TF increases the number of rhythmic metabolites in both microbiome-containing and abiotic flies. This is somewhat surprising given that flies typically eat during the daytime rather than at night, very similar to TF conditions. Future work could be done to restrict feeding to other times of day to see if there is a subsequent shift in the timing of metabolites.

(3) Along these lines, the authors show that Per loss of function reveals a change in the phase of rhythmic metabolites. The authors note that these changes are not due to altered daily feeding rhythms in per mutants. This data suggest Per itself is responsible for these changes. Future work could be done to characterize the mechanisms responsible for these effects.

(4) The calorie content of each diet - normal vs high protein vs high-sugar are different. Future work in this area could consider the possibility of a calorie effect rather than difference in nutrition (protein/carbohydrate) or an effect of high protein/sugar on the microbiome itself.

(5) The supplementary table provided outlining the specific metabolites will be useful for future research in this area.

Reviewer #2 (Public review):

The revised version of the paper clarifies the authors' discoveries regarding daily changes in metabolite concentrations in the gut of adult female Drosophila melanogaster. The authors have addressed all the questions and made the necessary changes, thereby strengthening the value of the article. They demonstrate that various factors influence metabolite oscillations: circadian clock genotype, dietary regime and composition, and gut microbiota.<br /> The notable strengths of this research article remain unchanged: the originality of the experimental design with multiple conditions tested, the variety of detected metabolites, and the clarity in data presentation.

Among the weaknesses, one may consider the following:<br /> Limitations of potential reproducibility: It is unclear whether another research team would identify the same set of cycling metabolites, although similar conclusions appear robust.<br /> Limitations of generalisation: While the conclusions regarding the influence of microbiota, circadian genotype, and dietary regime may be valid, the specific metabolic pathways affected might differ, whereas specific mechanistic explanations remain elusive.<br /> Accuracy of data interpretation: Addressed in comments to the authors. This point corresponds to interpretations discussed by the authors in the text of the manuscript, including beneficial effects of cycling metabolites and phenomenon of oscillation as a whole, its physiological relevance and lack of proofs for existence of any compensative effects, their relevance to metabolism in the gut.<br /> Nevertheless, the authors have clearly and thoroughly addressed all the reviewers' concerns, enabling a better interpretation of the entire study.

Reviewer #3 (Public review):

Summary:

Zhang et al sought to quantify the influence of the gut microbiome on metabolite cycling in a Drosophila model with extensive metabolomic profiling in 4 time points over a 24 hour period. The authors report that the microbiome enhances metabolite cycling in a context-dependent manner. The metabolomics data presented are comprehensive and complex, and they open up may new questions. The major strength of the work is the production of a large dataset of metabolites that can be the basis for hypothesis generation for more specific experiments. There are several weaknesses that make some of the conclusions speculative.

Strengths:

The revised manuscript is significantly improved due to the inclusion of new data and expanded analyses, particularly of time-resolved food intake. The dataset is comprehensive and of high value to the community. The experimental design includes multiple metabolomic comparisons across genetic and dietary conditions, specifically, germ-free versus microbially-colonized flies, time-restricted versus ad libitum feeding, high-sugar versus high protein diets, and wildtype genotype versus the per01 clock mutant. Additionally, the cycling of individual metabolites is presented, allowing readers to examine metabolites of interest. The datasets are made publicly available, allowing this resource to benefit the community.

Weaknesses

Many of the statistically significant differences, e.g. the effects of the microbiome on lipids and biogenic amines in Fig S5A, are quite small in magnitude, and, thus, it is difficult to believe that they are of biological significance without more mechanistic studies. Key conclusions, such as those pertaining to regulation or compensation by the microbiome, are not fully supported by mechanistic experiments. The manuscript uses terms like "regulate" or "compensate," which imply causality or a purpose of the microbiome that is not yet demonstrated, but this type of study opens up many important questions for which new hypotheses can be formed.

A minor limitation is the modest temporal resolution (only four time points in 24 hours), which constrains interpretation of rhythmicity and phase. Additional experimental controls and targeted perturbation experiments are needed to support conclusions about functional impacts of metabolite oscillations. However, these types of limitations are expected from an early study in the field such as this one. Overall, the data are valuable, and the findings demonstrate the promise of the model for studying the interplay between the microbiome, metabolome, and circadian rhythm.

Assessment of Aims

The authors explore how the microbiome interacts with host circadian rhythms and diet to shape metabolite cycling. They largely succeed in characterizing broad trends and generating a valuable resource dataset. However, the conclusion that the microbiome actively regulates or compensates for cycling under specific conditions is not convincingly demonstrated with the current data.

Impact and Utility

The dataset will be a useful reference for researchers interested in microbiome-host interactions, metabolomics, and circadian biology. Its primary value lies in descriptive insight rather than mechanistic resolution. An alternative perspective is that per01 mutants serve as a useful negative control for rhythmicity detection, providing a baseline for distinguishing signal from experimental noise ---an idea that could be emphasized more in the interpretation.

Contextual Considerations

Metabolomics datasets are valuable for understanding the influence of the microbiome. Future follow-up work using higher resolution sampling and functional perturbations (e.g., more extensive genetic or microbial manipulations) will be essential to test hypotheses about the roles of specific metabolites, regulatory pathways, and microbiota members in circadian modulation. This paper lays a strong foundation for such studies.

Reviewer #1 (Public review):

Summary:

Jiang et al. present a measure of phenological lag by quantifying the effects of abiotic constraints on the differences between observed and expected phenological changes, using a combination of previously published phenology change data for 980 species, and associated climate data for study sites. They found that, across all samples, observed phenological responses to climate warming were smaller than expected responses for both leafing and flowering spring events. They also show that data from experimental studies included in their analysis exhibited increased phenological lag compared to observational studies, possibly as a result of reduced sensitivity to climatic changes. Furthermore, the authors present compelling evidence that spatial trends in phenological responses to warming may differ from what would be expected from phenological sensitivity, due to the seasonal timing of when warming occurs. Thus, climate change may not result in geographic convergences of phenological responses. This study presents an interesting way to separate the individual effects of climate change and other abiotic changes on the phenological responses across sites and species.

Strengths:

A clearly defined and straightforward mathematical definition of phenological lag allows for this method to be applied in different scientific contexts. Where data exists, other researchers can partition the effects of various abiotic forcings on phenological responses that differ from those expected from warming sensitivity alone.

Identifying phenological lag and associated contributing factors provides a method by which more nuanced predictions of phenological responses to climate change can be made. Thus, this study could improve ecological forecasting models.

Weaknesses:

The authors include very few data visualizations, and instead report results and model statistics in tables. This is difficult to interpret and may obscure underlying patterns in the data. Including visual representations of variable distributions and between-variable relationships, in addition to model statistics, provides stronger evidence than model statistics alone.

The use of stepwise, automated regression may be less suitable than a hypothesis-driven approach to model selection, combined with expanded data visualization. The use of stepwise regression may produce inappropriate models based on factors of the sample data that may preclude or require different variable selection.

Reviewer #2 (Public review):

Summary:

This is a meta-analysis of the relative contributions of spring forcing temperature, winter chilling, photoperiod and environmental variables in explaining plant flowering and leafing phenology. The authors develop a new summary variable called phenology lag to describe why species might have different responses than predicted by spring temperature.

Strengths:

The summary statistic is used to make a variety of comparisons, such as between observational studies and experimental studies.

Weaknesses:

By combining winter chilling effects, photoperiod effects, and environmental stresses that might affect phenology, the authors create a new variable that is hard to interpret. The authors do not provide information in the abstract about new insights that this variable provides.

Comments:

It would be useful to have a map showing the sites of the studies.

The authors should provide a section in which the strengths and weaknesses of the approach are discussed. Is it possible that mixing different types of data, studies, sample sizes, number of years, experimental set-ups, and growth habits results in artifacts that influence the results?

Now that the authors have created this new variable, phenological lag, which of the components that contribute to it has the most influence on it? Or which components are most influential in which circumstances? For example, what are some examples where photoperiod causes a phenological lag?

Reviewer #1 (Public review):

Summary:

The study by Wang et al. investigates cardiac electromechanical modeling and simulation techniques, focusing on the calibration and validation of ventricular models according to ASME V&V40 standards. The researchers aim to calibrate model parameters to align with key biomarkers such as QRS duration and left ventricular ejection fraction, and validate the model against independent measurements such as displacement and strain metrics. The authors also examine the impact of parameter variations on deformation, ejection fraction, strains, and other biomarkers. The overarching aim of the study is to give "credibility to the underlying computational electromechanics framework" and to "pave the way towards credible cardiacelectromechanical Digital Twins."

Strengths:

(1) The study presents a solid validation strategy for cardiac models based on independent data.

(2) It integrates electrophysiological, mechanical, and hemodynamic biomarkers for sensitivity analysis and calibration.

Weaknesses and Limitations:

(1) Model Assumptions: The study employs simplified modeling assumptions that are not state-of-the-art, e.g.,<br /> a) Isotropic scaling of the mesh to generate an unloaded reference geometry.<br /> b) Simple afterload and preload models that fail to produce physiological results.<br /> c) Simplified epicardial boundary conditions.

(2) Numerical Framework:<br /> a) The mesh resolution and/or the numerical framework used for the mechanical part appears to suffer from known numerical artifacts (locking effects), leading to overly stiff or inaccurate behavior in finite element analysis. This results in an artificially stiff response to deformation, which is compensated by setting active contraction to ten times the value reported in the literature. The authors attribute this to limitations in using ex vivo tissue measurements to represent in vivo function, although similar issues were not observed in previous works.<br /> b) Further, the authors employ the monodomain model for the simulation of the electrical excitation and relaxation on a relatively coarse grid with an approximate edge length of 1mm. This resolution is known to be insufficient for reliable results in organ-scale electrophysiology modeling.

(3) Geometrical model and digital twin: The geometrical model, taken from a public cohort and calibrated to an ECG of another individual along with population-averaged values from a databank (UK Biobank), and unrelated measurements from surgical procedures, can hardly be considered a digital twin. Further, validation of the model was then performed against data from yet another cohort.

(4) Calibration procedure: There are apparent flaws in the calibration procedure, or it is not described in sufficient detail. The authors dedicate significant effort to motivating parameter ranges, but in the end they use mostly other parameters for the calibration process, aiming to maximize left ventricular ejection fraction. It is not clear whether the chosen parameters result in, e.g., physiological calcium traces or calibrated parameters that are within physiological ranges.

(5) Goodness of fits, e.g., a direct comparison of the measured and the simulated ECG, are not provided to assess calibration quality.

(6) Due to these limitations and weaknesses, the authors fall short of achieving some of their goals, particularly establishing credibility for the underlying computational framework and in reproducing healthy pressure-volume loops, and in achieving physiological simulations while using physiological or reported ranges for the calibrated parameters.

For example, a key physiological requirement is that the right and left ventricular stroke volumes are approximately equal in a heart beating at a limit cycle, as the blood pumped by the right ventricle into the pulmonary circulation must match the amount pumped by the left ventricle into the systemic circulation. This balance is not achieved in this study.

(7) The conclusive claim that "the study paves the way towards credible electromechanical cardiac Digital Twins" is not supported. The model exhibits non-physiological behavior, requires unsupported parameter alterations (such as a 10-fold active stress scaling), and does not represent a digital twin, as model data are drawn from various unrelated, non-patient-specific sources.

Conclusion:

Overall, this reviewer considers that the study requires a major revision, including improvements in numerical methods, modeling choices, and checks for physiological behavior. Nevertheless, the provided tables with averaged values from the UK Biobank and the presented validation strategy could be valuable to the research community.

Reviewer #2 (Public review):

The authors present an interesting study on calibrating and validating a biventricular cardiac electromechanical model. This is an important contribution, but some questions remain about the quantitative validation and verification aspects of the study.

Major comments:

(1) The title and paper stress the importance of validation on several occasions. However, the actual validation performed is limited to the section in lines 427-439. Furthermore, it is entirely qualitative, making assessing the model's quality difficult. Most of the paper is focused on sensitivity analysis, which is also interesting but unrelated to validation. Can you include a quantitative comparison with deformation biomarkers? E.g., spatially quantify strain differences between simulation and in vivo data, or overlay the current configuration of the geometry with MRI in various views, and calculate a displacement error norm.

(2) You mention the ASME V&V40 standards throughout your paper. Yet, you only address the "second V" validation, ignoring the "first V" verification. How did you ensure that your computational models are implemented correctly?

(3) All parameters discussed in this publication are physical parameters. What is the sensitivity of your model outputs concerning computational parameters?

Reviewer #1 (Public review):

The authors investigated the role of the zinc transporter ZIP10 in regulating zinc sparks during fertilization in mice. By utilizing oocyte-specific Zip6 and Zip10 conditional knockout mice, the authors effectively demonstrate the importance of ZIP10 in zinc homeostasis, zinc spark generation, and early embryonic development. The study is overall useful as it identifies ZIP10 as an important component of oocyte processes that support embryo development, thus opening the door for further investigations. While the study provides solid evidence for the requirement of ZIP10 in the regulation of zinc sparks and zinc homeostasis, it falls short of revealing the underlying mechanism of how ZIP10 exerts this important function.

(1) The zinc transporters the authors are knocking out are expressed in mouse oocytes through follicular development, and the Gdf9-cre driver used means these oocytes were grown in the absence of appropriate Zinc signaling. Thus, it would be difficult to assert that the lack of fertilization associated with zinc sparks is solely responsible for the failure of embryo development. Spindle morphology and other meiotic parameters do not necessarily report oocyte health, so normalcy of these features may not be a strong argument when it comes to metabolic issues.

(2) While comparing ZIP6 and ZIP10 in the abstract provides context, focusing more on ZIP10 would improve reader comprehension, as ZIP10 is the primary focus of the study. Emphasizing the specific role of ZIP10 will help the reader grasp the core findings more clearly.

(3) Zinc transporters ZIP6 and ZIP10 are expressed during follicular development, but the biological significance of the observation is not clearly addressed. The authors should investigate whether the ZIP6 and ZIP10 knockout affects follicular development and discuss the potential implications.

(4) In Figure 3, the zinc fluorescence images are unclear, making it difficult for readers to interpret the data. Including snapshot images of calcium and zinc spikes as part of the main figure would improve clarity. Moreover, adding more comparative statements and a deeper explanation of why Zip10 KO mice exhibit normal calcium oscillations but lack zinc sparks would strengthen the manuscript.

(5) While the study identifies the role of ZIP10 in zinc spark generation, it lacks a clear mechanistic insight. The topic itself is interesting, but without providing a more detailed explanation of the underlying mechanisms, the study leaves an important gap. Further discussion on the signaling pathways potentially involved in zinc spark regulation would add depth to the findings.

Reviewer #2 (Public review):

Summary:

In this important study, the authors examine the role of two zinc uptake transporters, Zip6 and Zip10, which are important during the maturation of oocytes, and are critical for both successful fertilization and early embryogenesis.

Strengths:

The authors report that oocytes from Zip10 knockout mice exhibit lower labile zinc content during oocyte maturation, decreased amounts of zinc exocytosis during fertilization, and affect the rate of blastocyst generation in fertilized eggs relative to a control strain. They do not observe these changes in their Zip6 knockout animals. The authors present clear and well-documented results from a broad range of experimental modalities in support of their conclusions.

Weaknesses:

(1) The authors' statement that Zip10 is not expressed in the oocyte nuclei (line 252). Furthermore, in that study, ZIP10 was detected in the nuclear/nucleolar positions of oocytes of all follicular stages (Chen et al., 2023), which we did not observe. This is not supported by Figure 1, where some Zip10 signal is apparent in the primordial, primary, and secondary follicle oocytes. This statement should be corrected.

(2) Based on the FluoZin-3AM data, there appears to be less labile zinc in the Zip10d/d oocyte, eggs, and embryos; however, FluoZin-3AM has a number of well-known artifacts and does not accurately capture the localization of labile zinc pools. The patterns do not correspond to the well-documented zinc-containing cortical vesicles. Another zinc probe, such as ZinPyr-4 or ZincBY-1 should be used to visualize the zinc vesicles and confirm that there is less labile zinc in these locations as well.

(3) Line 268 The results indicate that ZIP10 is mostly responsible for the uptake of zinc ions in mouse oocytes. The situation seems a bit more complicated given that the differences in labile zinc content between oocytes from the WT and Zip10d/d animals are small (only 20-30 %) and that the zinc spark is diminished but still apparent at a low level in the Zip10d/d oocytes. Clearly, other factors are involved in zinc uptake at these stages. A variety of studies have suggested that Zip6 and Zip10 work together, perhaps even functioning as a heterodimer in some systems. The double KO would address this more clearly, but if it is not available, it might be more prudent to state that Zip10 plays some role in uptake of zinc in mouse oocytes while the role of Zip6 remains uncertain.

(4) Zip6d/d oocytes did not have changes in labile zinc, nor did the lack of Zip6 have an impact on the zinc spark. However, Figure S1 does show a small amount of detectable Zip6 in the western blot. It is possible that this small amount could compensate for the complete lack of Zip6. Can ZIP6 be found in immunofluorescence of GV oocytes or MII eggs from the Zip6d/d animals? Additionally, it is possible that Zip6's role is only supplementary to that of Zip10. The authors should discuss this possibility. It would also be interesting to see if the Zip6/Zip10 double knockout displays greater defects compared to the Zip10 knockout when considering previous studies.

Reviewer #1 (Public Review):

Insects, such as bees, are surprisingly good at recognizing visual patterns. How they achieve this challenging task with limited computational resources is not fully understood. Based on the actual bee's behaviour and visual circuit structure, MaBouDi et al. constructed a biologically plausible model where the circuit extracts essential visual features from scanned natural scenes. The model successfully discriminated a variety set of visual patterns as the actual bee does. By implementing a type of Hebb's rule for non-associative learning, an early layer of the model extracted orientational information from natural scenes essential to pattern recognition. Throughout the paper, the authors provided intuitive logic for how the relatively simple circuit could achieve pattern recognition. This work could draw broad attention not only in visual neuroscience but also in computer vision.

However, there are a number of weaknesses in the manuscript. 1) The authors claim that the model is inspired by micromorphology, yet it does not rigorously follow the detailed anatomy of the insect brain revealed as of now. 2) Some claims sound a bit too strong compared to what the authors demonstrated with the model. For example, when the authors say the model is minimal, the authors simply investigated how many lobula neurons are required for pattern discrimination in the model. However, the manuscript appears to use this to claim that the presented model is the minimal one required for visual tasks. 3) It lacks explanations of what mechanisms in the model could discriminate some patterns but not others, making the descriptions very qualitative. 4) The authors did not provide compelling evidence that the algorithm is particularly tuned to natural scenes.

Reviewer #2 (Public Review):

This study is inspired by the scanning movements observed in bees when performing visual recognition tasks. It uses a multilayered network, representing stages of processing in the visual lobes (lamina, medulla, lobula), and uses the lobula output as input to a model of associative learning in the mushroom body (MB). The network is first trained with short "scanning" sequences of natural images, in a non-associative adaptation process, and then several experimental paradigms where images are rewarded or punished are simulated, with the output of the MB able to provide the appropriate discriminative decisions (in some but not all cases). The lobula receptive fields formed by the initial adaptation process show spatiotemporal tuning to edges moving at particular orientations and speeds that are comparable to recorded responses of such neurons in the insect brain.

There are two main limitations to the study in my view. First, although described (caption fig 1) as a model "inspired by the micromorphology" of the insect brain, implying a significant degree of accuracy and detail, there are many arbitrary features (unsupported by current connectomics). For example, the strongly constrained delay line structure from medulla to­ lobula neurons, and the use of a single MB0N that has input synapses that undergo facilitation and decay according to different neuromodulators. Second, while it is reasonable to explore some arbitrary architectural features, given that not everything is yet known about these pathways, the presented work does not sufficiently assess the necessity and sufficiency of the different components, given the repeated claims that this is the "minimal circuit" required for the visual tasks explored.

Regarding the mushroom body (MB) learning model, it is strange that no reference is made to recent models closely tied to connectomic and other data in fruit flies, which suggests separate MBONS encode positive vs. negative value; that learning is not dependent on MB0N activity (so is not STDP); that feedback from MBONs to dopaminergic signalling plays an important role, etc. Possibly the MB of the bee operates in a completely different way to the fly, but the presented model relies on relatively old data about MB function, mostly from insects other than bees (e.g. locust) so its relationship to the increasingly comprehensive understanding emerging for the fly MB needs to be clarified. It is implied that the complex interaction of the differential effects of dopamine and octopamine, as modelled here, are required to learn the more complex visual paradigms, but it is not actually tested if simpler rules might suffice. Also, given previous work on models of view recognition in the MB, inspired by bees and ants, it seems plausible that simply using static 25×25 medulla activity as input to produce sparse activity in the KCs would be sufficient for MB0N output to discriminate the patterns used in training, including the face stimulus. Thus it is not clear whether the spatiotemporal input and the lobula encoding are necessary to solve these tasks.

It is also difficult to interpret the range of results in fig 3. The network sometimes learns well, sometimes just adequately (perhaps comparable to bees), and sometimes fails. The presentation of these results does not seem to identify any coherent pattern underlying success or failure, other than that the ability to generalise seems limited. That is, recognition (in most cases) requires the presentation of exactly the same stimulus in exactly the same way (same scanning pattern, distance and speed). In particular, it is hard to know what to conclude when the network appears able to learn some "complex patterns" (spirals, faces) but fails to learn the apparently simple plus vs. multiplication symbol discrimination if it is trained and tested with a scan passing across the whole pattern instead of just the lower half.

In summary, although it is certainly interesting to explore how active vision (scanning a visual pattern) might affect the encoding of stimuli and the ability to learn to discriminate rewarding stimuli, some claims in the paper need to be tempered or better supported by the demonstration that alternative, equally plausible, models of the visual and mushroom body circuits are not sufficient to solve the given tasks.

Reviewer #3 (Public Review):

In this manuscript, the authors use the data collected and observations made on bees' scanning behaviour during visual learning to design a bio-inspired artificial neural network. The network follows the architecture of bees visual systems, where photoreceptors project into the lamina, then the medulla, medulla neurons connect to a set of spiking neurons in the lobula. Lobula neurons project to kenyon cells and then to MBON, which controls reward and punishment. The authors then test the performance of the network in comparison with real bee data, finding it to perform well in all tasks. The paper attempts to reproduce a living organism network with a practical application in mind, and it is quite impressive! I appreciate both the potential implications for the understanding of biological systems and the applications in the development of autonomous agents, making the paper absolutely worth reading.

However, I believe that the current version somewhat lacks in clarity regarding the methodology and in some of the keywords used to describe the model.

Definitions:

Throughout the manuscript, the authors use some key terminology that I believe would benefit from some clarification.

The generated model is described in the title and once in the introduction as "neuromorphic". The model is definitely bio-inspired, but at least in some layers of the neural network, the model is built very differently from actual brain connectivity. Generally, when we use the term neuromorphic we imply many advantages of neural tissue, like energy efficiency, that I am not sure the current model is achieving. I absolutely see how this work is going in that direction, and I also fundamentally agree with the choice of terminology, but this should be clearly explained to not risk over-implications

The authors describe this as a model of "active vision". This is done in the title of the article, and in the many paragraph headings (methods, results). In the introduction, however, the term active vision is reserved to the description of bees' behavior. Indeed, the developed model is not a model of active vision, as this would require for the model to control the movement of the "camera". Here instead the stimuli display is given to the model in a fixed progression. What I suspect is that the authors' aim is to describe a model that supports the bees' active vision, not a model of active vision. I believe this should be very clear from the paper, and it may be appropriate to remove the term from the title.

In the short title, it said that this network is minimal. This is then characterized in the introduction as the minimal network capable of enabling active vision in bees. The authors, however, in their experiment only vary the number of lobula neurons, without changing other parts of the architecture. Given this, we can only say that 16 lobula neurons is the minimal number required to solve the experimental task with the given model. I don't believe that this is generalizable to bees, nor that this network is minimal, as there may be different architectures (for the other layers especially) that require overall less neurons. Moreover, the tasks attempted in the minimal network experiment did not include any of the complex stimuli presented in figure 3, like faces. It may be that 16 lobula neurons are sufficient for the X vs + and clockwise vs counter-clockwise spirals, but we do not know if increasing stimuli complexity would result in a failure of the model with 16 neurons.

Methodology:

The current explanation of the model is currently a bit lacking in clarity and details. This risks impacting negatively on the relevance of the whole work which is interesting and worth reading! This issue affects also the interpretation of the results, as it is not clear to what extent each part of the network could affect the results shown. This is especially the case when the network under-performs with respect to the best performing scenario (e.g., when varying the speed and part of the pattern that is observed, such as in Fig 2C). Adding a detailed technical scheme/drawing specific to the network architecture could have been a way of significantly increasing the clarity of the Methods section and the interpretation of the results.

On a similar note, the authors make some comparisons between the model and real bees. However, it remains unclear whether these similarities are actually indicative of an optimality in the bees visual scanning strategy, or just deriving from the authors design. This is for me particularly important in the experiments aimed at finding the best scanning procedure. If the initial model training is based on natural images it is performed by presenting left to right moving frames, the highest efficiency of lower-half scanning may be due to how the weights in the initial layers are structured and a low generalizability of the model, rather than to the strategy optimality

Joint Public Review:

This elegant study provides important insights into the organization of sub-membrane microtubules in pancreatic β-cells, highlighting a key role for the motor protein KIF5B. The authors propose that KIF5B drives microtubule sliding and alignment along the plasma membrane, a process enhanced by high glucose levels. This precise microtubule arrangement is essential for regulated secretion in β-cells. Supporting this model, the authors show that KIF5B is more highly expressed than other kinesins in MIN6 cells, and its depletion via shRNA disrupts sub-membrane microtubule density and organization. In contrast, KIF5A knockdown alters overall microtubule architecture. Using a dominant-negative approach, they further demonstrate that KIF5B-mediated microtubule sliding relies on its tail domain and is stimulated by glucose, paralleling known glucose-dependent increases in kinesin-1 activity.

Reviewer #2 (Public review):

Summary:

In this manuscript, the authors set out to resolve a long-standing mystery in the field of sensory biology - how large, presynaptic bodies called "ribbon synapses" migrate to the basolateral end of hair cells. The ribbon synapse is found in sensory hair cells and photoreceptors, and is a critical structural feature of a readily releasable pool of glutamate that excites postsynaptic afferent neurons. For decades, we have known these structures exist, but the mechanisms that control how ribbon synapses coalesce at the bottom of hair cells is not well understood. The authors addressed this question by leveraging the highly-tractable zebrafish lateral line neuromast, which exhibits a small number of visible hair cells, easily observed in time-lapse imaging. The approach combined genetics, pharmacological manipulations, high-resolution imaging and careful quantifications. The manuscript commences with a developmental time course of ribbon synapse development, characterizing both immature and mature ribbon bodies (defined by position in the hair cell, apical vs. basal). Next, the authors show convincing (and frankly mesmerizing) imaging data of plus end-directed microtubule trafficking toward the basal end of the hair cells, and data highlighting the directed motion of ribbon bodies. The authors then use a series of pharmacological and genetic manipulations showing the role of microtubule stability and one particular kinesin (Kif1aa) in the transport and fusion of ribbon bodies, which is presumably all prerequisite for hair cell synaptic transmission. The data suggest that microtubules and their stability is necessary for normal numbers of mature ribbons, and that Kif1aa is likely required for fusion events associated with ribbon maturation. Overall, the data provide a new and interesting story on ribbon synapse dynamics.

Strengths:

(1) The manuscript offers comprehensive Introduction and Discussion sections that will inform generalists and specialists.<br /> (2) The use of Airyscan imaging in living samples to view and measure microtubule and ribbon dynamics in vivo represents a strength. With the rigorous quantification and thoughtful analyses, the authors generate datasets often only gotten in cultured cells or more diminutive animal models (e.g., C. elegans).<br /> (3) The number of biological replicates and the statistical analyses are strong. The combination of pharmacology and genetic manipulations also represents strong rigor.<br /> (4) One of the most important strengths is that the manuscript and data spur on other questions - namely, do (or how do) ribbon bodies attach to Kinesin proteins? Also, and as noted in the Discussion, do hair cell activity and subsequent intracellular calcium rises facilitate ribbon transport/fusion.

Reviewer #3 (Public review):

Summary:

The manuscript uses live imaging to study the role of microtubules in the movement of ribeye aggregates in neuromast hair cells in zebrafish. The main findings are that

(1) Ribeye aggregates, assumed to be ribbon precursors, move in a directed motion toward the active zone;<br /> (2) Disruption of microtubules and kif1aa increases the number of ribeye aggregates and decreases the number of mature synapses.

The evidence for point 2 is compelling, while the evidence for point 1 is less convincing. In particular, the directed motion conclusion is dependent upon fitting of mean squared displacement that can be prone to error and variance to do stochasticity, which is not accounted for in the analysis. Only a small subset of the aggregates meet this criteria and one wonders whether the focus on this subset misses the bigger picture of what is happening with the majority of spots.

Strengths:

(1) The effects of Kif1aa removal and nocodozole on ribbon precursor number and size is convincing and novel.<br /> (2) The live imaging of Ribeye aggregate dynamics provides interesting insight into ribbon formation. The movies showing fusion of ribeye spots are convincing and the demonstrated effects of nocodozole and kif1aa removal on the frequency of these events is novel.<br /> (3) The effect of nocodozole and kif1aa removal on precursor fusion is novel and interesting.<br /> (4) The quality of the data is extremely high and the results are interesting.

Weaknesses:

(1) To image ribeye aggregates, the investigators overexpressed Ribeye-a TAGRFP under control of a MyoVI promoter. While it is understandable why they chose to do the experiments this way, expression is not under the same transcriptional regulation as the native protein and some caution is warranted in drawing some conclusions. For example, the reduction in the number of puncta with maturity may partially reflect regulation of the MyoVI promoter with hair cell maturity. Similarly, it is unknown whether overexpression has the potential to saturate binding sites (for example to motors), which could influence mobility. In the revised manuscript, the authors provide evidence to suggest that overexpression is not at unreasonably high levels, which is reasonable. However, I think it remains important to think of these caveats while reading the paper--especially keeping in mind that expression timing is undoubtedly influenced by the transcriptional control of the exogenous promoter .<br /> (2) The examples of punctae colocalizing with microtubules look clear (fig 1 F-G), but the presentation is anecdotal. It would be better and more informative, if quantified.<br /> (3) It appears that any directed transport may be rare. Simply having an alpha >1 is not sufficient to declare movement to be directed (motor driven transport typically has an alpha approaching 2). Due to randomness of a random walk and errors in fits in imperfect data will yield some spread in movement driven by Brownian motion. Many of the tracks in figure 3H look as thought they might be reasonably fit by a straight line (i.e. alpha = 1).<br /> (4) The "directed motion" shown here does not really resemble motor driven transport observed in other systems (axonal transport, for example) even in the subset that have been picked out as examples here. While the role for microtubules and kif1aa in synapse maturation is strong, it seems likely that this role may be something non-canonical (which would be interesting). In the revision, the authors do an excellent job of considering the issues brought up in point 3 and 4. While perhaps no longer a weakness, I am leaving the critiques here for context for the readers to consider. The added taxol results may not completely settle the issue, but are interesting and provide important information.

Reviewer #1 (Public review):

Summary:

In this manuscript, Chua, Daugherty, and Smith analyze a new set of archaeal 20S proteasomes obtained by cryo-EM that illustrate how the occupancy of the HbYX binding pocket induces gate opening. They do so primarily through a V24Y mutation in the α-subunit. These results are supported by a limited set of mutations in K66 in the α subunit, bringing new emphasis to this unit.

Strengths:

The new structure's analysis is comprehensive, occupying the entire manuscript. As such, the scope of this manuscript is very narrow, but the strength of the data is solid, and they offer an interesting and important new piece to the gate-opening literature.

Weaknesses:

Major Concerns

(1) This manuscript rests on one new cryo-EM structure, leading to a single (albeit convincing) experiment demonstrating the importance of occupying the pocket and moving K66. Could a corresponding bulky mutation at K66 not activate the 20S proteasome?

(2) To emphasize the importance of this work, the authors highlight the importance of gate-opening to human 20S proteasomes. However, the key distinctions between these proteasomes are not given sufficient weight.<br /> (a) As the authors note, the six distinct Rpt C-termini can occupy seven different pickets. However, how these differences would impact activation is not thoroughly discussed.<br /> (b) With those other sites, the relative importance of various pockets, such as the one controlling the α3 N-terminus, should be discussed more thoroughly as a potential critical difference.<br /> (c) These differences can lead to eukaryote 20S gates shifting between closed and open and having a partially opened state. This becomes relevant if the goal is to lead to an activated 20S. It would have been interesting to have archaea 20S with a mix of WT and V24Y α-subunits. However, one might imagine the subclassification problem would be challenging and require an extraordinary number of particles.<br /> (d) Furthermore, the conservation of the amino acids around the binding pocket was not addressed. This seems particularly important in the relative contribution of a residue analogous to K66 or V24.

Reviewer #2 (Public review):

Summary:

The manuscript by Chuah et al. reports the experimental results that suggest the occupancy of the HbYX pockets suffices for proteasome gate opening. The authors conducted cryo-EM reconstructions of two mutant archaeal proteasomes. The work is technically sound and may be of special interest in the field of structural biology of the proteasomes.

Strengths:

Overall, the work incrementally deepens our understanding of the proteasome activation and expands the structural foundation for therapeutic intervention of proteasome function. The evidence presented appears to be well aligned with the existing literature, which adds confidence in the presentation.

Weaknesses:

The paper may benefit from some minor revision by making improvements on the figures and necessary quantitative comparative studies.

Reviewer #1 (Public review):

Summary:

In this manuscript, the authors discovered MYL3 of marine medaka (Oryzias melastigma) as a novel NNV entry receptor, elucidating its facilitation of RGNNV entry into host cells through macropinocytosis, mediated by the IGF1R-Rac1/Cdc42 pathway.

Strengths:

In this manuscript, the authors have performed in vitro and in vivo experiments to prove that MnMYL3 may serve as a receptor for NNV via macropinocytosis pathway. These experiments with different methods include Co-IP, RNAi, pulldown, SPR, flow cytometry, immunofluorescence assays and so on. In general, the results are clearly presented in the manuscript.

Comments on revisions:

The authors have addressed all my comments.

Reviewer #2 (Public review):

Summary:

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

Strengths:

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

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

Comments on revisions:

The authors have addressed the concerns from reviewers. This manuscript can be published in the current form.

Reviewer #3 (Public review):

Summary:

The manuscript presents a detailed study on the role of MmMYL3 in the viral entry of NNV, focusing on its function as a receptor that mediates viral internalization through the macropinocytosis pathway. The use of both in vitro assays (e.g., Co-IP, SPR, and GST pull-down) and in vivo experiments (such as infection assays in marine medaka) adds robustness to the evidence for MmMYL3 as a novel receptor for RGNNV. The findings have important implications for understanding NNV infection mechanisms, which could pave the way for new antiviral strategies in aquaculture.

Strengths:

The authors show that MmMYL3 directly binds the viral capsid protein, facilitates NNV entry via the IGF1R-Rac1/Cdc42 pathway, and can render otherwise resistant cells susceptible to infection. This multifaceted approach effectively demonstrates the central role of MmMYL3 in NNV entry.

Reviewer #2 (Public review):

Summary:

Tanaka et al. investigated the role of CCR4 in early atherosclerosis, focusing on the immune modulation elicited by this chemokine receptor under hypercholesterolemia. The study found that Ccr4 deficiency led to qualitative changes in atherosclerotic plaques, characterized by an increased inflammatory phenotype. The authors further analyzed the CD4 T cell immune response in para-aortic lymph nodes and atherosclerotic aorta, showing an increase mainly in Th1 cells and the Th1/Treg ratio in Ccr4-/-Apoe-/- mice compared to Apoe-/- mice. They then focused on Tregs, demonstrating that Ccr4 deficiency impaired their immunosuppressive function in in vitro assays. Authors also states that Ccr4-deficient Tregs had, as expected, impaired migration to the atherosclerotic aorta. Adoptive cell transfer of Ccr4-/- Tregs to Apoe-/- mice mimicked early atherosclerosis development in Ccr4-/-Apoe-/- mice. Therefore, this work shows that CCR4 plays an important role in early atherosclerosis but not in advanced stages.

Strengths:

Several in vivo and in vitro approaches were used to address the role of CCR4 in early atherosclerosis. Particularly, through the adoptive cell transfer of CCR4+ or CCR4- Tregs, the authors aimed to demonstrate the role of CCR4 in Tregs' protection against early atherosclerosis.

Weaknesses:

Flow cytometry experiments are not well controlled. Dead cells and doublets were not excluded from analysis.

Clinical relevance is unclear.

Comments on revisions:

I thank the authors for addressing my suggestions.<br /> I understand that excluding dead cells would require repeating the entire experiment. However, the authors can at least exclude doublets from the existing flow cytometry data.<br /> I also agree with the more cautious claim regarding the role of CCR4 in Treg migration.

Reviewer #3 (Public review):

Summary

Tanaka and colleagues addressed the role of the C-C chemokine receptor 4 (CCR4) in early atherosclerotic plaque development using ApoE-deficient mice on a standard chow diet as a model. Because several CD4+ T cell subsets express CCR4, they examined whether CCR4-deficiency alters the immune response mediated by CD4+ T cells. By histological analysis of aortic lesions, they demonstrated that the absence of CCR4 promoted the development of early atherosclerosis, with heightened inflammation linked to increased macrophages and pro-inflammatory CD4+ T cells, along with reduced collagen content. Flow cytometry and mRNA expression analysis for identifying CD4+ T cell subsets showed that CCR4 deficiency promoted higher proliferation of pro-inflammatory effector CD4+ T cells in peripheral lymphoid tissues and accumulation of Th1 cells in the atherosclerotic lesions. Interestingly, the increased pro-inflammatory CD4+ T cell response occurred despite the expansion of T CD4+ Foxp3+ regulatory cells (Tregs), found in higher numbers in lymphoid tissues of CCR4-deficient mice, suggesting that CCR4 deficiency interfered with Treg's regulatory actions. The findings contrast with earlier studies in a murine model of advanced atherosclerosis, where CCR4 deficiency did not alter the development of the aortic lesions. The authors included a thoughtful discussion about hypothetical mechanisms explaining these contrasting results, including putative differences in the role played by the CCL17/CCL22-CCR4 axis along the stages of atherosclerosis development in this murine model.

Major strengths

• Demonstration of CCR4 deficiency's impact on early atherosclerosis. CCR4 deficiency effects on the early atherosclerosis development in the Apoe-/-mice model were demonstrated by a quantitative analysis of the lesion area, inflammatory cell content and the expression profile of several pro- and anti-inflammatory markers.<br /> • Analysis of the T CD4+ response in various lymphoid tissues (peripheral and para-aortic lymph nodes and spleen) and the atherosclerotic aorta during the early phase of atherosclerosis in the Apoe-/-mice model. This analysis, combining flow cytometry and mRNA expression, showed that CCR4 deficiency enhanced T CD4+ cell activation, favouring the amplification of the typical biased Th1-mediated inflammatory response observed in the lymphoid tissues of hypercholesterolemic mice.<br /> • Treg transference experiments. Transference of Treg from Apoe-/- or Ccr4-/- Apoe-/- mice to Apoe-/- mice under a standard chow diet was useful for addressing the relevance of CCR4 expression on Tregs for the atheroprotective effect of this regulatory T cell subset during early atherosclerosis.

Major weaknesses

• Methodological Limitations: The controls used in the flow cytometry analysis were suboptimal, as neither cell viability nor doublets were assessed. This may have introduced artifacts, particularly when measuring less-represented cell populations within complex samples, such as in assays evaluating Treg migration to the aorta in atherosclerotic mice.<br /> • Incomplete understanding of CCR4-Mediated Mechanisms: The mechanisms by which CCR4 regulates early inflammation and the development of atherosclerosis were not fully clarified.

I have previously addressed the study limitations and their global impact in my earlier reviews.

Reviewer #1 (Public review):

The authors investigate the function and neural circuitry of reentrant signals in visual cortex. Recurrent signaling is thought to be necessary to common types of perceptual experience that are defined by long-range relationships or prior expectation. Contour illusions - where perceptual objects are implied by stimuli characteristics - are a good example of this. The perception of these illusions is thought to emerge as recurrent signals from higher cortical areas feedback onto early visual cortex, to tell early visual cortex that it should be seeing object contours where none are actually present.

The authors test the involvement of reentrant cortical activity in this kind of perception using a drug challenge. Reentrance in visual cortex is thought to rely on NMDAR-mediated glutamate signalling. The authors accordingly employ an NMDA antagonist to stop this mechanism, looking for the effect of this manipulation on visually evoked activity recorded in EEG.

The motivating hypothesis for the paper is that NMDA antagonism should stop recurrent activity, and that this should degrade perceptual activity supporting perception of a contour illusion, but not other types of visual experience. Results in fact show the opposite. Rather than degrading cortical activity evoked by the illusion, memantine makes it more likely that machine learning classification of EEG will correctly infer the presence of the illusion.

On the face of it, this is confusing. But the paper does a good job of providing possible accounts based on specific details of neurochemical signalling and receptor populations.

I broadly find the paper interesting, graceful, and creative. The hypotheses are clear and compelling, the techniques for both manipulation of brain state and observation of that impact are cutting edge and well suited, and the paper draws clear and convincing conclusions that are made necessary by the results. The work sits at the very interesting crux of systems neuroscience, neuroimaging, and pharmacology.

Reviewer #2 (Public review):

This study presents an important finding to the field interested in recurrent processing and the role of NMDA-receptors herein. The evidence for improved decoding under memantine is convincing, while some open questions remain to be followed up in future studies (the lack of a behavioural effect, why is decoding improved rather than decreased?). It is an excellent example of how an unexpected finding can generate novel research ideas to the mechanisms underlying recurrent processing, suggesting that the answer lies in the differences in the effects of ketamine and memantine, rather than their commonalities.

I would like to thank the authors for the great care they have taken in addressing my concerns. I think the revised manuscript is significantly easier to follow now that specific hypothesis have been formulated in the introduction, and the direction of the results is explicitly stated throughout the manuscript. I further appreciate the dampening of some of the claims that are not completely supported by the appropriate interactions.

I think the resulting manuscript is an incredibly exciting contribution to our understanding of NMDA-receptor function, and a great example of how an unexpected finding can raise questions that could potentially drive the field forward. It shows how NMDA's role in recurrent processing is much more complicate than previously assumed, and reveals that it is not the commonalities between memantine and ketamine that are important in understanding recurrent processing, but rather the differences. I look forward to future studies that will target these differences.

Overall great job.

Reviewer #3 (Public review):

Summary:

In this study, Stein and colleagues use a clever masking/attentional blink paradigm using Kanisza stimuli, coupled with EEG decoding and the NMDA antagonist memantine, to isolate putative neural markers of feedforward, lateral, and feedback processing.

In two elegant experiments, they show that memantine selective influences EEG decoding of only illusory Kanisza surfaces (but not contour continuation or raw contrast), only when unmasked, only when attention is available (not when "blinked"), and only when task-relevant.

This neatly implicates NMDA receptors in the feedback mechanisms that are believed to be involved in inferring illusory Kanisza surfaces, and builds a difficult bridge between the large body of human perceptual experiments and pharmacological and neurophysiological work in animals.

Strengths:

Three key strengths of the paper are 1) its elegant and thorough experimental design, which includes internal replication of some key findings, and 2) the clear pattern of results across the full set of experiments, and 3) its clear writing and presentation of results.

The paper effectively reports a 4-way interaction, with memantine only influencing decoding of surfaces (1) that are unmasked (2), with attention available (3) and task-relevant (4). Nevertheless, the results are very clear, with a clear separation between null effects on other conditions and quite a strong (and thus highly selective) effect on this one intersection of conditions. This makes the pattern of findings very convincing.

Weaknesses:

Overall this is an impressive and important paper. However, to my mind there are two minor weaknesses.

First, despite its clear pattern of neural effects, there is no corresponding perceptual effect. Although the manipulation fits neatly within the conceptual framework, and there are many reasons for not finding such an effect (floor and ceiling effects, narrow perceptual tasks etc), this does leave open the possibility that the observation is entirely epiphenomenal, and that the mechanisms being recorded here are not actually causally involved in perception per se.

Second, although it is clear that there is an effect on decoding in this particular condition, what that means is not entirely clear - particularly since performance improves, rather than decreases. It should be noted here that improvements in decoding performance do not necessarily need to map onto functional improvements, and we should all be careful to remain agnostic about what is driving classifier performance. Here too, the effect of memantine on decoding might be epiphenomenal - unrelated to the information carried in the neural population, but somehow changing the balance of how that is electrically aggregated on the surface of the skull. *Something* is changing, but that might be a neurochemical or electrical side-effect unrelated to actual processing (particularly since no corresponding behavioural impact is observed.)

Comments on revisions:

I think the authors responsed fairly to my comments. Even if they weren't really able to add new insight into why behaviour didn't show the same effects as decoding, they discuss this in the revised text.

Reviewer #1 (Public Review):

Many studies reported findings implying that rhizobial infection is associated with cell cycle re-entry and progression, however, our understanding has been fragmented. This study provides exciting new insights as it represents a comprehensive description of the cell cycle progression during early stages of nodulation using fluorescence markers.

To briefly summarize, the authors first monitor H3.1 / H3.3 replacement to distinguish between replicating (S phase) and non-replicating cells to show that M. truncatula cortex cells along the bacterial infection thread are non-replicating (while neighbors enter the S phase). Nuclear size measurements revealed that these non-replicative cells are in the post-replicative stage (G2) rather than in the pre-replicative G1 phase, which the authors confirm with the Plant Cell Cycle Indicator (PlaCCI) fluorescent marker to track cell cycle progression in more detail. Cortex cells in the trajectory of the infection thread did not accumulate the late G2 marker of the PlaCCI nor the G2/M marker KNOLLE, indicating that these cells indeed remain in G2. Because nuclear size measurements indicated that infected cells are polyploid, the authors used the centromere histone marker CENH3 to determine chromosome number. They find that cortex cells giving rise to the nodule primordium are endomitotic and tetraploid, probably because their cell cycle is halted at centromere separation. Although not a focus of this manuscript, the authors also use their fluorescent tools to track cell cycle progression during arbuscular mycorrhiza symbiosis. They confirm that infected cells transition from a replicating to a non-replicating state (H3.1 to H3.3) with progressing development of the arbuscules. In addition, the CENH3 marker confirms previous findings that cortex cells infected by fungi are endocycling (i.e., DNA synthesis without segregation of replicated parts). This represents an important confirmation of previous findings and contrasts with the situation during nodulation symbiosis, where chromosomes separate after replication.

In general, all microscopy images are of very high quality and support the authors' conclusions. While individually each set of fluorescent markers has its limitations, combined they constitute a powerful tool to track various stages of cell cycle progression in individual root cells during symbiosis. Overall, this is a very strong manuscript that comprehensively elucidates root cell cycle changes during microbial infection.

Reviewer #2 (Public Review):

Cell cycle control during nitrogen-fixing symbiosis is an important topic, but our understanding of the process is poor and lacks resolution, as the nodule is a complex organ with many cell types that undergo profound changes. The authors aim to define the cell cycle state of individual plant cells in the emerging nodule primordium, as a transcellular infection thread passes through the meristem to reach cells deep in the incipient nodule and releases bacteria to form symbiosomes. The authors used a number of cell cycle reporters, such as different Histone 3 variants and cyclins, to follow cell cycle progress in exquisite detail. They showed that the host cells in the path of an infection thread exhibit a cell fate distinct from their immediate neighbors: after entering the S phase similar to their neighbors, these cells exit the cell cycle and enter a special differentiated state. This is likely an important shift that allows the proper passage of the infection thread. Although definitive proof needs more investigation, they showed that a pioneering transcription factor, NF-YA1, likely represses these endoreduplicated cells from completing the cell cycle.

Reviewer #1 (Public review):

The structure of a heterohexameric 3:3 LGI1-ADAM22 complex is resolved by Yamaguchi et al. It reveals the intermolecular LGI1 interactions and its role in bringing three ADAM22 molecules together. This may be relevant for the clustering of axonal Kv1 channels and control over their density. While it is currently not clear if the heterohexameric 3:3 LGI1-ADAM22 complex has a physiological role, the detailed structural information presented here allows to pinpoint mutations or other strategies to probe the relevance of the 3:3 complex in future work.

The experimental work is done to a high standard, and all my comments have been addressed. This new version of the manuscript has been improved substantially, and the figures have been enhanced and clarified.

Reviewer #1 (Public review):

This study exploits novel agent (IMT) that inhibits mitochondrial activity in combination with venetoclax. While the concept is not novel, the agent is novel (inhibitor of the mitochondrial RNA polymerase, described in Nature in other tumor models), and quest for safe mitochondrial inhibitors is highly warranted. The strength is in vivo activity data shown in CLDX and in one of the two AML PDX models tested, and apparent safety of the combination. However, the impact on survival is impressive in CLDX but not in PDX, and unclear why Ven-sensitive PDX is resistant to combination (opposite what cell line data show). There is no real evidence that this agent overcome Ven resistance, which could be done for example in primary AML cells. Finally, no on-target pharmacodynamic endpoints are measured in vivo to support the activity of the compound on mitochondrial activity at the doses used (which are safe).

Both Reviewers requested to demonstrate that IMT1 inhibits the target at doses used in vitro or in vivo; while the prior paper showed this for original compound, it is imperative to demonstrate this for this modified agent in a different tumor type such as AML.

These points have not been addressed in the Revision.

Reviewer #2 (Public review):

Summary:

The manuscript by Arabanian and colleagues presents studies showing how inhibition of mitochondrial transcription and replication with a novel inhibitor of the mitochondrial polymerase, IMT, can promote AML cell death in combination with the Bcl2 inhibitor venetoclax. They further show that this combinatorial efficacy is evident in vivo in both the AML cell line MV411 and in a PDX model. Given the multiple studies showing the importance of Oxphos in maintaining AML cell survival, the current studies provide an additional strategy to inhibit Oxphos and thus improve the therapeutic management of AML.

Strengths:

A novel aspect of this work is that IMT is a new class of mitochondrial inhibitor that acts through inhibiting the mitochondrial polymerase. In addition, the demonstration of therapeutic efficacy both in vitro and in vivo (including with PDX), together with some data showing minimal toxicity, adds to the impact of this work. Their overall conclusion that IMT increases the potency of Vex in treating AMLs is supported.

Comments on revisions:

In all, the authors responded to most of the critiques, while two of the major critiques were not experimentally addressed. The work will still have potential impact, but will depend on further studies under more clinically relevant conditions and with a better understanding of drug effects.

Reviewer #1 (Public review):

Summary:

The study by Deng et al reports single cell expression analysis of developing mouse hearts and examines the requirements for cardiac fibroblasts in heart maturation. The work includes extensive gene expression profiling and bioinformatic analysis. The prenatal fibroblast ablation studies show new information on the requirement of these cells on heart maturation before birth.

The strengths of the manuscript are the new single cell datasets and comprehensive approach to ablating cardiac fibroblasts in pre and postnatal development in mice. Extensive data are presented on mouse embryo fibroblast diversity and morphology in response to fibroblast ablation. Histological data support localization of major cardiac cell types and effects of fibroblast ablation on cardiac gene expression at different times of development.

A weakness of the study is that the major conclusions regarding collagen signaling and heart maturation are based on gene expression patterns and are not functionally validated.

Reviewer #2 (Public review):

This study aims to elucidate the role of fibroblasts in regulating myocardium and vascular development through signaling to cardiomyocytes and endothelial cells. This focus is significant, given that fibroblasts, cardiomyocytes, and vascular endothelial cells are the three primary cell types in the heart. The authors employed a Pdgfra-CreER-controlled diphtheria toxin A (DTA) system to ablate fibroblasts at various embryonic and postnatal stages, characterizing the resulting cardiac defects, particularly in myocardium and vasculature development. Single-cell RNA sequencing (scRNA-seq) analysis of the ablated hearts identified collagen as a crucial signaling molecule from fibroblasts that influences the development of cardiomyocytes and vascular endothelial cells.

This is an interesting manuscript; however, there are several major issues, including an over-reliance on the scRNA-seq data, which shows inconsistencies between replicates.

Some of the major issues are described below.

(1) The CD31 immunostaining data (Figure 3B-G) indicate a reduction in endothelial cell numbers following fibroblast deletion using PdgfraCreER+/-; RosaDTA+/- mice. However, the scRNA-seq data show no percentage change in the endothelial cell population (Figure 4D). Furthermore, while the percentage of Vas_ECs decreased in ablated samples at E16.5, the results at E18.5 were inconsistent, showing an increase in one replicate and a decrease in another, raising concerns about the reliability of the RNA-seq findings.

(2) Similarly, while the percentage of Ven_CMs increased at E18.5, it exhibited differing trends at E16.5 (Fig. 4E), further highlighting the inconsistency of the scRNA-seq analysis with the other data.

(3) Furthermore, the authors noted that the ablated samples had slightly higher percentages of cardiomyocytes in the G1 phase compared to controls (Fig. 4H, S11D), which aligns with the enrichment of pathways related to heart development, sarcomere organization, heart tube morphogenesis, and cell proliferation. However, it is unclear how this correlates with heart development, given that the hearts of ablated mice are significantly smaller than those of controls (Figure 3E). Additionally, the heart sections from ablated samples used for CD31/DAPI staining in Figure 3F appear much larger than those of the controls, raising further inconsistencies in the manuscript.

(4) The manuscript relies heavily on the scRNA-seq dataset, which shows inconsistencies between the two replicates. Furthermore, the morphological and histological analyses do not align with the scRNA-seq findings.

(5) There is a lack of mechanistic insight into how collagen, as a key signaling molecule from fibroblasts, affects the development of cardiomyocytes and vascular endothelial cells.

(6) In Figure 1B, Col1a1 expression is observed in the epicardial cells (Figure 1A, E11.5), but this is not represented in the accompanying cartoon.

(7) Do the PdgfraCreER+/-; RosaDTA+/- mice survive after birth when induced at E15.5, and do they exhibit any cardiac defects?

Reviewer #3 (Public review):

Summary:

The authors investigated fibroblasts' communication with key cell types in developing and neonatal hearts, with focus on critical roles of fibroblast-cardiomyocyte and fibroblast-endothelial cells network in cardiac morphogenesis. They tried to map the spatial distribution of these cell types and reported the major pathways and signaling molecules driving the communication. They also used Cre-DTA system to ablate Pdgfra labeled cells and observed myocardial and endothelial cell defects at development. They screened the pathways and genes using sequencing data of ablated heart. Lastly they reported a compensatory collagen expression in long term ablated neonate heart. Overall, this study provides us with important insight on fibroblasts' roles in cardiac development and will be a powerful resource for collagens and ECM focused research.

Strengths:

The authors utilized good analyzing tools to investigate on multiple database of single cell sequencing and Multi-seq. They identified significant pathways, cellular and molecular interactions of fibroblasts. Additionally, they compared some of their analytic findings with human database, and identified several groups of ECM genes with varying roles in mice.

Weaknesses:

This study is majorly based on sequencing data analysis. At the bench, they used very strident technique to study fibroblast functions by ablating one of the major cell population of heart. Also, experimental validation of their analyzed downstream pathways will be required eventually.

Reviewer #1 (Public review):

The authors, Zhang et al., demonstrate the beneficial effects of treating degenerate human primary intervertebral disc (IVD) cells with recombinant human PDGF-AB/BB on the senescence transcriptomic signatures. Utilizing a combination of degenerate cells from elderly humans and experimentally induced senescence in young, healthy IVD cells, the authors show the therapeutic effects on mRNA transcription as well as cellular processes through informatics approaches.

One notable strength of this study is the use of human primary cells and recombinant forms of human PDGF-AB/BB proteins, which increases the translational potential of these in vitro studies. The manuscript is well-written, and the informatics analyses are thorough and clearly presented.

Comments on revisions:

The revised manuscript adds greater clarity, and the impact of the study is greatly enhanced.

Reviewer #2 (Public review):

Summary:

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

Strengths:

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

Weaknesses:

A weakness of these studies relates to qualitative data presented for the B-galactosidase assay. Quantification of such data sets would greatly strengthen the studies and lend further support to the hypotheses. The study in its current form could be strengthened by the inclusion of mechanistic studies probing the downstream PDGF receptor associated pathways for example specifically targeting or modulating the activity of the PDGF receptor PDGFRA.

Reviewer #1 (Public review):

Summary:

Zhao and colleagues employ Drosophila nephrocytes as a model to investigate the effects of a high-fat diet on these podocyte-like cells. Through a highly focused analysis, they initially confirm previous research in their hands demonstrating impaired nephrocyte function and move on to observe the mislocalization of a slit diaphragm-associated protein (pyd) and a knock-in into the locus of the Drosophila nephrin (sns). Employing another reporter construct, they identify activation of the JAK/STAT signaling pathway in nephrocytes. Subsequently, the authors demonstrate the involvement of this pathway in nephrocyte function from multiple angles, using a gain-of-function construct, silencing of an inhibitor, and ectopic overexpression of a ligand. Silencing the effector Stat92E via RNAi or inhibiting JAK/STAT with Methotrexate effectively restored impaired nephrocyte function and slit diaphragm architecture induced by a high-fat diet, while showing no impact under normal dietary conditions.

Strengths:

The findings establish a link between JAK/STAT activity and the impact of a high-fat diet on nephrocytes. This nicely underscores the importance of organ crosstalk for nephrocytes and supports a potential role for JAK/STAT in diabetic nephropathy, as previously suggested by other models.

Weaknesses:

While the analysis provides valuable insights, it appears somewhat over-reliant on tracer uptake in certain instances. Clinical inferences based on a Drosophila model should be interpreted with caution.

Reviewer #2 (Public review):

Summary:

In their manuscript, Zhao et al. describe a link between JAK-STAT pathway activation in nephrocytes upon a high-fat diet. Nephrocytes are the homologs to mammalian podocytes, and it has been previously shown that metabolic syndrome and obesity is associated with worse outcomes for chronic kidney disease. A study from 2021 (Lubojemska et al.) could already confirm a severe nephrocyte phenotype upon feeding Drosophila a high fat diet and also linking lipid overflow by expressing adipose triglyceride lipase in the fat body to nephrocyte dysfunction. In this study, the authors identified a second pathway and mechanism, how lipid dysregulation impact on nephrocyte function. In detail, they show an activation of JAK-STAT signaling in nephrocytes upon feeding a high-fat diet, which was induced by Upd2 expression (a leptin-like hormone) in the fat body, the adipose tissue in Drosophila. Further, they could show genetic and pharmacological interventions can reduce JAK-STAT activation and thereby prevent the nephrocyte phenotype in the high-fat diet model.

Strengths:

The strength of this study is the combination of genetic tools and pharmacological intervention to confirm a mechanistic link between the fat body/adipose tissue and nephrocytes. Inter-organ communication is crucial in the development of several diseases, but the underlying mechanisms are only poorly understood. Using Drosophila, it is possible to investigate several players of one pathway, here JAK-STAT. This was done, by investigating the functional role of Hop, Socs36E and Stat92E in nephrocytes and has also been combined with feeding a high-fat diet, to assess restoration of nephrocyte morphology and function by inhibiting JAK-STAT signaling. Adding a translational approach was done by inhibiting JAK-STAT signaling with methotrexate, which also resulted in attenuated nephrocyte dysfunction. Expression of the leptin-like hormone upd2 in the fat body is a good approach to study inter-organ communication and the impact of other organs/tissue on nephrocyte function and expands their findings from nephrocyte function towards whole animal physiology.

Weaknesses:

Although the general findings of this study are of great interest, the number of flies investigated for the majority of the experiments is very low (6 flies). Also it is not clear whether the 6 flies used are from independent experiments to exclude differences in food/diet.

Reviewer #1 (Public review):

Summary:

The authors use microscopy experiments to track the gliding motion of filaments of the cyanobacteria Fluctiforma draycotensis. They find that filament motion consists of back and forth trajectories along a "track", interspersed with reversals of movement direction, with no clear dependence between filament speed and length. It is also observed that longer filaments can buckle and form plectonemes. A computational model is used to rationalize these findings.

Strengths:

Much work in this field focuses on molecular mechanisms of motility; by tracking filament dynamics this work helps to connect molecular mechanisms to environmentally and industrially relevant ecological behavior such as aggregate formation.

The observation that filaments move on tracks is interesting and potentially ecologically signifiant.

The observation of rotating membrane-bound protein complexes and tubular arrangement of slime around the filament provide important clues to the mechanism of motion.

The observation that long filaments buckle has potential to shed light on the nature of mechanical forces in the filaments, e.g. through study of the length dependence of buckling.

The comparison between motility on agar and on glass is interesting since it shows that filaments have both intrinsic propensity to reverse (that is seen on glass) and mechanically triggered reversal (that is seen on agar when the filament reaches the end of a track).

Weaknesses:

The manuscript makes the interesting statement that the distribution of speed vs filament length is uniform, which would constrain the possibilities for mechanical coupling between the filaments. However Fig 2C does not show a uniform distribution but rather an apparent lack of correlation between speed and filament length, although the statistical degree of correlation is not given. In my view, Fig 2C should not be described as a uniform distribution since mathematically that means something very different than what is shown here. Instead the figure should be described quantitatively with the use of a measured correlation coefficient. This also applies to Fig. S3A.

The statement "since filament speed results from a balance between propulsive forces and drag, these observations of no or positive correlation between filament speed and length show that all (or a fixed proportion of) cells in a filament contribute to propulsive force generation" helps to clarify the important link between Fig 2C and the concept that all cells contribute, but I think this statement is not obvious for many readers, and could be made clearer, e.g. by the use of a simple mathematical model for a chain of bacterial that accounts for drag forces and propulsion forces for each bacterium.

The authors have now clarified that the computational model is 1D and cannot explain the coupling between rotation, slime generation and motion. I find it encouraging and important that model predictions for the dwell time distributions (Fig S12 and S13) are similar to experimental measurements, but I think it would be better to put these results in the main text, together also with Fig S4. If these important results are in the supplement it is harder for the reader to assess the match between model and experiments.

Filament buckling is not analysed in quantitative detail, but the authors have now clarified that this will be the topic of future work with a 2D or 3D computational model.

Reviewer #2 (Public review):

Summary:

The authors combined time-lapse microscopy with biophysical modeling to study the mechanisms and timescales of gliding and reversals in filamentous cyanobacterium Fluctiforma draycotensis. They observed the highly coordinated behavior of protein complexes moving in a helical fashion on cells' surfaces and along individual filaments as well as their de-coordination, which induces buckling in long filaments.

Strengths:

The authors provided concrete experimental evidence of cellular coordination and de-coordination of motility between cells along individual filaments. The evidence is comprised of individual trajectories of filaments that glide and reverse on surfaces as well as the helical trajectories of membrane-bound protein complexes that move on individual filaments and are implicated in generating propulsive forces.

Limitations:

The biophysical model is one-dimensional and thus does not capture the buckling observed in long filaments. I expect that the buckling contains useful information since it reflects the competition between bending rigidity, the speed at which cell synchronization occurs, and the strength of the propulsion forces.

Future directions:

The study highlights the need to identify molecular and mechanical signaling pathways of cellular coordination. In analogy to the many works on the mechanisms and functions of multi-ciliary coordination, elucidating coordination in cyanobacteria may reveal a variety of dynamic strategies in different filamentous cyanobacteria.

Reviewer #3 (Public review):

Summary:

The authors present new observations related to the gliding motility of the multicellular filamentous cyanobacteria Fluctiforma draycotensis. The bacteria move forward by rotating their about their long axis, which causes points on the cell surface to move along helical paths. As filaments glide forward they form visible tracks. Filaments preferentially move within the tracks. The authors device a simple model in which each cell in a filament exerts a force that either pushes forwards or backwards. Mechanical interactions between cells cause neighboring cells to align the forces they exert. The model qualitatively reproduces the tendency of filaments to move in a concerted direction and reverse at the end of tracks.

The authors seek to understand how cells in a filament synchronize their motion to move in a concerted direction. This question connects to the evolution of multicellular life and so is important well beyond the specific field of cyanobacterial locomotion.

Strengths:

The biophysical model used to describe cell-cell coordination of locomotion is clear and reasonable. This model provides a useful phenomenological framework in which to consider the roles of individual cells in the coordinated motion of the group. The qualitative consistency between theory and observation suggests that this model captures some essential qualities of the true system.

The observation that filaments reverse at the ends of tracks is compelling, but difficult to clearly connect to any one microscopic model.

The observations of helical motion of the filament are compelling.

Weaknesses:

The comparison of theory and observation is mainly qualitative. While the authors have done a good job fitting the observations to the theory, it is not possible to systematically vary parameters, independently estimate parameter values, or apply external forces. Consequently, more experiments are needed before the proposed model can the accepted or rejected. This manuscript provides a promising hypothesis but not a compelling justification for it.

Reviewer #1 (Public review):

Summary:

The manuscript by Yamamoto et al. presents a model by which the four main axes of the limb are required for limb regeneration to occur in the axolotl. A longstanding question in regeneration biology is how existing positional information is used to regenerate the correct missing elements. The limb provides an accessible experimental system by which to study the involvement of the anteroposterior, dorsoventral, and proximodistal axes in the regenerating limb. Extensive experimentation has been performed in this area using grafting experiments. Yamamoto et al. use the accessory limb model and some molecular tools to address this question. There are some interesting observations in the study. In particular, one strength is the potent induction of accessory limbs in the dorsal axis with BMP2+Fgf2+Fgf8, which is very interesting.

Strengths:

The manuscript presents some novel phenotypes generated in axolotl limbs due to Wnt signaling. This is generally the first example in which Wnt signaling has provided a gain-of-function in the axolotl limb model. They also present a potent way of inducing limb patterning in the dorsal axis by the addition of just beads loaded with Bmp2+Fgf8+Fgf2.

Weaknesses:

Although interesting, the study makes bold claims about determining the molecular basis of DV positional cues, but the experimental evidence is not definitive and does not take into account the previous work on DV patterning in the amniote limb. Also, testing the hypothesis on blastemas after limb amputation would be needed to support the strong claims in the study. There are several examples of very strong claims, but the evidence lacks support for these claims.

Reviewer #2 (Public review):

Summary:

This study explores how signals from all sides of a developing limb, front/back and top/bottom, work together to guide the regrowth of a fully patterned limb in axolotls, a type of salamander known for its impressive ability to regenerate limbs. Using a model called the Accessory Limb Model (ALM), the researchers created early limb regenerates (called blastemas) with cells from different sides of the limb. They discovered that successful limb regrowth only happens when the blastema contains cells from both the top (dorsal) and bottom (ventral) of the limb. They also found that a key gene involved in front/back limb patterning, called Shh (Sonic hedgehog), is only turned on when cells from both the dorsal and ventral sides come into contact. The study identified two important molecules, Wnt10B and FGF2, that help activate Shh when dorsal and ventral cells interact. Finally, the authors propose a new model that explains how cells from all four sides of a limb, dorsal, ventral, anterior (front), and posterior (back), contribute at both the cellular and molecular level to rebuilding a properly structured limb during regeneration.

Strengths:

The techniques used in this study, like delicate surgeries, tissue grafting, and implanting tiny beads soaked with growth factors, are extremely difficult, and only a few research groups in the world can do them successfully. These methods are essential for answering important questions about how animals like axolotls regenerate limbs with the correct structure and orientation. To understand how cells from different sides of the limb communicate during regeneration, the researchers used a technique called in situ hybridization, which lets them see where specific genes are active in the developing limb. They clearly showed that the gene Shh, which helps pattern the front and back of the limb, only turns on when cells from both the top (dorsal) and bottom (ventral) sides are present and interacting. The team also took a broad, unbiased approach to figure out which signaling molecules are unique to dorsal and ventral limb cells. They tested these molecules individually and discovered which could substitute for actual dorsal and ventral cells, providing the same necessary signals for proper limb development. Overall, this study makes a major contribution to our understanding of how complex signals guide limb regeneration, showing how different regions of the limb work together at both the cellular and molecular levels to rebuild a fully patterned structure.

Weaknesses:

Because the expressional analyses are performed on thin sections of regenerating tissue, they provide only a limited view of the gene expression patterns in their experiments, opening the possibility that they could be missing some expression in other regions of the blastema. Additionally, the quantification method of the expressional phenotypes in most of the experiments does not appear to be based on a rigorous methodology. Therefore, performing alternate expressional analysis, using RNA-seq or qRT-PCR (for example) on the entire blastema would help validate that the authors are not missing something.

Overall, the number of replicates per sample group is quite low (sometimes as low as 3), which is especially risky with challenging techniques like the ones the authors employ. The authors don't appear to have performed a power analysis to calculate the number of animals used in each experiment that are sufficient to identify possible statistical differences between groups. Increasing the sample sizes would substantially increase the rigor of their experiments.

Likewise, the authors' use of an AI-generated algorithm to quantify symmetry on the dorsal/ventral axis, and this approach doesn't appear to account for possible biases due to tissue sectioning angles. They also appear to arbitrarily pick locations in each sample group to compare symmetry measurements. There are other methods, which include using specific muscle groups and nerve bundles as dorsal/ventral landmarks, that would more clearly show differences in symmetry.

Reviewer #3 (Public review):

Summary:

After salamander limb amputation, the cross-section of the stump has two major axes: anterior-posterior and dorsal-ventral. Cells from all axial positions (anterior, posterior, dorsal, ventral) are necessary for regeneration, yet the molecular basis for this requirement has remained unknown. To address this gap, Yamamoto et al. took advantage of the ALM assay, in which defined positional identities can be combined on demand and their effects assessed through the outgrowth of an ectopic limb. They propose a compelling model in which dorsal and ventral cells communicate by secreting Wnt10b and Fgf2 ligands, respectively, with this interaction inducing Shh expression in posterior cells. Shh was previously shown to induce limb outgrowth in collaboration with anterior Fgf8 (PMID: 27120163). Thus, this study completes a concept in which four secreted signals from four axial positions interact for limb patterning. Notably, this work firmly places dorsal-ventral interactions upstream of anterior-posterior, which is striking for a field that has been focussed on anterior-posterior communication. The ligands identified (Wnt10b, Fgf2) are different from those implicated in dorsal-ventral patterning in the non-regenerative mouse and chick models. The results in the context of ALM/ectopic limb engineering are impressive, but the authors do not extend their experiments to assay 'normal' regeneration after amputation.

Strengths:

(1) The ALM and use of GFP grafts for lineage tracing (Figures 1-3) take full advantage of the salamander model's unique ability to outgrow patterned limbs under defined conditions. As far as I am aware, the ALM has not been combined with precise grafts that assay 2 axial positions at once, as performed in Figure 3. The number of ALMs performed in this study deserves special mention, considering the challenging surgery involved.

(2) The authors identify that posterior Shh is not expressed unless both dorsal and ventral cells are present. This echoes previous work in mouse limb development models (AER/ectoderm-mesoderm interaction), but this link between axes was not known in salamanders. The authors elegantly reconstitute dorsal-ventral communication by grafting, finding that this is sufficient to trigger Shh expression (Figure 3 - although see also the Weaknesses section.)

(3) Impressively, the authors discovered two molecules sufficient to substitute dorsal or ventral cells through electroporation into dorsal- or ventral-depleted ALMs (Figure 5). These molecules did not change the positional identity of target cells. The same group previously identified the ventral factor (Fgf2) to be a nerve-derived factor essential for regeneration. In Figure 6, the authors demonstrate that nerve-derived factors, including Fgf2, are alone sufficient to grow out ectopic limbs from a dorsal wound. Limb induction with a 3-factor cocktail without supplementing with other cells is conceptually important for regenerative engineering.

(4) The writing style and presentation of results are very clear.

Weaknesses:

(1) The expression data are the weakest part of this study.

• Despite being a central message, I found the Shh in situs unconvincing (e.g. Figure 2I, 3C, 5C), especially without sense probe controls. An additional assay would be essential to make the Shh data convincing - perhaps like in Figure 5D (qPCR?), RNA-sequencing, or a downstream target gene.

• It is not clear what the n numbers mean for the in situ data (slides analysed / number of biological samples / other?). This is crucial to understanding the reliability of the results.

• The authors do not assay where and when Wnt10b and Fgf2 are expressed beyond the bulk RNA-sequencing (which presumably contains both epidermis and mesenchyme cells). This is a shame, as understanding which cell types express these molecules, and when, would be important for understanding the mechanism.

(2) It is important to consider that the ALM is not 'regeneration', even if the authors have previously argued that ALM bumps and regenerating blastemas are equivalent (PMID: 17959163). The start- and end- points of ALM are different from regeneration, even though there are undoubtedly common principles involved. Thus, I find the word 'regeneration' in the title and last sentence of the abstract unsubstantiated unless evidence is provided that the same mechanisms (Wnt10b/Fgf2/Shh) function during normal limb regeneration.

(3) Drawing the exact boundaries of the Ant/Pos/Dor/Ven BL and grafts in the cartoon in Figure 1 (with respect to anatomical landmarks) would help to better understand the experiments in Figures 3 and 4.

(4) I find the 'positional cue' and 'positional value' terminology confusing, despite the authors' efforts. It is not clear if they refer to cell autonomous or secreted signals, and, as the authors mention, the definitions partially overlap. Lmx1b is defined as a positional value, even though it is necessary and sufficient for dorsal identity (so, isn't it positional information?). Much simpler would be to describe Wnt10b and Fgf2 as what they are: dorsally or ventrally expressed signals that substitute for dorsal or ventral tissue without inducing changes in positional information.

Overall appraisal:

This is a logical and well-executed study that creatively uses the axolotl model to advance an important framework for understanding limb patterning. The reliability of the Shh expression data is a weak point in this otherwise impressive study. The relevance of the mechanisms to normal limb regeneration is not substantiated.

Joint Public Review:

Summary:

The authors investigate how stochastic and deterministic factors are integrated in cell fate decisions, using Dictyostelium discoideum as a model system. They show that cells in different cell cycle phases (a deterministic factor) are predisposed to different fates, albeit with deviations, when exposed to the same environmental stimulus. However, gene expression variability (a stochastic factor) enhances the robustness of cellular responses to environmental cues that disrupt the cell cycle.

Using a simple, tractable mathematical model, the authors demonstrate that cell fate decisions in D. discoideum depend on a combination of deterministic and stochastic factors, i.e., cell cycle phase and gene expression variability, respectively. They then identify Set1 - a key regulator of gene expression variability - indicate the mechanism through which it modulates this variability, and link it to a phenotype in D. discoideum development. Finally, they confirm that gene expression variability contributes to the robustness of the cell's response to environmental disruptions that interfere with the cell cycle.

Strengths:

The authors are careful in the choice of their experiments and in measuring gene expression variability, using methods that account for expected trends with average gene expression.

Weaknesses:

However, in terms of mathematical modelling, it would be important to rule out sources of stochasticity (other than gene expression variability), and also to consider cases where stochastic factors are not necessarily completely independent of the deterministic ones.

Reviewer #1 (Public review):

Summary:

These authors have asked how lytic phage predation impacts antibiotic resistance and virulence phenotypes in methicillin-resistant Staphylococcus aureus (MRSA). They report that staphylococcal phages cause MRSA strains to become sensitized to b-lactams and to display reduced virulence. Moreover, they identify mutations in a set of genes required for phage infection that may impact antibiotic resistance and virulence phenotypes.

Strengths:

Phage-mediated re-sensitization to antibiotics has been reported previously but the underlying mutational analyses have not been described. These studies suggest that phages and antibiotics may target similar pathways in bacteria.

Weaknesses:

One limitation is the lack of mechanistic investigations linking particular mutations to the phenotypes reported here. This limits the impact of the work.

Another limitation of this work is the use of lab strains and a single pair of phages. However, while incorporation of clinical isolates would increase the translational relevance of this work it is unlikely to change the conclusions.

Comments on revisions:

The authors have addressed my concerns.

Reviewer #2 (Public review):

Summary:

The work presented in the manuscript by Tran et al deals with bacterial evolution in the presence of bacteriophage. Here, authors have taken three methicillin-resistant S. aureus strains that are also resistant to beta-lactams. Eventually, upon being exposed to phage, these strains develop beta-lactam sensitivity. Besides this, the strains also show other changes in their phenotype such as reduced binding to fibrinogen and hemolysis.

Strengths:

The experiments carried out are convincing to suggest such in vitro development of sensitivity to the antibiotics. Authors were also able to "evolve" phage in similar fashion thus showing enhanced virulence against the bacterium. In the end, authors carry out DNA sequencing of both evolved bacteria and phage and show mutations occurring in various genes. Overall, the experiments that have been carried out are convincing.

Weaknesses:

None. In the current version of the manuscript, I find the study complete.

Reviewer #1 (Public review):

Summary:

These authors have asked how lytic phage predation impacts antibiotic resistance and virulence phenotypes in methicillin-resistant Staphylococcus aureus (MRSA). They report that staphylococcal phages cause MRSA strains to become sensitized to b-lactams and to display reduced virulence. Moreover, they identify mutations in a set of genes required for phage infection that may impact antibiotic resistance and virulence phenotypes.

Strengths:

Phage-mediated re-sensitization to antibiotics has been reported previously but the underlying mutational analyses have not been described. These studies suggest that phages and antibiotics may target similar pathways in bacteria.

Weaknesses:

One limitation is the lack of mechanistic investigations linking particular mutations to the phenotypes reported here. This limits the impact of the work.

Another limitation of this work is the use of lab strains and a single pair of phages. However, while incorporation of clinical isolates would increase the translational relevance of this work it is unlikely to change the conclusions.

Reviewer #2 (Public review):

Summary:

The work presented in the manuscript by Tran et al deals with bacterial evolution in the presence of bacteriophage. Here, the authors have taken three methicillin-resistant S. aureus strains that are also resistant to beta-lactams. Eventually, upon being exposed to phage, these strains develop beta-lactam sensitivity. Besides this, the strains also show other changes in their phenotype such as reduced binding to fibrinogen and hemolysis.

Strengths:

The experiments carried out are convincing to suggest such in vitro development of sensitivity to the antibiotics. Authors were also able to "evolve" phage in a similar fashion thus showing enhanced virulence against the bacterium. In the end, authors carry out DNA sequencing of both evolved bacteria and phage and show mutations occurring in various genes. Overall, the experiments that have been carried out are convincing.

Weaknesses:

Although more experiments are not needed, additional experiments could add more information. For example, the phage gene showing the HTH motif could be reintroduced in the bacterial genome and such a strain can then be assayed with wildtype phage infection to see enhanced virulence as suggested. At least one such experiment proves the discoveries regarding the identification of mutations and their outcome. Secondly, I also feel that authors looked for beta-lactam sensitivity and they found it. I am sure that if they look for rifampicin resistance in these strains, they will find that too. In this case, I cannot say that the evolution was directed to beta-lactam sensitivity; this is perhaps just one trait that was observed. This is the only weakness I find in the work. Nevertheless, I find the experiments convincing enough; more experiments only add value to the work.

Reviewer #2 (Public review):

Summary:

This study uses in vivo multimodal high-resolution imaging to track how microglia and neutrophils respond to light-induced retinal injury from soon after injury to 2 months post-injury. The in vivo imaging finding was subsequently verified by ex vivo study. The results suggest that despite the highly active microglia at the injury site, neutrophils were not recruited in response to acute light-induced retinal injury.

Strengths:

An extremely thorough examination of the cellular-level immune activity at the injury site. In vivo imaging observations being verified using ex vivo techniques is a strong plus.

Reviewer #3 (Public review):

Summary

This work investigated the immune response in the murine retina after focal laser lesions. These lesions are made with close to 2 orders of magnitude lower laser power than the more prevalent choroidal neovascularization model of laser ablation. Histology and OCT together show that the laser insult is localized to the photoreceptors and spares the inner retina, the vasculature and the pigment epithelium. As early as 1-day after injury, a loss of cell bodies in the outer nuclear layer is observed. This is accompanied by strong microglial proliferation to the site of injury in the outer retina where microglia do not typically reside. The injury did not seem to result in the extravasation of neutrophils from the capillary network, constituting one of the main findings of the paper. The demonstrated paradigm of studying the immune response and potentially retinal remodeling in the future in vivo is valuable and would appeal to a broad audience in visual neuroscience.

Strengths

Adaptive optics imaging of murine retina is cutting edge and enables non-destructive visualization of fluorescently labeled cells in the milieu of retinal injury. As may be obvious, this in vivo approach is a benefit for studying fast and dynamic immune processes on a local time scale - minutes and hours, and also for the longer days-to-months follow-up of retinal remodeling as demonstrated in the article. In certain cases, the in vivo findings are corroborated with histology.

The analysis is sound and accompanied by stunning video and static imagery. A few different sets of mouse models are used: a) two different mouse lines, each with a fluorescent tag for neutrophils and microglia, b) two different models of inflammation - endotoxin-induced uveitis (EAU) and laser ablation are used to study differences in the immune interaction.

One of the major advances in this article is the development of the laser ablation model for 'mild' retinal damage as an alternative to the more severe neovascularization models. This model would potentially allow for controlling the size, depth and severity of the laser injury opening interesting avenues for future study.

The time-course, 2D and 3D spatial activation pattern of microglial activation are striking and provide an unprecedented view of the retinal response to mild injury.

Editor's note: The authors have addressed all the previous concerns raised by the reviewers.

Reviewer #1 (Public review):

Summary:

In this study, authors explored how galanin affects whole-brain activity in larval zebrafish using wide-field Ca2+ imaging, genetic modifications, and drugs that increase brain activity. The authors conclude that galanin has a sedative effect on the brain under normal conditions and during seizures, mainly through the galanin receptor 1a (galr1a). However, acute "stressors(?)" like pentylenetetrazole (PTZ) reduce galanin's effects, leading to increased brain activity and more seizures. Authors claim that galanin can reduce seizure severity while increasing seizure occurrence, speculated to occur through different receptor subtypes. This study confirms galanin's complex role in brain activity, supporting its potential impact on epilepsy.

Strengths:

The overall strength of the study lies primarily in its methodological approach using whole-brain Calcium imaging facilitated by the transparency of zebrafish larvae. Additionally, the use of transgenic zebrafish models is an advantage, as it enables genetic manipulations to investigate specific aspects of galanin signaling. This combination of advanced imaging and genetic tools allows for addressing galanin's role in regulating brain activity.

Weaknesses:

The weaknesses of the study also stem from the methodological approach, particularly the use of whole-brain Calcium imaging as a measure of brain activity. While epilepsy and seizures involve network interactions, they typically do not originate across the entire brain simultaneously. Seizures often begin in specific regions or even within specific populations of neurons within those regions. Therefore, a whole-brain approach, especially with Calcium imaging with inherited limitations, may not fully capture the localized nature of seizure initiation and propagation, potentially limiting the understanding of Galanin's role in epilepsy.

Furthermore, Galanin's effects may vary across different brain areas, likely influenced by the predominant receptor types expressed in those regions. Additionally, the use of PTZ as a "stressor" is questionable since PTZ induces seizures rather than conventional stress. Referring to seizures induced by PTZ as "stress" might be a misinterpretation intended to fit the proposed model of stress regulation by receptors other than Galanin receptor 1 (GalR1).

The description of the EAAT2 mutants is missing crucial details. EAAT2 plays a significant role in the uptake of glutamate from the synaptic cleft, thereby regulating excitatory neurotransmission and preventing excitotoxicity. Authors suggest that in EAAT2 knockout (KO) mice galanin expression is upregulated 15-fold compared to wild-type (WT) mice, which could be interpreted as galanin playing a role in the hypoactivity observed in these animals.

However, the study does not explore the misregulation of other genes that could be contributing to the observed phenotype. For instance, if AMPA receptors are significantly downregulated, or if there are alterations in other genes critical for brain activity, these changes could be more important than the upregulation of galanin. The lack of wider gene expression analysis leaves open the possibility that the observed hypoactivity could be due to factors other than, or in addition to, galanin upregulation.

Moreover, the observation that in double KO mice for both EAAT2 and galanin there was little difference in seizure susceptibility compared to EAAT2 KO mice alone further supports the idea that galanin upregulation might not be the reason to the observed phenotype. This indicates that other regulatory mechanisms or gene expressions might be playing a more pivotal role in the manifestation of hypoactivity in EAAT2 mutants.

These methodological shortcomings and conceptual inconsistencies undermine the perceived strengths of the study, and hinders understanding of Galanin's role in epilepsy and stress regulation.

Comments on revisions:

The revised manuscript and the answers of the authors is appreciated. However, the criticisms were addressed only partially and main weaknesses of the manuscript are still remaining.

Reviewer #2 (Public review):

This revised study is an investigation of galanin and galanin receptor signaling on whole-brain activity in the context of recurrent seizure activity or under homeostatic basal conditions. The authors primarily use calcium imaging to observe whole-brain neuronal activity accompanied by galanin qPCR to determine how manipulations of galanin or the galr1a receptor affect the activity of the whole-brain under non-ictal conditions or when seizure activity occurs. The authors use their eaat2a-/- model (introduced in their Glia 2022 paper, PMID 34716961) that shows recurrent seizure activity as well as suppression of neuronal activity and locomotion interictally. It is compared to the well-known pentylenetetrazole (PTZ) pharmacological model of seizures in zebrafish. Given the literature cited in their Introduction, the authors hypothesize that galanin will exert a net inhibitory effect on brain activity in models of seizures/epilepsy. They were surprised to find that this hypothesis was only moderately supported in their eaat2a-/- model. In contrast, after PTZ, fish with galanin overexpression showed increased seizure number and reduced duration while fish with galanin KO showed reduced seizure number and increased duration.

Previous concerns about sex or developmental biological variables were addressed, as their model's seizure phenotype emerges rapidly and long prior to the establishment of zebrafish sexual maturity. However, in the course of re-review, some additional concerns (below) were detected that, if addressed, could further improve the manuscript. These concerns relate to how seizures were defined from the measurement of fluorescent calcium imaging data. Overall, this study is important and convincing, and carries clear value for understanding the multifaceted functions that neuronal galanin can perform under homeostatic and disease conditions.

Additional Concerns:

- The authors have validated their ability to measure behavioral seizures quantitatively in their 2022 Glia paper but the information provided on defining behavioral seizures was limited. The definition of behavioral seizure activity is not expanded upon in this paper, but could provide detail about how the behavioral seizures relate to a seizure detected via calcium imaging.

- Related to the previous point, for the calcium imaging, the difference between an increase in fluorescence that the authors think reflects increased neuronal activity and the fluorescence that corresponds to seizures is not very clear. This detail is necessary because exactly when the term "seizure" describes a degree of increased activity can be difficult to distinguish objectively.

- The supplementary movies that were added were very useful, but raised some questions. For example, what brain regions were pulsating? What areas seemed to constantly exhibit strong fluorescence and was this an artifact? It seemed that sometimes there was background fluorescence in the body. Perhaps an anatomical diagram could be provided for the readers. In addition, there were some movies with much greater fluorescence changes - are these the seizures? These are some reasons for our request for clarified definitions of the term "seizure".

Reviewer #3 (Public review):

Summary:

The neuropeptide galanin is primarily expressed in the hypothalamus and has been shown to play critical roles in homeostatic functions such as arousal, sleep, stress, and brain disorders such as epilepsy. Previous work in rodents using galanin analogs and receptor-specific knockout have provided convincing evidence for anti-convulsant effects of galanin.

In the present study, the authors sought to determine the relationship between galanin expression and whole-brain activity. The authors took advantage of the transparent nature of larval zebrafish to perform whole-brain neural activity measurements via widefield calcium imaging. Two models of seizures were used (eaat2a-/- and pentylenetetrazol; PTZ). In the eaat2a-/- model, spontaneous seizures occur and the authors found that galanin transcript levels were significantly increased and associated with reduced frequency of calcium events. Similarly, two hours after PTZ galanin transcript levels roughly doubled and the frequency and amplitude of calcium events were reduced.

The authors also used a heat shock protein line (hsp70I:gal) where galanin transcripts levels are induced by activation of heat shock protein, but this line also shows higher basal transcript levels of galanin. Due to problems with whole-brain activity in wild-type larvae, the authors used the line without heat shock. They found higher level of galanin in hsp70I:gal larval zebrafish resulted in a reduction of calcium events and a reduction in amplitude of events. In contrast, galanin knockout (gal-/-) increased calcium activity, indicated by an increased number of calcium events, but a reduction in amplitude and duration. New data in the supplementary figure 2 used antibody staining to confirm the absence of galanin expression in gal-/- knockouts. Knockout of the galanin receptor subtype galr1a via crispants also increased the frequency of calcium events. New data in the revised manuscript reports that galr1aKO did not cause an upregulation of galanin, thereby ruling out genetic compensation effects.

In subsequent experiments in eaat2a-/- mutants were crossed with hsp70I:gal or gal-/- to increase or decrease galanin expression, respectively. These experiments showed modest effects, with eaat2a-/- x gal-/- knockouts showing an increased normalized area under the curve and seizure amplitude.

Lastly, the authors attempted to study the relationship between galanin and brain activity during a PTZ challenge. The hsp70I:gal larva showed increased number of seizures and reduced seizure duration during PTZ. In contrast, gal-/- mutants showed increased normalized area under the curve and a stark reduction in number of detected seizures, a reduction in seizure amplitude, but an increase in seizure duration. The authors then ruled out the role of Galr1a in modulating this effect during PTZ, since the number of seizures was unaffected, whereas the amplitude and duration of seizures was increased.

Strengths:

(1) The gain- and loss-of function galanin manipulations provided convincing evidence that galanin influences brain activity (via calcium imaging) during interictal and/or seizure-free periods. In particular, the relationship between galanin transcript levels and brain activity in figures 1 & 2 was convincing. New antibody staining confirms the absence of galanin in gal-/- mutants. New data also shows galanin transcript levels were unchanged in galr1ako brains.

(2) The authors use two models of epilepsy (eaat2a-/- and PTZ).

(3) Focus on the galanin receptor subtype galr1a provided good evidence for an important role of this receptor in controlling brain activity during interictal and/or seizure-free periods.

(4) The authors have added supplementary video files for calcium imaging to support their observations.

Weaknesses:

(1) Although the relationship between galanin and brain activity during interictal or seizure-free periods was clear, the revised manuscript still lacks mechanistic insight in the role of galanin during seizure-like activity induced by PTZ.

(2) The revised manuscript continues to heavily rely on calcium imaging of different mutant lines. Confirmation of knockouts has been provided with immunostaining in a new supplementary figure. Additional methods could strengthen the data, translational relevance, and interpretation (e.g., acute pharmacology using galanin agonists or antagonists, brain or cell recordings, biochemistry, etc).

Reviewer #1 (Public review):

Summary:

In this manuscript, the authors addressed the previous comments from reviewers.

Strengths:

This study identified that NOLC1 could bind to p53 and decrease its nuclear transcriptional activity, then inhibit p53-mediated ferroptosis in gastric cancer.

Weaknesses:

There are a few Western blot images that were processed with excessive contrast adjustment, such as Figure 2I (Caspase-3 in MKN-45 group), Figure 4H (GPX4 in MKN-45 group), and Figure 5G/5I.

Reviewer #2 (Public review):

Summary:

Shengsheng Zhao et al. investigated the role of nucleolar and coiled-body phosphoprotein 1 (NOLC1) in relegating gastric cancer (GC) development and cisplatin-induced drug resistance in GC. They found a significant correlation between high NOLC1 expression and the poor prognosis of GC. Meanwhile, upregulation of NOLC1 was associated with cis-resistant GC. Experimentally, the authors demonstrate that knocking down NOLC1 increased GC sensitivity to Cis possibly by regulating ferroptosis. Mechanistically, they found NOLC1 suppressed ferroptosis by blocking the translocation of P53 from the cytoplasm to the nucleus and promoting its degradation. In addition, the authors also evaluated the effect of combinational treatment of anti-PD-1 and cisplatin in NOLC1 -knockdown tumor cells, revealing a potential role of NOLC1 in the targeted therapy for GC.

Strengths:

Chemoresistance is considered a major reason causing failure of tumor treatment and death of cancer patients. This paper explored the role of NOLC1 in the regulation of Cis-mediated resistance, which involves a regulated cell death named ferroptosis. These findings provide more evidence highlighting the study of regulated cell death to overcome drug resistance in cancer treatment, which could give us more potential strategies or targets for combating cancer.

Weaknesses:

More evidence supporting the regulation of ferroptosis induced by Cisplatin by NOLC1 should be added. Particularly, the role of ferroptosis in the cisplatin-resistance should be verified and whether NOLC1 regulates ferroptosis induced by additional FINs should be explored. Besides, the experiments to verify the regulation of ferroptosis sensitivity by NOLC1 are sort of superficial. The role of MDM2/p53 in ferroptosis or cisplatin resistance mediated by NOLC1 should be further studied by genetic manipulation of p53, which is the key evidence to confirm its contribution to NOLC1 regulation of GC and relative cell death.

Reviewer #1 (Public review):

Summary:

Gene transfer agent (GTA) from Bartonella is a fascinating chimeric GTA that evolved from the domestication of two phages. Not much is known about how the expression of the BaGTA is regulated. In this manuscript, Korotaev et al noted the structural similarity between BrrG (a protein encoded by the ror locus of BaGTA) to a well-known transcriptional anti-termination factor, 21Q, from phage P21. This sparked the investigation into the possibility that BaGTA cluster is also regulated by anti-termination. Using a suite of cell biology, genetics, and genome-wide techniques (ChIP-seq), Korotaev et al convincingly showed that this is most likely the case. The findings offer the first insight into the regulation of GTA cluster (and GTA-mediated gene transfer) particularly in this pathogen Bartonella. Note that anti-termination is a well-known/studied mechanism of transcriptional control. Anti-termination is a very common mechanism for gene expression control of prophages, phages, bacterial gene clusters, and other GTAs, so in this sense, the impact of the findings in this study here is limited to Bartonella.

Strengths:

convincing results that overall support the main claim of the manuscript.

Weaknesses:

A few important controls are missing.

Comments on revisions:

I am happy with this revised version except for one point, that is a single replicate for ChIP-seq, I don't think that is appropriate.

Reviewer #2 (Public review):

Summary:

In this study, the authors identified and characterized a regulatory mechanism based on transcriptional anti-termination that connects the two gene clusters, capsid and run-off replication (ROR) locus, of the bipartite Bartonella gene transfer agent (GTA). Among genes essential for GTA functionality identified in a previous transposon sequencing project, they found a potential antiterminatior of phage origin within the ROR locus. They employed fluorescence reporter and gene transfer assays of overexpression and knockout strains in combination with ChiPSeq and promoter-fusions to convincingly show that this protein indeed acts as an antiterminator counteracting attenuation of the capsid gene cluster expression.

Impact on the field:

The results provide valuable insights into the evolution of the chimeric BaGTA, a unique example of phage co-domestication by bacteria. A similar system found in the other broadly studied Rhodobacterales/Caulobacterales GTA family suggests that antitermination could be a general mechanism for GTA control.

Strengths:

Results of the selected and carefully designed experiments support the main conclusions.

Weaknesses:

The question why overexpression of the antiterminator does not increase the gene tranfer frequency needs to be answered in further studies.

Comments on revisions:

The authors further improved the already strong manuscript. All my concerns have been addressed. The addition of a summry figure helps to understand the proposed mechanism.

Reviewer #1 (Public review):

Koesters and colleagues investigated the role of the small GTPase Rab3A in homeostatic scaling of miniature synaptic transmission in primary mouse cortical cultures using electrophysiology and immunohistochemistry. The major finding is that TTX incubation for 48 hours does not induce an increase in the amplitude of excitatory synaptic miniature events in neuronal cortical cultures derived from Rab3A KO and Rab3A Earlybird mutant mice. NASPM application had comparable effects on mEPSC amplitude in control and after TTX, implying that Ca2+-permeable glutamate receptors are unlikely modulated during synaptic scaling. Immunohistochemical analysis revealed no significant changes in GluA2 puncta size, intensity, and integral after TTX treatment in control and Rab3A KO cultures. Finally, they provide evidence that loss of Rab3A in neurons, but not astrocytes, blocks homeostatic scaling. Based on these data, the authors propose a model in which neuronal Rab3A is required for homeostatic scaling of synaptic transmission, potentially through GluA2-independent mechanisms.

The major finding - impaired homeostatic up-scaling after TTX treatment in Rab3A KO and Rab3 earlybird mutant neurons - is supported by data of high quality. However, the paper falls short of providing any evidence or direction regarding potential mechanisms. The data on GluA2 modulation after TTX incubation are likely statistically underpowered and do not allow drawing solid conclusions, such as GluA2-independent mechanisms of up-scaling.

The study should be of interest to the field because it implicates a presynaptic molecule in homeostatic scaling, which is generally thought to involve postsynaptic neurotransmitter receptor modulation. However, it remains unclear how Rab3A participates in homeostatic plasticity.

Major (remaining) point:

(1) The current version of the abstract only includes the results on GluA2 immunofluorescence and mEPSC amplitude modulation after TTX treatment in control cultures, and a requirement for Rab3A in neurons instead of astrocytes. The major findings, including the block of the mEPSC amplitude increase upon TTX treatment in Rab3KO/EB mutants, are not mentioned. The abstract should be revised so that it reflects all major findings, potentially at the expense of citing previous work by the authors.

Reviewer #2 (Public review):

First, I would like to thank the authors for the response. I acknowledge that the authors show in previous studies that Rab3A acts from the presynaptic side at the NMJ, and that is, as the authors indicate, their impetus for the current study. However, mechanisms observed at a completely different type of synapses cannot be used as an argument for conclusions here. The authors also acknowledge that they should restrict their conclusions to the data in the current study, and they are merely proposing interpretations. Then perhaps they should restrict these interpretations to the discussion rather than make this claim in the abstract (lines 44-47). Here the authors ask whether Rab3A is involved in the homeostatic increase of postsynaptic AMPARs, am I understanding it correctly that their conclusion for this question is "increase in AMPAR levels in WT cultures is more variable than those in mEPSCs so that it is impossible to determine if Rab3A is involved at all"? If so, then this question has not been answered and should not be regarded as one of the main conclusions with the data presented here. It also remains unclear to me how this piece of inconclusive data serves the main objective of the study.

The authors state at the end that the current study is just an extension of their previous work, and therefore their interpretations here further support the idea that Rab3A is acting presynaptically. I would argue that it is the conclusive data, rather than interpretations that lack concrete evidence, that support ideas and models. I think that we would all agree that immunostaining measurements can be very variable. However, if the authors are determined to use this approach to answer one of their major questions, then perhaps one way to significantly strengthen their conclusions is to find ways to somewhat overcome this technical limitation.

Finally, I thank the authors for addressing other minor concerns of mine.

Reviewer #3 (Public review):

This manuscript presents a number of interesting findings that have the potential to increase our understanding of the mechanism underlying homeostatic synaptic plasticity (HSP). The data broadly support that Rab3A plays a role in HSP, although the site and mechanism of action remain uncertain.

The authors clearly demonstrate the Rab3A plays a role in HSP at excitatory synapses, with substantially less plasticity occurring in the Rab3A KO neurons. There is also no apparent HSP in the Earlybird Rab3A mutation, although baseline synaptic strength is already elevated. In this context, it is unclear if the plasticity is absent, already induced by this mutation, or just occluded by a ceiling effect due the synapses already being strengthened. Occlusion may also occur in the mixed cultures, when Rab3A is missing from neurons but not astrocytes. The authors do appropriately discuss these options. The authors have solid data showing that Rab3A is unlikely to be active in astrocytes, Finally, they attempt to study the linkage between changes in synaptic strength and AMPA receptor trafficking during HSP, and conclude that trafficking may not be solely responsible for the changes in synaptic strength during HSP.

Strengths:

This work adds another player into the mechanisms underlying an important form of synaptic plasticity. The plasticity is likely only reduced, suggesting Rab3A is only partially required and perhaps multiple mechanisms contribute. The authors speculate about some possible novel mechanisms, including whether Rab3A is active pre-synaptically to regulate quantal amplitude.

As Rab3A is primarily known as a pre-synaptic molecule, this possibility is intriguing and novel for this system. However, it is based on the partial dissociation of AMPAR trafficking and synaptic response, and lacks strong support. On average, they saw similar magnitude of change in mEPSC amplitude and GluA2 cluster area and integral, but the GluA2 data was not significant due to higher variability. It is difficult to determine if this is due to biology or methodology - the imaging method involves assessing puncta pairs (GluA2/VGlut1) clearly associated with a MAP2 labeled dendrite. This is a small subset of synapses, with usually less than 20 synapses per neuron analyzed, which would be expected to be more variable than mEPSC recordings averaged across several hundred events. However, when they reduce the mEPSC number of events to similar numbers as the imaging, the mESPC amplitudes are still less variable than the imaging data. The reason for this remains unclear. The pool of sampled synapses is still different between the methods and recent data has shown that synapses have variable responses during HSP. Further, there could be variability in the subunit composition of newly inserted AMPARs, and only assessing GluA2 could mask this (see below). It is intriguing that pre-synaptic changes might contribute to HSP, especially given the likely localization of Rab3A. But it remains difficult to distinguish if the apparent difference in imaging and electrophysiology is a methodological issue rather than a biological one. Stronger data, especially positive data on changes in release, will be necessary to conclude that pre-synaptic factors are required for HSP, beyond the established changes in post-synaptic receptor trafficking. Specific deletion of Rab3A from pre-synaptic neurons would also be highly informative.

Other questions arise from the NASPM experiments, used to justify looking at GluA2 (and not GluA1) in the immunostaining. First, there is a strong frequency effect that is unclear in origin. One would expect NASPM to merely block some fraction of the post-synaptic current, and not affect pre-synaptic release or block whole synapses. But the change in frequency seems to argue (as the authors do) that some synapses only have CP-AMPARs, while the rest of the synapses have few or none. Another possibility is that there are pre-synaptic NASPM-sensitive receptors that influence release probability. Further, the amplitude data show a strong trend towards smaller amplitude following NASPM treatment (Fig 3B). The p value for both control and TTX neurons was 0.08 - it is very difficult to argue that there is no effect. And the decrease on average is larger in the TTX neurons, and some cells show a strong effect. It is possible there is some heterogeneity between neurons on whether GluA1/A2 heteromers or GluA1 homomers are added during HSP. This would impact the conclusions about the GluA2 imaging as compared to the mEPSC amplitude data.

To understand the role of Rab3A in HSP will require addressing two main issues:

(1) Is Rab3A acting pre-synaptically, post-synaptically or both? The authors provide good evidence that Rab3A is acting within neurons and not astrocytes. But where it is acting (pre or post) would aid substantially in understanding its role. The general view in the field has been that HSP is regulated post-synaptically via regulation of AMPAR trafficking, and considerable evidence supports this view. More concrete support for the authors suggestion of a pre-synaptic site of control would be helpful.

(2) Rab3A is also found at inhibitory synapses. It would be very informative to know if HSP at inhibitory synapses is similarly affected. This is particularly relevant as at inhibitory synapses, one expects a removal of GABARs or a decrease in GABA release (ie the opposite of whatever is happening at excitatory synapses). If both processes are regulated by Rab3A, this might suggest a role for this protein more upstream in the signaling; an effect only at excitatory synapses would argue for a more specific role just at those synapses.

Comments on revisions:

The section on TNF is a bit odd. The data on the astrocyte deletion of Rab3A only argues that Rab3A is unlikely to regulate TNF release. But it could easily be downstream of the neuronal TNF receptor. Without any data addressing the TNF response, it seems quite premature to argue that Rab3A is part of a TNF-independent pathway.

The section title (line 506-7) declaring Rab3A as the first presynaptic protein involved in HSP is also premature, as they don't know it is acting pre-synaptically.

Reviewer #1 (Public review):

The authors of this study use electron microscopy and 3D reconstruction techniques to study the morphology of distinct classes of Drosophila sensory neurons *across many neurons of the same class.* This is a comprehensive study attempting to look at nearly all the sensory neurons across multiple sensilla to determine a) how much morphological variability exists between and within neurons of different and similar sensory classes, and 2) identify dendritic features that may have evolved to support particular sensory functions. This study builds upon the authors' previous work, which allowed them to identify and distinguish sensory neuron subtypes in the EM volumes without additional staining so that reconstructed neurons could reliably be placed in the appropriate class. This work is unique in looking at a large number of individual neurons of the same class to determine what is consistent and what is variable about their class-specific morphologies.

This means that in addition to providing specific structural information about these particular cells, the authors explore broader questions of how much morphological diversity exists between sensory neurons of the same class and how different dendritic morphologies might affect sensory and physiological properties of neurons.

The authors found that CO2-sensing neurons have an unusual, sheet-like morphology in contrast to the thin branches of odor-sensing neurons. They show that this morphology greatly increases the surface area to volume ratio above what could be achieved by modest branching of thin dendrites, and posit that this might be important for their sensory function, though this was not directly tested in their study. The study is mainly descriptive in nature, but thorough, and provides a nice jumping-off point for future functional studies. One interesting future analysis could be to examine all four cell types within a single sensilla together to see if there are any general correlations that could reveal insights about how morphology is determined and the relative contributions of intrinsic mechanisms vs interactions with neighboring cells. For example, if higher than average branching in one cell type correlated with higher than average branching in another type, if in the same sensilla. This might suggest higher extracellular growth or branching cues within a sensilla. Conversely, if higher branching in one cell type consistently leads to reduced length or branching in another, this might point to dendrite-dendrite interactions between cells undergoing competitive or repulsive interactions to define territories within each sensilla as a major determinant of the variability.

Reviewer #2 (Public review):

Summary:

The manuscript employs serial block‐face electron microscopy (SBEM) and cryofixation to obtain high‐resolution, three‐dimensional reconstructions of Drosophila antennal sensilla containing olfactory receptor neurons (ORNs) that detect CO2. This method has been used previously by the same lab in Gonzales et. al, 2021. (https://elifesciences.org/articles/69896), which had provided an exemplary model by integrating high-resolution EM with electrophysiology and cell-type-specific labeling. The previous study ended up correlating morphology with activity for multiple olfactory sensillar types. Compared to the 2021 study, this current manuscript appears somewhat incomplete and lacks integration with activity.

In fact older studies have also reported two-dimensional TEM images of the putative CO2 neuron in Drosophila (Shanbhag et al., 1999) and in mosquitoes (McIver and Siemicki, 1975; Lu et al, 2007), and in these instances reported that the dendritic architecture of the CO2 neuron was somewhat different (circular and flattened, lamellated) from other olfactory neurons.

The authors claim that this approach offers an artifact‐minimized ultrastructural dataset compared to earlier. In this study, not only do they confirm this different morphology but also classify it into distinct subtypes (loosely curled, fully curled, split, and mixed). This detailed morphological categorization was not provided in prior studies (e.g., Shanbhag et al., 1999 ). The authors would benefit from providing quantitative thresholds or objective metrics to improve reproducibility and to clarify whether these structural distinctions correlate with distinct functional roles.

Strengths:

The study makes a convincing case that ab1C neurons exhibit a unique, flattened dendritic morphology unlike the cylindrical dendrites found in ab1D neurons. This observation extends previous qualitative TEM findings by not only confirming the presence of flattened lamellae in CO₂ neurons but also quantifying key morphometrics such as dendritic length, surface area, and volume, and calculating surface area-to-volume ratios. The enhanced ratios observed in the flattened segments are speculated to be linked to potential advantages in receptor distribution (e.g., Gr21a/Gr63a) and efficient signal propagation.

Weaknesses:

While the manuscript offers valuable ultrastructural insights and reveals previously unappreciated heterogeneity among CO₂-sensing neurons, several issues warrant further investigation in addition to the points made above.

(1) Although this quantitative approach is robust compared to earlier descriptive reports, its impact is somewhat limited by the absence of direct electrophysiological data to confirm that ultrastructural differences translate into altered neuronal function. A direct comparison or discussion of how the present findings align with the functional data obtained from electrophysiology would strengthen the overall argument.

(2) Clarifying the criteria for dendritic subtype classification with quantitative parameters would enhance reproducibility and interpretability. Moreover, incorporating electrophysiological recordings from ab1C neurons would provide compelling evidence linking structure and function, and mapping key receptor proteins through immunolabeling could directly correlate receptor distribution with the observed morphological diversity.

(3) Even though Cryofixation is claimed to be superior to chemical fixation for generating fewer artifacts, authors need to confirm independently the variation observed in the CO2 neuron morphologies across populations. All types of fixation in TEMs cause some artifacts, as does serial sectioning. Without understanding the error rates or without independent validation with another method, it is hard to have confidence in the conclusions drawn by the authors of the paper.

Addressing these concerns and integrating additional experiments would significantly bolster the manuscript's completeness and advancement.

Reviewer #3 (Public review):

Summary:

In the current manuscript entitled "Population-level morphological analysis of paired CO2- and odor-sensing olfactory neurons in D. melanogaster via volume electron microscopy", Choy, Charara et al. use volume electron microscopy and neuron reconstruction to compare the dendritic morphology of ab1C and ab1D neurons of the Drosophila basiconic ab1 sensillum. They aim to investigate the degree of dendritic heterogeneity within a functional class of neurons using ab1C and ab1D, which they can identify due to the unique feature of ab1 sensilla to house four neurons and the stereotypic location on the third antennal segment. This is a great use of volumetric electron imaging and neuron reconstruction to sample a population of neurons of the same type. Their data convincingly shows that there is dendritic heterogeneity in both investigated populations, and their sample size is sufficient to strongly support this observation. This data proposes that the phenomenon of dendritic heterogenity is common in the Drosophila olfactory system and will stimulate future investigations into the developmental origin, functional implications, and potential adaptive advantage of this feature.

Moreover, the authors discovered that there is a difference between CO2- and odour-sensing neurons of which the first show a characteristic flattened and sheet-like structure not observed in other sensory neurons sampled in this and previous studies. They hypothesize that this unique dendritic organization, which increases the surface area to volume ratio, might allow more efficient Co2 sensing by housing higher numbers of Co2 receptors. This is supported by previous attempts to express Co2 sensors in olfactory sensory neurons, which lack this dendritic morphology, resulting in lower Co2 sensitivity compared to endogenous neurons.

Overall, this detailed morphological description of olfactory sensory neurons' dendrites convincingly shows heterogeneity in two neuron classes with potential functional impacts for odour sensing.

Strength:

The volumetric EM imaging and reconstruction approach offers unprecedented details in single cell morphology and compares dendrite heterogeneity across a great fraction of ab1 sensilla.<br /> The authors identify specific shapes for ab1C sensilla potentially linked to their unique function in CO2 sensing.

Weaknesses:

While the morphological description is highly detailed, no attempts are made to link this to odour sensitivity or other properties of the neurons. It would have been exciting to see how altered morphology impacts physiology in these olfactory sensory cells.

Reviewer #1 (Public review):

In this study, Marocco and colleagues perform a deep characterization of the complex molecular mechanism guiding the recognition of a particular CELLmotif previously identified in hepatocytes in another publication. Having miR-155-3p with or without this CELLmotif as initial focus, the authors identify 21 proteins differentially binding to these two miRNA versions. From these, they decided to focus on PCBP2. They elegantly demonstrate PCBP2 binding to miR-155-3p WT version but not to the CELLmotif-mutated version. miR-155-3p contains a hEXOmotif identified in a different report, whose recognition is largely mediated by another RNA-binding protein called SYNCRIP. Interestingly, mutation of the hEXOmotif contained in miR-155-3p did not only blunt SYNCRIP binding, but also PCBP2 binding despite the maintenance of the CELLmotif. This indicates that somehow SYNCRIP binding is a prerequisite for PCBP2 binding. EMSA assay confirms that SYNCRIP is necessary for PCBP2 binding to miR-155-3p, while PCBP2 is not needed for SYNCRIP binding. The authors aim to extend these findings to other miRNAs containing both motifs. For that, they perform a small-RNA-Seq of EVs released from cells knockdown for PCBP2 versus control cells, identifying a subset of miRNAs whose expression either increases or decreases. The assumption is that those miRNAs containing PCBP2-binding CELLmotif should now be less retained in the cell and go more to extracellular vesicles, thus reflecting a higher EV expression. The specific subset of miRNAs having both the CELLmotif and hEXOmotif (9 miRNAs) whose expressions increase in EVs due to PCBP2 reduction is also affected by knocking down SYNCRIP in the sense that reduction of SYNCRIP leads to lower EV sorting. Further experiments confirm that PCBP2 and SYNCRIP bind to these 9 miRNAs and that knocking down SYNCRIP impairs their EV sorting.

Reviewer #2 (Public review):

Summary:

The author of this manuscript aimed to uncover the mechanisms behind miRNA retention within cells. They identified PCBP2 as a crucial factor in this process, revealing a novel role for RNA-binding proteins. Additionally, the study discovered that SYNCRIP is essential for PCBP2's function, demonstrating the cooperative interaction between these two proteins. This research not only sheds light on the intricate dynamics of miRNA retention but also emphasizes the importance of protein interactions in regulating miRNA behavior within cells.

Strengths:

This paper makes important progress in understanding how miRNAs are kept inside cells. It identifies PCBP2 as a key player in this process, showing a new role for proteins that bind RNA. The study also finds that SYNCRIP is needed for PCBP2 to work, highlighting how these proteins work together. These discoveries not only improve our knowledge of miRNA behavior but also suggest new ways to develop treatments by controlling miRNA locations to influence cell communication in diseases. The use of liver cell models and thorough experiments ensures the results are reliable and show their potential for RNA-based therapies.

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 overexpression 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 a sufficient sample size and appropriate statistics.<br /> (2) Good mix of genetics and biochemistry.<br /> (3) Generation of new transgenes and Drosophila alleles that will be beneficial for the community.

Weaknesses:

(1) Phenotypes are based on artificial overexpression. It is not clear whether these results are relevant to normal physiology.

(2) The phenotype of "degenerating ovaries" is very broad, and the study is not focused on phenotypes at the cellular level. Furthermore, no information is provided in the Materials and Methods on how degenerating ovaries are scored, despite this being the most important assay in the study.

(3) In Figure 5, the authors want to conclude that uev1a is a tumor-suppressor, and so they over-express ubev1/2 in human cancer cell lines that have RasK12 and find reduced proliferation, colony formation, and xenograft size. However, genes that act as tumor suppressors have loss-of-function phenotypes that allow for increased cell division. The Drosophila uev1a mutant is viable and fertile, suggesting that it is not a tumor suppressor in flies. Additionally, they do not deplete human ubev1/2 from human cancer cell lines and assess whether this increases cell division, colony formation, and xenograph growth.

(4) A critical part of the model does not make sense. CycA is a key part of their model, but they do not show CycA protein expression in WT egg chambers or in their over-expression models (nos.RasV12 or bam>RasV12). Based on Lilly and Spradling 1996, Cyclin A is not expressed in germ cells in region 2-3 of the germarium; whether CycA is expressed in nurse cells in later egg chambers is not shown but is critical to document comprehensively.

(5) The authors should provide more information about the knowledge base of uev1a and its homologs in the introduction.

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 homologs, UBE2V1 and UBE2V2, suppresses tumor growth in human colorectal cancer xenografts and cell lines. Notably, the expression of these genes correlates with the survival of colorectal cancer patients carrying the 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.

Weakness:

The quantification of some crucial experiments lacks sufficient clarity.

Reviewer #1 (Public review):

Summary:

The authors confirmed earlier findings that AVP influences α and β cells differently, depending on glucose concentrations. At substimulatory glucose levels, AVP combined with forskolin - an activator of cAMP -did not significantly stimulate β cells, although it did activate α cells. Once glucose was raised to stimulatory levels, β cells became active, and α cell activity declined, indicating glucose's suppressive effect on α cells and permissive effect on β cells. Under physiological glucose levels (8-9 mM), forskolin enhanced β-cell calcium oscillations, and AVP further modulated this activity. However, AVP's effect on β cells was variable across islets and did not significantly alter AUC measurements (a combined indicator of oscillation frequency and duration). In α cells, forskolin and AVP led to increased activity even at high glucose levels, suggesting that α cells remain responsive despite expected suppression by insulin and glucose.

Experiments with physiological concentrations of epinephrine suggest that AVP does not operate via Gs-coupled V2 receptors in β cells, as AVP could not counteract epinephrine's inhibitory effects. Instead, epinephrine reduced β cell activity while increasing α cell activity through different G-protein-coupled mechanisms. These results emphasize that AVP can potentiate α-cell activation and has a nuanced, context-dependent effect on β cells.

The most robust activation of both α and β cells by AVP occurred within its physiological osmo-regulatory range (~10-100 pM), confirming that AVP exerts bell-shaped concentration-dependent effects on β cells. At low concentrations, AVP increased β cell calcium oscillation frequency and reduced "halfwidths"; high concentrations eventually suppressed β cell activity, mimicking the muscarinic signaling. In α cells, higher AVP concentrations were required for peak activation, which was not blunted by receptor inactivation within physiological ranges.

Attempting to further dissect the role of specific AVP receptors, the authors designed and tested peptide ligands selective for V1b receptors. These included a selective V1b agonist; a V1b agonist with antagonist properties at V1a and oxytocin receptors; and a selective V1a antagonist. In pancreatic slices, these peptides seem to replicate AVP's effects on Ca²⁺ signaling, although responses were highly variable, with some islets showing increased activity and others no change or suppression. The variability was partly attributed to islet-specific baseline activity, and the authors conclude that AVP and V1b receptor agonists can modulate β cell activity in a state-dependent manner, stimulating insulin secretion in quiescent cells and inhibiting it in already active cells.

Strengths:

Overall, the study is technically advanced and provides useful pharmacological tools. However, the conclusions are limited by a lack of direct mechanistic and functional data. Addressing these gaps through a combination of signaling pathway interrogation, functional hormone output, genetic validation, and receptor localization would strengthen the conclusions and reduce the current (interpretive) ambiguity.

Weaknesses:

(1) The study is entirely based on pharmacological tools. Without genetic models, off-target effects or incomplete specificity of the peptides cannot be fully ruled out.

(2) Despite multiple claims about β cell activation or inhibition, the functional output - insulin secretion - is weakly assessed, and only in limited conditions. This aspect makes it very hard to correlate calcium dynamics with physiological outcomes.

(3) Insulin and glucagon secretion assays should be provided; the authors should measure hormone release in parallel with Ca2+ imaging, using perifusion assays, especially during AVP ramp and peptide ligand applications.

Additionally, there is no standardization of the metabolic state of islets. The authors should consider measuring islet NAD(P)H autofluorescence or mitochondrial potential (e.g., using TMRE) to control for metabolic variability that may affect responsiveness.

(4) There is a high degree of variability in response to AVP and V1b agonists across islets (activation, no effect, inhibition). Surprisingly, the authors do not fully explore the cause of this heterogeneity (whether it is due to receptor expression differences, metabolic state, experimental variability, or other conditions).

(5) There is no validation of V1b receptor expression at the protein or mRNA level in α or β cells using in situ hybridization, immunohistochemistry, or spatial transcriptomics.

(6) AVP effects are described in terms of permissive or antagonistic effects on cAMP (especially in relation to epinephrine), but direct measurements of cAMP in α and β cells are not shown, weakening these conclusions. The authors should use Epac-based cAMP FRET sensors in α and β cells to monitor the interaction between AVP, forskolin, and epinephrine more conclusively.

(7) Single-islet transcriptomics or proteomics (also to clarify variability) should be provided to analyze receptor expression variability across islets to correlate with response phenotypes (activation vs inhibition). Alternatively, the authors could perform calcium imaging with simultaneous insulin granule tracking or ATP levels to assess islet functional states.

(8) While the study implies AVP acts through V1b receptors on β cells, the signaling downstream (e.g., PLC activation, IP3R isoforms involved) is simply inferred but not directly shown.

(9) The interpretation that IP3R inactivation (mentioned in the title!) underlies the bell-shaped AVP effect is just hypothetical, without direct measurements. Assays in β (and/or α)-cell-specific V1b KO mice and IP3R KO mice must be provided to support these speculations.

Reviewer #2 (Public review):

Summary:

In this paper, Drs. Kercmar, Murko, and Bombek make a series of observations related to the role of AVP in pancreatic islets. They use the pancreatic slice preparation that their group is well known for. The observations on the slide physiology are technically impressive. However, I am not convinced by the conclusions of this manuscript for a number of reasons. At the core of my concern is perhaps that this manuscript appears to be motivated to resolve 'controversies' surrounding the actions of AVP on insulin and glucagon secretion. This manuscript adds more observations, but these do not move the field forward in improving or solidifying our mechanistic understanding of AVP actions on islets. A major claim in this manuscript is the beta cell expression of the V1b Receptor for AVP, but the evidence presented in this paper falls short of supporting this claim. Observations on the activation of calcium in alpha cells via V1b receptor align with prior observations of this effect.

I have focused my main concerns below. I hope the authors will consider these suggestions carefully - please be assured that they were made with the intent to support the authors and increase the impact of this work.

Strengths:

The main strength of this paper is the technical sophistication of the approach and the analysis and representation of the calcium traces from alpha and beta cells.

Weaknesses:

(1) The introduction is long and summarizes a substantive body of literature on AVP actions on insulin secretion in vivo. There are a number of possible explanations for these observations that do not directly target islet cells. If the goal is to resolve the mechanistic basis of AVP action on alpha and beta cells, the more limited number of papers that describe direct islet effects is more helpful. There are excellent data that indicate that the actions of AVP are mediated via V1bR on alpha cells and that V1bR is a) not expressed by beta cells and b) does not activate beta cell calcium at all at 10 nM - which is the same concentration used in this paper (Figure 4G) for peak alpha cell Ca2+ activation (see https://doi.org/10.1016/j.cmet.2017.03.017; cited as ref 30 in the current manuscript).

(2) We know from bulk RNAseq data on purified alpha, beta, and delta cells from both the Huising and Gribble groups that there is no expression of V2a. I will point you to the data from the Huising lab website published almost a decade ago (http://dx.doi.org/10.1016/j.molmet.2016.04.007) - which is publicly available and can be used to generate figures (https://huisinglab.com/data-ghrelin-ucsc/index.html). They indicate the absence of expression of not only AVP2 receptors anywhere in the islet, but also the lack of expression of V1bra, V1brb, and Oxtr in beta cells. Instead of the detailed list of expression of these 4 receptors elsewhere in the body, it would be more directly relevant to set up their pancreatic slice experiments to summarize the known expression in pancreatic islets that is publicly available. It would also have helped ground the efforts that involved the generation of the V1aR agonist and V2R antagonist, which confirm these known AVP/OXT receptor expression patterns.

(3) Importantly, the lack of V1br from beta cells does not invalidate observations that AVP affects calcium in beta cells, but it does indicate that these effects are mediated a) indirectly, downstream of alpha cell V1br or b) via an unknown off-target mechanism (less likely). The different peak efficacies in Figure 4G would also suggest that they are not mediated by the same receptor.

(4) The rationale for the use of forskolin across almost all traces is unclear. It is motivated by a desire to 'study the AVP dependence of both alpha and beta cells at the same time'. As best as I can determine, the design choice to conduct all studies under sustained forskolin stimulation is related to the permissive actions of AVP on hormone secretion in response to cAMP-generating stimuli. The permissive actions by AVP that are cited are on hormone secretion, which in many cell types requires activation of both calcium and cAMP signaling. Whether the activation of V1br and subsequent calcium response is permitted by cAMP is unclear. I believe the argument the authors are making here is that the activation of beta cell calcium by AVP is permitted by forskolin. i.e., the cAMP stimulated by it in beta cells. However, the design does not account for the elevation of cAMP in alpha cells and subsequent release of glucagon, particularly upon co-stimulation with AVP, which permits glucagon release by activating a calcium response in alpha cells. This glucagon could then activate beta cells. If resolving the mechanism of action is the goal, often less is more. The activation of Gaq-mediated calcium is not cAMP dependent (although the downstream hormone secretion clearly often is). As was shown, AVP does not activate calcium in beta cells in the absence of cAMP. The experiments in Figures 1, 2, and 4 should have been completed in the absence of cAMP first.

(5) It is unexpected that epinephrine in Figure 2 does not activate the alpha cell calcium? A recent paper from the same group (Sluga et al) shows robust calcium activation in alpha cells in a similar prep by 1 nM epinephrine, which is similar to the dose used here.

(6) Figure 8 suggests a pharmacological activation of beta cell V1bR in the low pM range. How do the authors reconcile this comparison with the apparent absence of an effect of AVP stimulation at low pM to low nM doses in beta cells (Figure 4A)? I note that there are changes over time with sustained beta cell stimulation with 8 mM glucose, but these changes are relatively subtle, gradual, and quite likely represent the progression of calcium behaviors that would have occurred under sustained glucose, irrespective of these very low AVP concentrations. I will note that the Kd of the V1bR for AVP is around 1 nM, with tracer displacement starting around 100 pM according to the data in figure 5B, which is hard to reconcile with changes in beta cell calcium by AVP doses that start 10-100-fold lower than this dose at 1 and 10 pM (Figure 8).

Reviewer #3 (Public review):

Summary:

This work aims to better understand the role of arginine vasopressin (AVP) in the control of islet hormone secretion. This builds on previous literature in this area reporting on the actions of AVP to stimulate islet hormones. The gap in literature being addressed by these studies is primarily focused on the glucose-dependency of AVP on both insulin and glucagon secretion. A secondary objective is to explore the role of individual receptors with the use of newly generated peptides and existing tools. The methods include the use of Ca2+ imaging in pancreas slices from mice, with additional outcomes including insulin secretion in some areas. The conclusions presented are that AVP acts through V1b receptors in both alpha- and beta-cells, that this activity occurs in the high cAMP environment, and is glucose dependent.

Strengths:

The area of research is emerging with plenty of room for new contributions. The concept of AVP stimulating islet hormone secretion is important and deserving of further insight. The use of pancreas tissue to image primary cells makes the experiments physiologically relevant. The advancement of novel tools in this area should be helpful to other groups investigating the actions of AVP.

Weaknesses:

The conclusions are only modestly supported by the data and lack experimental depth and rigor. The rationale for only conducting studies at high cAMP conditions is not entirely clear and limits the conclusions that can be made. The use of Ca2+ is helpful, but it is a surrogate for hormone secretion. Additional measurements of hormone secretion are needed to enhance the robustness of these conclusions. Consideration of paracrine effects between alpha- and beta-cells is only superficially made and is likely essential in the context of the experimental design. For instance, there is clear literature that alpha-cells secrete several factors that work in paracrine interactions on beta-cells and autocrine actions back on alpha-cells. Conducting these studies in a high cAMP context only completely overlooks these interactions, skewing the interpretations made by the investigators. Finally, the clarity of the experiments and results could be significantly enhanced.

Reviewer #1 (Public review):

Summary

In this manuscript, the authors introduce Gcoupler, a Python-based computational pipeline designed to identify endogenous intracellular metabolites that function as allosteric modulators at the G protein-coupled receptor (GPCR) - Gα protein interface. Gcoupler is comprised of four modules:

I. Synthesizer - identifies protein cavities and generates synthetic ligands using LigBuilder3

II. Authenticator - classifies ligands into high-affinity binders (HABs) and low-affinity binders (LABs) based on AutoDock Vina binding energies

III. Generator - trains graph neural network (GNN) models (GCM, GCN, AFP, GAT) to predict binding affinity using synthetic ligands

IV. BioRanker - prioritizes ligands based on statistical and bioactivity data

The authors apply Gcoupler to study the Ste2p-Gpa1p interface in yeast, identifying sterols such as zymosterol (ZST) and lanosterol (LST) as modulators of GPCR signaling. Our review will focus on the computational aspects of the work. Overall, we found the Gcoupler approach interesting and potentially valuable, but we have several concerns with the methods and validation that need to be addressed prior to publication/dissemination.

(1) The exact algorithmic advancement of the Synthesizer beyond being some type of application wrapper around LigBuilder is unclear. Is the grow-link approach mentioned in the methods already a component of LigBuilder, or is it custom? If it is custom, what does it do? Is the API for custom optimization routines new with the Synthesizer, or is this a component of LigBuilder? Is the genetic algorithm novel or already an existing software implementation? Is the cavity detection tool a component of LigBuilder or novel in some way? Is the fragment library utilized in the Synthesizer the default fragment library in LigBuilder, or has it been customized? Are there rules that dictate how molecule growth can occur? The scientific contribution of the Synthesizer is unclear. If there has not been any new methodological development, then it may be more appropriate to just refer to this part of the algorithm as an application layer for LigBuilder.

(2) The use of AutoDock Vina binding energy scores to classify ligands into HABs and LABs is problematic. AutoDock Vina's energy function is primarily tuned for pose prediction and displays highly system-dependent affinity ranking capabilities. Moreover, the HAB/LAB thresholds of -7 kcal/mol or -8 kcal/mol lack justification. Were these arbitrarily selected cutoffs, or was benchmarking performed to identify appropriate cutoffs? It seems like these thresholds should be determined by calibrating the docking scores with experimental binding data (e.g., known binders with measured affinities) or through re-scoring molecules with a rigorous alchemical free energy approach.

(3) Neither the Results nor Methods sections provide information on how the GNNs were trained in this study. Details such as node features, edge attributes, standardization, pooling, activation functions, layers, dropout, etc., should all be described in detail. The training protocol should also be described, including loss functions, independent monitoring and early stopping criteria, learning rate adjustments, etc.

(4) GNN model training seems to occur on at most 500 molecules per training run? This is unclear from the manuscript. That is a very small number of training samples if true. Please clarify. How was upsampling performed? What were the HAB/LAB class distributions? In addition, it seems as though only synthetically generated molecules are used for training, and the task is to discriminate synthetic molecules based on their docking scores. Synthetic ligands generated by LigBuilder may occupy distinct chemical space, making classification trivial, particularly in the setting of a random split k-folds validation approach. In the absence of a leave-class-out validation, it is unclear if the model learns generalizable features or exploits clear chemical differences. Historically, it was inappropriate to evaluate ligand-based QSAR models on synthetic decoys such as the DUD-E sets - synthetic ligands can be much more easily distinguished by heavily parameterized ligand-based machine learning models than by physically constrained single-point docking score functions.

(5) Training QSAR models on docking scores to accelerate virtual screening is not in itself novel (see here for a nice recent example: https://www.nature.com/articles/s43588-025-00777-x), but can be highly useful to focus structure-based analysis on the most promising areas of ligand chemical space; however, we are perplexed by the motivation here. If only a few hundred or a few thousand molecules are being sampled, why not just use AutoDock Vina? The models are trained to try to discriminate molecules by AutoDock Vina score rather than experimental affinity, so it seems like we would ideally just run Vina? Perhaps we are misunderstanding the scale of the screening that was done here. Please clarify the manuscript methods to help justify the approach.

(6) The brevity of the MD simulations raises some concerns that the results may be over-interpreted. RMSD plots do not reliably compare the affinity behavior in this context because of the short timescales coupled with the dramatic topological differences between the ligands being compared; CoQ6 is long and highly flexible compared to ZST and LST. Convergence metrics, such as block averaging and time-dependent MM/GBSA energies, should be included over much longer timescales. For CoQ6, the authors may need to run multiple simulations of several microseconds, identify the longest-lived metastable states of CoQ6, and perform MM/GBSA energies for each state weighted by each state's probability.

Reviewer #2 (Public review):

Summary:

Mohanty et al. present a new deep learning method to identify intracellular allosteric modulators of GPCRs. This is an interesting field for e.g. the design of novel small molecule inhibitors of GPCR signalling. A key limitation, as mentioned by the authors, is the limited availability of data. The method presented, Gcoupler, aims to overcome these limitations, as shown by experimental validation of sterols in the inhibition of Ste2p, which has been shown to be relevant molecules in human and rat cardiac hypertrophy models.<br /> They have made their code available for download and installation, which can easily be followed to set up software on a local machine.

Strengths:

- Clear GitHub repository

- Extensive data on yeast systems

Weaknesses:

- No assay to directly determine the affinity of the compounds to the protein of interest.

In conclusion, the authors present an interesting new method to identify allosteric inhibitors of GPCRs, which can easily be employed by research labs. Whilst their efforts to characterize the compounds in yeast cells, in order to confirm their findings, it would be beneficial if the authors show their compounds are active in a simple binding assay.

Reviewer #3 (Public review):

Summary:

In this paper, the authors introduce the Gcoupler software, an open-source deep learning-based platform for structure-guided discovery of ligands targeting GPCR interfaces.<br /> Overall, this manuscript represents a field-advancing contribution at the intersection of AI-based ligand discovery and GPCR signaling regulation.

Strengths:

The paper presents a comprehensive and well-structured workflow combining cavity identification, de novo ligand generation, statistical validation, and graph neural network-based classification. Notably, the authors use Gcoupler to identify endogenous intracellular sterols as allosteric modulators of the GPCR-Gα interface in yeast, with experimental validations extending to mammalian systems. The ability to systematically explore intracellular metabolite modulation of GPCR signaling represents a novel and impactful contribution. This study significantly advances the field of GPCR biology and computational ligand discovery.

Reviewer #1 (Public review):

Summary:

In this study, Tittelmeier et al. explored the role of sphingolipid metabolism in maintaining endolysosomal membrane integrity and its downstream effects on tau aggregation and toxicity, using both worms and human cell models. The authors showed that knockdown of sphingolipid metabolism genes reduced endolysosomal membrane fluidity, as revealed by FRAP and C-Laurdan imaging, leading to increased vesicle rupture. Furthermore, tau aggregates accumulated in endolysosomes and exacerbated membrane rigidity and damage, promoting seeded tau aggregation, likely by enabling tau seed escape into the cytosol. Importantly, unsaturated fatty acid supplementation restored membrane fluidity, suppressed tau propagation, and alleviated neurotoxicity in C. elegans. These findings provide insight into how lipid dysregulation contributes to tau pathology and highlight membrane fluidity restoration as a potential therapeutic avenue for Alzheimer's disease.

Strengths:

The study addresses the connection between sphingolipid metabolism, endolysosomal membrane integrity, and tau pathology, which is a relevant topic in the context of Alzheimer's disease and related tauopathies.

The use of both C. elegans and human cell models provides cross-species perspectives that help frame the findings in a broader biological context.

The combination of FRAP and C-Laurdan dye imaging offers a biophysical approach to investigate changes in membrane properties, which is a technically interesting aspect of the study.

The observation that unsaturated fatty acid supplementation can modulate membrane fluidity and influence tau-related phenotypes adds an element of potential therapeutic interest.

The study presents multiple experimental approaches to address the proposed mechanism, and efforts were made to examine both membrane behavior and tau aggregation dynamics.

Weaknesses:

In Figure 3, the authors used C-Laurdan imaging to assess membrane fluidity and showed that knockdown of SPHK2, the human ortholog of sphk-1, led to increased membrane rigidity. However, the authors did not co-stain with a lysosomal marker, making it unclear whether the observed effect is specific to lysosomal membranes or reflects general membrane changes. Co-staining with LysoTracker or applying segmentation masks to isolate lysosomal signals would significantly improve interpretation.

Line 173 states that Lipofectamine 2000 increases membrane fluidity based on GP index changes, but this is incorrect. A higher GP index indicates increased membrane order (i.e., reduced fluidity), so the statement should be revised. Additionally, Lipofectamine 2000 can itself alter membrane rigidity, posing a risk of false-positive interpretations. To confirm the role of SPHK2 in this phenotype, the authors should use a CRISPR/Cas9 knockout model instead of relying solely on siRNA transfection, which may be confounded by the delivery reagent. Without lysosomal co-staining and SPHK2 KO validation, the authors cannot conclusively claim that SPHK2 loss affects endolysosomal membrane integrity.

The section titled "Fibrillar tau increases membrane rigidity and exacerbates endolysosomal damage" (lines 177-215) requires substantial revision. The narrative jumps abruptly between worms and cell models, making it hard to follow the logic. The use of the F3ΔK281::mCherry strain is introduced without explanation or context. It is unclear whether this strain is relevant to lysosomal membrane rupture, as no reference or justification is provided. The authors should clarify whether this reporter is intended to detect lysosomal membrane permeabilization (LMP). If so, it would be more appropriate to use established LMP reporters, such as lysosome-targeted fluorescent sensors, galectin-based reporters, or dextran leakage assays. Based on the current data in Figure 3G, it is difficult to draw firm conclusions regarding membrane rupture levels.

To support the conclusion that sphingolipid metabolism gene knockdown alters membrane properties, the study would benefit from direct lipidomic analysis. Measuring changes in sphingolipid profiles in both C. elegans and cell models would provide biochemical evidence for the proposed disruption of lipid homeostasis. Given the availability of lipidomics platforms, this type of analysis should be feasible in both worms and human cells and would significantly strengthen the mechanistic claims regarding membrane fluidity and integrity.

The conclusions of the study rely heavily on imaging-based assays, including FRAP, C-Laurdan, and fluorescence microscopy. While these approaches provide valuable spatial and qualitative insights, they are inherently indirect and subject to interpretive limitations. To strengthen the mechanistic claims, the authors should incorporate additional biochemical or quantitative approaches. For example, lipidomics would allow direct measurement of membrane lipid composition changes, and western blotting or quantitative proteomics could assess levels of membrane-associated proteins involved in endolysosomal function or stress responses. Including such data would significantly improve the robustness and reproducibility of the study's conclusions.

The human cell experiments were performed exclusively in HEK293T cells, which are not physiologically relevant for modeling Alzheimer's disease or lysosomal function in neurons. Given that the study aims to draw conclusions related to tau aggregation and lysosomal membrane integrity, the use of a more disease-relevant cellular model is essential. There are several established AD-relevant cell models, including iPSC-derived neurons, neuroblastoma lines expressing tau, or microglial models, which would better reflect the cellular context of tauopathies. Validation of key findings in at least one of these systems would substantially enhance the biological relevance and translational impact of the study.

The authors reported that PUFA supplementation rescues neurotoxic phenotypes by increasing membrane fluidity. However, the data supporting this claim rely entirely on confocal imaging, shown in both the main and supplemental figures. To substantiate the mechanistic link between PUFA treatment and improved lysosomal membrane properties, the authors should include functional assays demonstrating that PUFAs are indeed incorporated into lysosomal membranes. Additionally, lipidomics analysis would be valuable to identify which lipid species are altered upon supplementation and correlate these changes with the observed phenotypic rescue. Furthermore, the conclusion that PUFAs rescue "neurotoxic phenotypes" is not appropriate based on data derived solely from HEK293T cells, which are not neuronal. To make claims about tau-related neurotoxicity, the authors should validate their findings in a more relevant neuronal model, such as SH-SY5Y neuroblastoma cells expressing tau or iPSC-derived neurons. This would better reflect the cellular environment of Alzheimer's disease and provide stronger support for the proposed therapeutic potential of PUFA supplementation.

While the authors demonstrate that ALA supplementation mitigates neurotoxicity in C. elegans expressing aggregated tau (F3ΔK281::mCherry), the current data are not sufficient to conclude that ALA directly rescues tau aggregation toxicity via a lysosome-specific mechanism. It remains unclear how lipid composition is altered upon ALA treatment and whether these changes correlate with functional improvement of lysosomal pathways. The manuscript does not provide mechanistic insight into how ALA enhances lysosomal health or attenuates endolysosomal damage. Moreover, supplementation with PUFAs like ALA can activate a wide range of cellular processes beyond lysosomal function, including alterations in membrane fluidity, signaling cascades, and oxidative stress responses. The authors should clarify how they distinguish the lysosome-related effects from these alternative pathways. For example, did they observe specific lysosomal markers or structural improvements in lysosomes upon ALA treatment? Additional data or controls would be necessary to support a lysosome-specific protective mechanism and to exclude the involvement of other PUFA-responsive pathways in the observed phenotypes.

Reviewer #2 (Public review):

Tittelmeier et al. investigated the role of sphingolipid (SL) metabolism in the maintenance of endolysosomal vesicle integrity. They find that both impaired SL biosynthesis and degradation in C. elegans, decrease the fluidity of endolysosomal membranes and promote their rupture, while it has little effect on plasma membrane fluidity. Endolysosomal membrane fluidity is also negatively affected in human cells upon knockdown (KD) of a gene (SPHK2) involved in the SL degradation pathway. Aggregated forms of tau in both models (C. elegans and human cells) can also cause rigidification of the endolysosomal membrane, with SL homeostasis disruption having an additive effect, exacerbating endolysosomal rupture. Notably, KD of SPHK2 also increased the formation of tau foci, suggesting that compromised endolysosomal integrity may promote tau aggregation. These data provide a clearer understanding of how genetic manipulation of SL metabolism affects endolysosomal membranes and their rigidification in the context of tau aggregation. Supplementation of polyunsaturated fatty acids (PUFAs), which has a beneficial effect on Alzheimer's patients, improved membrane fluidity and reduced tau propagation in human cells and tau-associated neurotoxicity in C. elegans, suggesting a possible mechanism of action.

Overall, the conclusions of this paper are supported by the data, with a few aspects requiring further clarification and elaboration.

(1) A reference to Figure S2E-G, which shows that KD of SL biosynthesis genes do not affect the plasma membrane, is missing from the main text.

(2) In Figure 3C, lipofectamine alone shows that it increases membrane rigidity (increased GP values), not membrane fluidity.

(3) In Figure 3F, the EV cntl condition expressing F3:mCh tau should have increased LGALS3 foci compared to the mCh EV cntl according to Ref (20) and its Figure 2G (at least for Day 5 animals), which would be indicative of the tau spreading in hypodermal tissue. What C. elegans age was examined in Figure 3F? Can the authors provide evidence of the transmission of the F3:mCh tau from the touch receptor neurons to the hypodermis in the EV [similar to Figure 2C & D from Ref (20)] and compare it to the KDs? Otherwise, it seems that KD of SL genes impacts not only endolysosomal rupture but significantly affects tau accumulation/spreading as well (e.g., shown later in HEK cells, where SPHK2 KD increases the formation of tau-Venus foci).

(4) Sphingolipids are essential membrane components and signaling molecules. Does KD of SL genes in C. elegans and the subsequent endolysosomal rupture cause any major, intermediate, or minor defects/phenotypes (in non-aggregation prone models, w/t..)?

Reviewer #3 (Public review):

Summary:

The authors set off with an analysis of the lysosomal integrity upon knockdown of genes of the sphingolipid metabolic pathway that they identified in a previous (yet unpublished) work of an RNA screen using a new C. elegans Tau model. They then used cell culture and C. elegans experiments to study the link between lysosomal rupture and Tau propagation.

Strengths:

The authors use two complementary model systems and use probes to assess membrane rigidity that allow a quick assessment of the membrane dynamics and offer the opportunity to treat the cells with lipids, RNAi. Tau seeds, etc.

Weaknesses:

The main weakness is that this work builds on not-yet-peer-reviewed manuscript that established a new C. elegans Tau model and RNAi screen that aimed to identify genes involved in the propagation of Tau.

This reviewer misses essential information of the C. elegans Tau strain (not included in the method section): e.g., promoter used for the expression, information on the used Tau variant, expression pattern, and aggregation, etc.

Throughout the study, I missed data on:

(1) Effect of the knockdown on Tau expression, localisation (with lysosomal membrane?), aggregation, and proteotoxicity. The effect of the RNAi-mediated knockdown could also simply lead to a reduced expression of Tau that, in turn, leads to suppressed propagation.

(2) A quantification of RNAi knockdown is needed to judge the efficiency of the RNAi, in particular for the combinatorial RNAi experiments involving 2 and even 4 genes in parallel. Ideally, these analyses should be validated with mutants for these genes.

Further:

(3) Figure 4 H, I: Would Tau also aggregate in the absence of externally added Tau?

(4) How specific is the effect for Tau? It would help if the authors could assess other amyloid proteins.

(5) The connection between sphingolipids and AD is not new. See He et al, 2010, Neurobiol. Aging + numerous publications and also not between Tau seeding and lysosomal rupture: Rose et al., PNAS 2024 (that has been cited by the authors).

Reviewer #1 (Public review):

Summary:

It is now increasingly becoming clear that macromolecules and their complexes can form larger structures such as filaments or cages in the cells under certain conditions. These can be beneficial for the cells to promote and coordinate metabolic activity or result in protection against stress. Reactive oxygen species (ROS) can be damaging to macromolecules in cells that grow both aerobically and anaerobically, and they have evolved different mechanisms to cope with ROS. Aerobic organisms have a number of enzymes to combat ROS, while anaerobic organisms have evolved other means, and one such mechanism is described by Song et al in the article.<br /> In Pyrococcus furiosus, a hyperthermophilic anaerobic bacterium, Song et al describe the formation of Oxidative stress-induced tubular structures (OSITs). Using proteomics and electron cryomicroscopy (CryoEM), the authors find that the protein Rubrerythrin is upregulated upon exposure to oxygen, and the tetramer of this protein assembles to form these tubules that are varied in length with a consistent diameter of ~480 Å. They further observe that some of these tubules also have spherical viral-like particles. With enriched fraction of the OSITs from the cells and proteomics, it is shown that the predominant protein is encapsulin, which forms a caged structure and traps ferric iron. The combined structures of OSIT by rubreerythrin and the VLPs of encapsulin protect the cells from oxygen radicals by forming a complex.

Strengths:

The combination of proteomics and electron microscopy with the employment of both tomography of cellular sections and single particle cryoEM of enriched samples.

Weaknesses:

Some description of the methods, in particular the workflow of image processing, is not easy to follow and can be described with more clarity and be easier for non-experts to read/understand.

Reviewer #2 (Public review):

The manuscript entitled "Structure of an oxygen-induced tubular nanocompartment in Pyrococcus furiosus" by Wenfei Song et al. employs whole-cell mass spectrometry and cryo-EM (including tomography, helical reconstruction, and single-particle analysis) to investigate the structure and function of the oxidoreductase Rubrerythrin (Rbr) from Pyrococcus furiosus. The study reports that under oxidative stress, Rbr forms a tubular structure, in contrast to its behaviour under anaerobic conditions. Authors characterized oxidoreductase Rubrerythrin (Rbr) from Pyrococcus furiosus under anaerobic conditions and formed a tubular structure when induced with oxidative stress. This study is well-designed. However, I have several questions related to the experimental design and the results obtained from those experiments, which are listed below.

(1) The authors have mentioned that "Under aerobic conditions, Rbr levels are 3 to 13 times higher compared to anaerobic conditions (Figures 1a-d)." Also, they performed whole-cell mass spec to measure the overexpression of the Rbr enzyme under anaerobic conditions. Thus, from the above statement, I consider the authors' claim that P. furiosus cells were cultured under anaerobic conditions and then exposed to oxidative stress. While cell growth under anaerobic conditions appears perfectly fine, the authors conducted the rest of the experiment under aerobic conditions during mass spectrometry and cryo-EM sample preparation. As a baseline, the author first grew the cells in their preferred anaerobic environment and also imaged the same cells that were exposed to air (aerobic) after anaerobic growth. The cell growth in anaerobic conditions is perfectly fine. But how did authors make sure that during anaerobic conditions, the Rbr enzyme is not expressed or not formed? As a control experiment, authors should demonstrate that during mass spec and cryo-EM sample preparations, cells are not exposed to air or maintained in an anaerobic environment. From anaerobic conditions, whenever cells were selected for spec and cryo-EM, cells were exposed to O2, and definitely controlled cells were not in anaerobic conditions anymore.

The authors collected P. furiosus wild-type or Rbr knockout cells in an anaerobic hood, but after that, they centrifuged the cells and plunged them using a Vitrobot. Are the instrument, centrifuge, and Vitrobot kept in an anaerobic environment? Recently, a few studies (anaerobic plunge-freezing in cryo-electron microscopy, Cook et al. (2024), Hands-Portman and Bakker (2022) DOI: 10.1039/D2FD00060A ) have mentioned the anaerobic plunge freeze setup for protein sample or cell freezing. I guess the authors did not use that setup. In these circumstances, the cell is already exposed to O2 during centrifugation and Vitrobot freezing. How were the control experiments properly performed in anaerobic conditions? A similar argument is true for Lamella grid preparation, where the enzyme was already exposed to O2, and single-particle grid preparation, where the purified enzyme is already exposed to O2. How were the control experiments properly performed in anaerobic conditions?

(2) It is important to provide evidence that the overexpressed protein is actually in an anaerobic condition and is later induced with more O2. Also, authors should confirm biochemically that the overexpressed protein in their desired protein "oxidoreductase Rubrerythrin (Rbr)". No biochemical data were provided in this manuscript. During single-particle analysis, the authors had to purify the protein sample and confirm that these were their desired protein samples. No biochemical or biophysical experiments were performed to confirm that the overexpressed protein is the desired protein.

(3) Figure 3, the atomic model looks different in all four tetramers. However, I have fitted the atomic model into the cryo-EM map, which looks reasonable. However, it will be easier for the reader to evaluate the model if the authors show different orientations of the atomic model, as well as if the authors could show that the atomic model fits the cryo-EM map.

(4) How did the authors select initial particle sets like 24 lakhs when forming helices and not forming isolated particles?

(5) The authors proposed a model for electron transfer upon oxidative stress. However, the data is not convincing that VLP is surrounded by Rbr and forms a tube-like structure. Generally, VLP is a sphere-like structure, and Rbr can form a tube-like structure when it interacts with spherical VLP. Rbr will surround VLP, and it will form a Rbr-decorated sphere-like structure.

(6) It will also be important to comment on the diameter of Oxidative stress-induced tubules (OSITs) and 3D reconstruction and/or helical reconstruction of purified protein samples. The spherical cyan densities within the tube are not very clear. If VLP is surrounded by Rbr (Figure 4), extra Rbr densities will be observed on VLP in the tomogram (in Figure 1). However, in the tomogram, VLP is inside Oxidative stress-induced tubules (OSITs). Figure 1 is a contradicting Figure 4. The authors should explain it properly.

(7) The authors performed helical reconstruction. Where is the Layer line calculation in helical reconstruction, and how do authors identify helical parameters for reconstruction?

(8) The authors used an extremely confusing methodology, which was very difficult to follow. The authors performed tomography, helical reconstruction, and single-particle analysis. Why did the authors need 3 different image processing methods to resolve structures that are not clear to me? The authors should also show the proper fitting between the map and the model. In Supplemental Figure 6c, the overall fitting of the subdomain looks ok. However, many peptide chains and side chains are not fitted properly in the EM density map. It will be helpful to show proper side chain fitting. In Supplementary Fig. 6a, the authors binned the data (Bin 8 or Bin 2) but did not mention when they unbinned the data for data processing. Also, the authors implemented C2 symmetry during local refinement. Why do authors suddenly use C2 symmetry expansion?

Minor Comments:

(1) The authors should properly show a schematic diagram of the enzyme subdomains. It will help to understand interactions or tetrameric assembly.

(2) The introduction is poorly written. It will really be helpful for the reader if the authors provide a proper introduction.

(3) The atomic model did not fit into the cryo-EM, so it was hard to determine the overall fitting.

(4) 17.1A pixel size? It's surprising.

(5) It will be better to calculate local resolution and show the map's angular distribution. It is obvious that resolution at the peripheral region will be poorer than core region. Therefore, it will be better to calculate local resolution. Additionally, authors should show the map to model fitting.

Reviewer #3 (Public review):

Summary:

The manuscript authored by Song et al explores the oxidative stress response of Rubrerythrin in Pyrococcus furiosus and the formation of unique tubules that also encapsulate Encapsulin VLPs. This is an excellent study employing diverse methods to comprehensively study the formation of these assemblies under oxidative stress and lays the foundation of understanding oxidative stress through the formation of tubules among redox-sensing proteins like Rubrerythrin. The authors decipher the molecular structure of the tubules and also present a high-resolution reconstruction of the rubrerythin unit that forms the OSITs.

Strengths:

The study is done thoroughly by employing methods like cryoET, single particle cryoEM, mass spectrometry, and expression analyses of knockout strains to delve into an important mechanism to counter oxidative stress. The authors perform comprehensive analyses, and this study represents a vital contribution to understanding how anaerobic organisms can respond to oxidative stress.

Weaknesses:

Not all encapsulin particles seem to be inside the OSITs. Do the authors have any insights into how the tubules sequester these viral particles? Do the VLPs have a role in nucleating the OSIT assembly, and are there interactions between VLP and OSIT surfaces? These could be points that can be discussed in greater detail by the authors.

Can the authors get a subtomogram averaging done for the encapsulin VLPs? A higher resolution reconstruction may provide potential interaction details with the OSITs, if there are any.

The role of the dense granules observed in the rubrerythrin deletion strain is not very well discussed. Is there a way these granules counter oxidative stress? The EDX scanning seems to show a Phosphate increase similar to Ca and Mg. Are these aggregates therefore likely to be calcium and Mg phosphate aggregates? This section of the paper seems incompletely analysed.

The authors should provide density and coordination distances around the diiron ions and provide a comparison with available crystal structures and highlight differences, if any, in Figure 3. Local resolution for the high-res map may be provided for Supplementary Figure 6.

Overall, this is a well-performed study with clear conclusions. The discussion points need to be improved further.

Reviewer #1 (Public review):

Summary:

This study shows a novel role for SCoR2 in regulating metabolic pathways in the heart to prevent injury following ischemia/reperfusion. It combines a new multi-omics method to determine SCoR2 mediated metabolic pathways in the heart. This paper would be of interest to cardiovascular researchers working on cardioprotective strategies following ischemic injury in the heart.

Strengths:

(1) Use of SCoR2KO mice subjected to I/R injury.

(2) Identification of multiple metabolic pathways in the heart by a novel multi-omics approach.

Weaknesses:

(1) Use of a global SCoR2KO mice is a limitation since the effects in the heart can be a combination of global loss of SCoR2.

(2) Lack of a cell type specific effect.

Reviewer #2 (Public review):

Summary:

This manuscript addresses the gap in knowledge related to the cardiac function of the S-denitrosylase SNO-CoA Reductase 2 (SCoR2; product of the Akr1a1 gene). Genetic variants in SCoR2 have been linked to cardiovascular disease, yet their exact role in the heart remains unclear. This paper demonstrates that mice deficient in SCoR2 show significant protection in a myocardial infarction (MI) model. SCoR2 also affected ketolytic energy production, antioxidant levels, and polyol balance through the S-nitrosylation of crucial metabolic regulators.

Strengths:

(1) Addresses a well-defined gap in knowledge related to the cardiac role of SNO-CoA Reductase 2. Besides the in-depth case for this specific player, the manuscript sheds more light on the links between S-nitrosylation and metabolic reprogramming in the heart.

(2) Rigorous proof of requirement through the combination of gene knockout and in vivo myocardial ischemia/reperfusion.

(3) Identification of precise Cys residue for SNO-modification of BDH1 as SCoR2 target in cardiac ketolysis

Weaknesses:

(1) The experiments with BDH1 stability were performed in mutant 293 cells. Was there a difference in BDH1 stability in myocardial tissue or primary cardiomyocytes from SCoR2-null vs -WT mice? The same question extends to PKM2.

(2) In the absence of tracing experiments, the cross-sectional changes in ketolysis, glycolysis, or polyol intermediates presented in Figures 4 and 5 are suggestive at best. This needs to be stressed while describing and interpreting these results.

(3) The findings from human samples with ischemic and non-ischemic cardiomyopathy do not seem immediately or linearly in line with each other and with the model proposed from the KO mice. While the correlation holds up in the non-ischemic cardiomyopathy (increased SNO-BDH1, SNO-PKM2 with decreased SCoR2 expression), how do the authors explain the decreased SNO-BDH1 with preserved SCoR2 expression in ischemic cardiomyopathy? This seems counterintuitive as activation of ketolysis is a quite established myocardial response to ischemic stress. It may help the overall message clarity to focus the human data part on only NICM patients.

(4) This issue is partially linked to point #(3). Currently, important evidence that is lacking is the demonstration of sufficiency for SCoR2 in S-nytrosylation of targets and cardiac remodeling. Does SCoR2 overexpression in the heart or isolated cardiomyocytes reduce S-nitrosylation of BDH1 and other targets, thus affecting heart function at baseline or under stress?

Reviewer #3 (Public review):

Summary:

This manuscript demonstrates that mice lacking the denitrosylase enzyme SCoR2/AKR1A1 demonstrate robust cardioprotection resulting from reprogramming of multiple metabolic pathways, revealing widespread, coordinated metabolic regulation by SCoR2.

Strengths:

(1) The extensive experimental evidence.

(2) The use of the knockout model.

Weaknesses:

(1) Lack of direct evidence for underlying mechanism(s).

(2) The mouse model used is not tissue-specific.

Reviewer #1 (Public review):

The authors present exciting new experimental data on the antigenic recognition of 78 H3N2 strains (from the beginning of the 2023 Northern Hemisphere season) against a set of 150 serum samples. The authors compare protection profiles of individual sera and find that the antigenic effect of amino acid substitutions at specific sites depends on the immune class of the sera, differentiating between children and adults. Person-to-person heterogeneity in the measured titers is strong, specifically in the group of children's sera. The authors find that the fraction of sera with low titers correlates with the inferred growth rate using maximum likelihood regression (MLR), a correlation that does not hold for pooled sera. The authors then measure the protection profile of the sera against historical vaccine strains and find that it can be explained by birth cohort for children. Finally, the authors present data comparing pre- and post- vaccination protection profiles for 39 (USA) and 8 (Australia) adults. The data shows a cohort-specific vaccination effect as measured by the average titer increase, and also a virus-specific vaccination effect for the historical vaccine strains. The generated data is shared by the authors and they also note that these methods can be applied to inform the bi-annual vaccine composition meetings, which could be highly valuable.

The following points could be addressed in a revision:

(1) The authors conclude that much of the person-to-person and strain-to-strain variation seems idiosyncratic to individual sera rather than age groups. This point is not yet fully convincing. While the mean titer of an individual may be idiosyncratic to the individual sera, the strain-to-strain variation still reveals some patterns that are consistent across individuals (the authors note the effects of substitutions at sites 145 and 275/276). A more detailed analysis, removing the individual-specific mean titer, could still show shared patterns in groups of individuals that are not necessarily defined by the birth cohort.

(2) The authors show that the fraction of sera with a titer below 138 correlates strongly with the inferred growth rate using MLR. However, the authors also note that there exists a strong correlation between the MLR growth rate and the number of HA1 mutations. This analysis does not yet show that the titers provide substantially more information about the evolutionary success. The actual relation between the measured titers and fitness is certainly more subtle than suggested by the correlation plot in Figure 5. For example, the clades A/Massachusetts and A/Sydney both have a positive fitness at the beginning of 2023, but A/Massachusetts has substantially higher relative fitness than A/Sydney. The growth inference in Figure 5b does not appear to map that difference, and the antigenic data would give the opposite ranking. Similarly, the clades A/Massachusetts and A/Ontario have both positive relative fitness, as correctly identified by the antigenic ranking, but at quite different times (i.e., in different contexts of competing clades). Other clades, like A/St. Petersburg are assigned high growth and high escape but remain at low frequency throughout. Some mention of these effects not mapped by the analysis may be appropriate.

(3) For the protection profile against the vaccine strains, the authors find for the adult cohort that the highest titer is always against the oldest vaccine strain tested, which is A/Texas/50/2012. However, the adult sera do not show an increase in titer towards older strains, but only a peak at A/Texas. Therefore, it could be that this is a virus-specific effect, rather than a property of the protection profile. Could the authors test with one older vaccine virus (A/Perth/16/2009?) whether this really can be a general property?

Reviewer #2 (Public review):

This is an excellent paper. The ability to measure the immune response to multiple viruses in parallel is a major advancement for the field, which will be relevant across pathogens (assuming the assay can be appropriately adapted). I only have a few comments, focused on maximising the information provided by the sera.

Firstly, one of the major findings is that there is wide heterogeneity in responses across individuals. However, we could expect that individuals' responses should be at least correlated across the viruses considered, especially when individuals are of a similar age. It would be interesting to quantify the correlation in responses as a function of the difference in ages between pairs of individuals. I am also left wondering what the potential drivers of the differences in responses are, with age being presumably key. It would be interesting to explore individual factors associated with responses to specific viruses (beyond simply comparing adults versus children).

Relatedly, is the phylogenetic distance between pairs of viruses associated with similarity in responses?

Figure 5C is also a really interesting result. To be able to predict growth rates based on titers in the sera is fascinating. As touched upon in the discussion, I suspect it is really dependent on the representativeness of the sera of the population (so, e.g., if only elderly individuals provided sera, it would be a different result than if only children provided samples). It may be interesting to compare different hypotheses - so e.g., see if a population-weighted titer is even better correlated with fitness - so the contribution from each individual's titer is linked to a number of individuals of that age in the population. Alternatively, maybe only the titers in younger individuals are most relevant to fitness, etc.

In Figure 6, the authors lump together individuals within 10-year age categories - however, this is potentially throwing away the nuances of what is happening at individual ages, especially for the children, where the measured viruses cross different groups. I realise the numbers are small and the viruses only come from a small numbers of years, however, it may be preferable to order all the individuals by age (y-axis) and the viral responses in ascending order (x-axis) and plot the response as a heatmap. As currently plotted, it is difficult to compare across panels

Reviewer #3 (Public review):

The authors use high-throughput neutralisation data to explore how different summary statistics for population immune responses relate to strain success, as measured by growth rate during the 2023 season. The question of how serological measurements relate to epidemic growth is an important one, and I thought the authors present a thoughtful analysis tackling this question, with some clear figures. In particular, they found that stratifying the population based on the magnitude of their antibody titres correlates more with strain growth than using measurements derived from pooled serum data. However, there are some areas where I thought the work could be more strongly motivated and linked together. In particular, how the vaccine responses in US and Australia in Figures 6-7 relate to the earlier analysis around growth rates, and what we would expect the relationship between growth rate and population immunity to be based on epidemic theory.

Reviewer #1 (Public review):

Summary:

In this manuscript, Uphoff et al. propose a structural and mechanistic model in which the multidomain ECM protein SVEP1 enables Angiopoietin (ANG) binding to the orphan receptor TIE1, thereby promoting downstream receptor phosphorylation and signaling. Using AlphaFold-based modeling, the authors predict that the CCP20 domain of SVEP1 binds to TIE1, creating a composite surface that facilitates Angiopoietin association and TIE1 activation. The resulting ternary model (SVEP1-TIE1-ANG) offers a structural rationale for how SVEP1 converts TIE1 into a functional, ligand-responsive receptor. Additional models and biological assays suggest roles for other domains of SVEP1, such as CCP5-EGF-L7, although these interactions are predicted with low confidence. The authors interpret these findings as the first structural framework for how SVEP1 enables ANG-TIE1 signaling.

Strengths:

(1) The central hypothesis - that SVEP1 enables ANG binding to the orphan receptor TIE1 - is biologically compelling and addresses an important question in vascular biology.

(2) The AlphaFold-predicted ternary complex (SVEP1-TIE1-ANG) is plausible, high-confidence, and structurally consistent with prior functional data (e.g., poly-Ala scanning from Sato-Nishiuchi et al.).

(3) The authors' model offers a potential explanation for the previously observed role of SVEP1 in enhancing ANG signaling through TIE1, and may represent the first structural insight into TIE1's transition from orphan to ligand-activated receptor.

(4) The potential clinical implication - that a combinatorial ligand (ANG+SVEP1) can activate TIE1- could have translational relevance for vascular leak and inflammatory disease.

Weaknesses:

(1) Lack of structural validation and mechanistic follow-up:
Despite the promising AlphaFold model, there are no figures of the predicted interface, no residue-level interactions shown, no ipTM values reported, and no experimental follow-up to test the interface. PAE plots are incorrectly used as confidence justifications, which is not appropriate for complex predictions.

(2) Biophysical validation is missing:
No surface plasmon resonance (SPR), ITC, or biochemical assays are included to confirm ternary complex formation or quantify binding kinetics. Given the manuscript's structural focus, this is a major gap. For instance, an SPR experiment where ANG is immobilized, and TIE1 binding is measured {plus minus} SVEP1, would directly test the model. And allow direct comparison to ANG-TIE2.

(3) Missed opportunity for mutagenesis-driven validation:
 The manuscript does not include any interface-targeted mutations, despite clear opportunities. For example, mutating T2595 in SVEP1 (to R) or mutating the TIE1-specific residues (residues PL 202-203 to LF) could strongly test the model and potentially reveal dominant-negative behaviors. E.g. A T2595 mutant should block ANG binding but not TIE1 binding.

(4) Overinterpretation of weak models:
The additional AlphaFold model involving the CCP5-EGFL7 domains binding TIE1 has extremely low confidence (ipTM < 0.15) when reexamined by this reader and should not be emphasized. There is no biophysical evidence or binding data (SPR) to support this interaction, and its inclusion detracts from the much stronger CCP20 model.

(5) Language around modeling is overstated and potentially misleading:
Terms like "unequivocal," "high-affinity," or "affirms strong binding" in reference to AlphaFold predictions are inappropriate. These are hypotheses -not confirmations - and must be tested at the biochemical level. This should be clarified throughout the manuscript to ensure non-experts do not misinterpret modeling confidence as binding affinity.

(6) Negative stain EM data is not informative due to low resolution and lack of defined interfaces; unless replaced by higher-resolution Cryo-EM, this should be omitted. Better would be co-gel filtration, AUC, or SEC-MALLs with ANG-SVEP1-TIE1.

(7) Disjointed narrative:
The manuscript presents a compelling mechanism involving CCP20-driven ANG binding to TIE1, but then becomes fragmented by introducing the low-confidence CCP5-EGFL7 model and speculative higher-order polymerization models that are not experimentally supported.

Reviewer #2 (Public review):

Uphoff and colleagues present the results of a study focused on characterizing the binding of SVEP1 to TIE1 along with Angiopoietin-2. Starting with computational prediction of SVEP1 binding to TIE1, the authors identify the region of SVEP1 that serves as a high-affinity ligand for TIE1. Advanced studies identify a weak secondary binding site within SVEP1 that appears to be sufficient but not necessary for its interaction with TIE1 based on in vivo rescue experiments. The most novel contribution of the manuscript seems to be the identification of angiopoietin-1 and -2 as co-factors that seem to enhance the binding of SVEP1 with TIE1 and impact downstream AKT signaling. They propose a complex in which SVEP1 binds to TIE1 and ANG2.

Although the first set of results is essentially confirmatory, the identification of ANG-2 as a "co-factor" enhancing the binding of SVEP1 to TIE1 and associated downstream signaling (i.e., Figures 3 and 4) is novel and is of interest. However, the manuscript and its conclusions would greatly benefit from some clarifying details and additional experiments to ensure rigor and support specific claims.

Reviewer #1 (Public review):

Engineering of AAV replication proteins may provide new insights into Parvoviral replication and potentially enable improved recombinant AAV vector yield when incorporated into the manufacturing process. Silberg and colleagues report an AAV Rep library, that is an interesting and powerful approach, however, the screening design and subsequent experiments lack rigor and ultimately the results are premature. Overall, the manuscript does not accurately describe state-of-the-art in the field and has significant shortcomings with experimental design/data analysis. Key concerns are noted below:

The high enrichment of P19 variants in the library was likely an artifact of the fact they only transfected 20 ng of RepCap into their 5-plate preps. When such little Rep is provided, any boost in Rep expression levels will have a major on yield. When more RepCap is provided, 10 ug in their later evaluation, small changes in Rep expression are unlikely to have major impacts on yield. A more effective strategy would have been to transfect a normal amount of DNA and then utilize serial passaging through infectious cycling to account for cross packaging.

Introduction:<br /> - There are 7 FDA approved AAV gene therapies.<br /> - The description of "shuffling" when citing Mietsczh et al is misapplied. The cited paper discusses rationally designed hybrids.<br /> - The graphic represents a hybrid capsid, but the focus is rep. As such, this should be depicted differently.

Figures 1 and 2 are validation of previously published findings and general optimization of the experimental conditions. These do not provide the reader any new insight or information.

In Figure 3: The experimental approach is limited. It is unclear how the subpooling of different conditions was performed. As mentioned above, their library transfection strategy will significantly bias the results. The enriched variants have not been evaluated - specifically, the enriched non-synonymous mutations have not been shown to yield higher titers when tested individually.<br /> In Figure 4: The claim is made that "several synonymous mutations within the p19 promoter region increase Rep DNA packaging activity." However, Figure 4c does not show statistically significant differences in support of this claim. Additional supporting data is needed. Further, Authors state that the synonymous mutations are near the P19 promoter. However, looking at the sequence shown in figure 4, their annotation of the P19 promoter is not correct and the mutations are actually within the P19 promoter. Relatedly, the authors note that mutations enriched in the p19 region include additional tetranucleotide repeats. No synthetic variants with additional GCTCs have been generated to test this hypothesis. Further, these results would benefit from a Western blot and transcript analysis to confirm Rep52/40, expression levels of constructs.

Reviewer #2 (Public review):

In the present study the authors have investigated the effects of mutations on Rep protein ability to package DNA within the gene therapy vector, AAV. A detailed investigation of Rep mutants selected from a library has been probed for their ability to produce active virions. While the concept is interesting the outcome effects are very limited.

The major issue is the lack of immediate applicability and relevance in the vector production pipeline for AAV. The authors have found that with the synthetic GFP transgene cargo, mutations of the p19 promoter did not lead to enhanced AAV vector packing. Thus the data is quite preliminary and a complete characterization may be necessary to further enhance the translational potential of the approach.

Reviewer #3 (Public review):

While the AAV capsid has long been the target of protein engineering, its Rep proteins have been comparatively less studied. Since Rep plays a variety of roles for genome replication and virion packaging, gaining a deeper mechanistic understanding of their function and/or engineering versions that enable higher packaging productivity would be of interest to the field. This study generates a library of non-synonymous mutations in AAV2 rep (intended to cover all 19 aa changes at all positions, and coming close), packaged an AAV with AAV9 capsid, and sequenced the results to assess which amino acid changes resulted in an enrichment/depletion of genomes containing that variant rep. They found that proline substitutions are disruptive, well known from protein mutagenesis studies. The most significant enrichment sfound, however, were a set of synonymous mutations (unintended members of the library, as the library was designed to contain non-synonymous mutations) that lie within the p19 promoter. However, attempts to package recombinant vector using these individual rep variants in the AAV helper construct did not increase viral titer.

A previous study conducted analogous mutagenesis on Rep: Jain et al., "Comprehensive mutagenesis maps the effect of all single-codon mutations in the AAV2 rep gene on AAV production" eLife 2024 (cited here as reference 19). It is not clear that this current study is a significant advance relative to the prior, quite comprehensive study. Both generated a library of non-synonymous mutations and observed fitness effects on Rep. Because this study sequenced the full rep, rather than barcodes associated with each rep variant, it found the enrichment in the synonymous mutations. However, these should ideally advance a basic understanding of Rep biology and/or result in better AAV production, but they did neither. It is speculated in the Discussion that the mutations generated additional GCTC motifs in p19, elements that mediate protein-DNA interactions. However, the role of GCTC motifs is speculative, and no transcriptional analysis is conducted. Furthermore, as discussed above, the mutations do not result in higher viral titers. Perhaps there's a transcriptional effect at the much lower copy numbers of vector genome present during library selection vs. rAAV packaging. They also found stop codons in Rep domains thought to be required for viral packaging, but functional studies confirming the screening findings are not conducted. As a result, the biological or technical relevance of the findings are extremely unclear, and thus the impact is relatively low.

The description of herring DNA co-transfection and cross-packaging (which is a well-known pitfall) are somewhat technical and arguably don't merit too much main manuscript attention.

Reviewer #1 (Public review):

Summary:

The authors test whether the archerfish can modulate the fast response to a falling target. By manipulating the trajectory of the target, they claim that the fish can modulate the fast response. While it is clear from the result that the fish can modulate the fast response, the experimental support for argument that the fish can do it for a reflex like behavior is inadequate.

Strengths:

Overall, the question that the authors raised in the manuscript is interesting.

Weaknesses:

Major comments:

(1) The argument that the fish can modulate reflex-like behavior relies on the claim that the archerfish makes the decision in 40 ms. There is little support for the 40 ms reaction time. The reaction time for the same behavior in Schlegel 2008, is 60-70 ms and in Tsvilling 2012 about 75 ms, if we take the half height of the maximum as estimated reaction time in both cases. If we take the peak (or average) of the distribution as an estimation of reaction time, the reaction time is even longer. This number is critical for the analysis the authors perform since if the reaction time is longer, maybe this is not a reflex as claimed. In addition, mentioning the 40 ms in the abstract is overselling the result. The title is also not supported by the results.

(2) A critical technical issue of the stimulus delivery is not clear. The frame rate is 120 FPS and the target horizontal speed can be up to 1.775 m/s. This produces target jumping on the screen 15 mm each frame. This is not a continuous motion. Thus, the similarity between the natural system where the target experience ballistic trajectory and the experiment here is not clear. Ideally, another type of stimulus delivery system is needed for a project of this kind that requires fast moving targets (e.g. Reiser, J. Neurosci.Meth. 2008). In addition, the screen is rectangular and not circular, so in some directions the target vanishes earlier than others. It must produce a bias in the fish response but there is no analysis of this type.

(3) The results here rely on the ability to measure the error of response in the case of virtual experiment. It is not clear how this is done since the virtual target does not fall. How do authors validate that the fish indeed perceives the virtual target as falling target? Since the deflection is at a later stage of the virtual trajectory, it is not clear what is the actual physics that governs the world of the experiment. Overall, the experimental setup is not well designed.

Comments on revisions:

The authors handled the comments, and the manuscript has improved accordingly. While some issues could still benefit from further clarification and depth, the current version meets the necessary standards.

Reviewer #2 (Public review):

Summary:

This manuscript studies the prey capture by archer fish, which observe the initial values of motion of aerial prey they made fall by spitting on them, and then rapidly turn to reach the ballistic landing point on the water surface. The question raised by the article is whether this incredibly fast decision-making process is hardwired and thus unmodifiable or can be adjusted by experience to follow a new rule, namely that the landing point is deflected from a certain amount from the expected ballistic landing point. The results show that the fish learn the new rule and use it afterwards in a variety of novel situations that include height, side and speed of the prey, and which preserve the speed of the fish's decision. Moreover, a remarkable finding presented in this work is the fact that fish that have learned to use the new rule can relearn to use the ballistic landing point for an object based on its shape (a triangle) while keeping simultaneously the 'deflected rule' for an object differing in shape (a disc); in other words, fish can master simultaneously two decision-making rules based on the different shape of objects.

Strengths:

The manuscript relies on a sophisticated and clever experimental design that allows changing the apparent landing point of a virtual prey using a virtual reality system. Several robust controls are provided to demonstrate the reliability and usefulness of the experimental setup.

Overall, I like very much the idea conveyed by the authors that even stimuli triggering apparently hardwired responses can be relearned in order to be associated to a different response, thus showing the impressive flexibility of circuits that are sometimes considered as mediating pure reflexive responses. This is the case - as an additional example - of the main component of the Nasanov pheromone of bees (geraniol), which triggers immediate reflexive attraction and appetitive responses, and which can, nevertheless, be learned by bees in association with an electric shock so that bees end up exhibiting avoidance and the aversive response of sting extension to this odorant(1), which is a fully unnatural situation, and which shows that associative aversive learning is strong enough to override preprogrammed responding, thus reflecting an impressive behavioral flexibility.

Weaknesses:

As a general remark, there is some information that I missed and that are mandatory in the analysis of behavioral changes: one is the variability in the performances displayed. The authors mentioned that the results reported come from 6 fish (which is a low sample size). How were the individual performances in terms of consistency? Were all fish equally good in adjusting/learning the new rule? How did errors vary according to individual identity? It seems to me that this kind of information should be available as the authors reported that individual fish could be recognized and tracked (see lines 620-635) and is essential for appreciating the flexibility of the system under study.

The other information that I could not find explained in a proper way is referred to the speed of the learning process. Admittedly, fish learn in an impressive way the new rule and even two rules simultaneously; yet, how long did they need to achieve this? In the article, Fig 2 mention that at least 6 training stages (each defined as a block of 60 evaluated turn decisions, which actually shows that the standard term 'Training Block' would be more appropriate) were required for the fish to learn the 'deflected rule'. While this means 360 trials (turning starts), I was left with the question of how long did this process last? How many hours, days, weeks were needed for the fish to learn? And as mentioned above, were al fish equally fast in learning? I would appreciate explaining this very important point because learning dynamics is relevant to understanding the flexibility of the system.

Comments After Revision:

There was consensus among reviewers that the authors addressed the initial critiques adequately and that the manuscript improved accordingly. The revision clarified several methodological aspects, and the addition of the new Fig. 2 was particularly helpful. It elucidates the experimental approach used in the study and offers essential context for understanding points that may have been unclear in the previous version.

Reviewer #1 (Public review):

In this study the authors aim to understand why decision formation during behavioural tasks is distributed across multiple brain areas. They hypothesize that multiple areas are used in order to implement an information bottleneck (IB). Using neural activity recorded from monkey DLPFC and PMd performing a 2-AFC task, they show that DLPFC represents various task variables (decision, color, target configuration), while downstream PMd primarily represents decision information. Since decision information is the only information needed to make a decision, the authors suggest that PMd has a minimal sufficient representation (as expected from an IB). They then train 3-area RNNs on the same task, and show that activity in the first and third areas resemble the neural representations of DLPFC and PMd, respectively. In order to propose a mechanism, they analyse the RNN and find that area 3 ends up with primarily decision information because feedforward connections between areas primarily propagate decision information.

Overall, the paper reads well and the data analysis and RNN modeling are well done and mostly correct. I agree with the authors that PMd has less information than DLPFC, meaning that some of the target and color information is attenuated. I also agree that this also happens in their multi-area RNN.

However, I find the use of the IB principle here muddles the water rather than clarifying anything. The key problem is that the authors evoke the information bottleneck in a mostly intuitive sense, but they do not actually use it (say, in their modelling). Rather, the IB is simply used to motivate why information will be or should be lost. Since the IB is a generic compressor, however, it does not make any statements about how a particular compression should be distributed or computed across brain areas.

If I ignore the reference to the information bottleneck, I still see a more mechanistic study that proposes a neural mechanism of how decisions are formed, in the tradition of RNN-modelling of neural activity as in Mante et al 2013. Seen through this more limited sense, the present study succeeds at pointing out a good model-data match.

Major points

(1) The IB is a formal, information-theoretic method to identify relevant information. However, in the paper, reference to the information bottleneck method (IB) is only used to motivate why (task-irrelevant) information should be lost in higher areas. The IB principle itself is actually never used. The RNNs are fitted using standard techniques, without reference to the IB. Without a formal link, I think the authors should describe their findings using words (e.g., task-irrelevant information is lost), rather than stating this as evidence for an information-theoretic principle.

(2) The advantage of employing a formal theory is that all assumptions have to be clarified. Since the authors only evoke the IB, but never employ it, they refrain from clarifying some of their assumptions. That is what creates unnecessary confusion.

For instance, the authors cite the following predictions of the IB principle: "(1) There exists a downstream area of cortex that has a minimal and sufficient representation to perform a task ... (2) there exists an upstream area of cortex that has more task information than the minimal sufficient area" - However, since the information bottleneck method is a generic compressor, it does not make any predictions about areas (or neurons). For a given sensory input p(x), a given task output p(y|x), and a given information loss, the IB generates exactly one optimal representation. In other words, the predictions made by the authors relie on other assumptions (e.g. feedforward processing, hierarchy, etc.) and these are not clearly stated.

(3) A corrollary to this problem is that the authors do not formally define task-irrelevant information. It seems the authors simply use the choice or decision as the thing that needs to be computed, and identify all other information as task-irrelevant. That's at least what I glean from the RNN model. However, I find that highly confusing because it suggests the conclusion that color information or target information are task-irrelevant. Surely, that cannot be true, since the decision is based on these quantities!

(4) If we define the output as the only task-relevant information, then any representation that is a pure motor representation would qualify as a minimal sufficient representation to carry out the correct actions. However, it is well-known that sensory information is lost in motor areas. It is not clear to me what exactly we gain by calling motor representations "minimal sufficient representations."

In summary, I think the authors should refrain from evoking the IB - which is a formal, mathematical principle - unless they actually use it formally as well.

Reviewer #2 (Public review):

This study advances our understanding of information encoding in the DLPFC and PMD brain regions. The conclusions are supported with convincing and robust analyses conducted on monkey datasets and trained RNN models. However, there are some concerns regarding the interpretation of findings related to the information bottleneck theory and the mapping of brain areas in the RNN simulations.

The authors' justification regarding mapping between model areas and anatomical areas remains insufficient, in my opinion. However, I recognize that my initial critique may not have been fully clear. The issue I see is this: whichever area is mapped to the first RNN module will trivially exhibit stimulus information, and downstream regions will naturally show a gradual loss of that information if one simply reads out their responses.

Thus, the observed stimulus loss in later modules could be an inevitable consequence of the model's structure, rather than a meaningful analog to the PFC-PMd transition. This point requires more careful justification or a reevaluation of the proposed mapping.

Reviewer #1 (Public review):

Summary:

In this manuscript, Pakula et al. explore the impact of reactive oxygen species (ROS) on neonatal cerebellar regeneration, providing evidence that ROS activates regeneration through Nestin-expressing progenitors (NEPs). Using scRNA-seq analysis of FACS-isolated NEPs, the authors characterize injury-induced changes, including an enrichment in ROS metabolic processes within the cerebellar microenvironment. Biochemical analyses confirm a rapid increase in ROS levels following irradiation and forced catalase expression, which reduces ROS levels, and impairs external granule layer (EGL) replenishment post-injury.

Strengths:

Overall, the study robustly supports its main conclusion and provides valuable insights into ROS as a regenerative signal in the neonatal cerebellum.

Comments on revisions:

The authors have addressed most of the previous comments. However, they should clarify the following response:

*"For reasons we have not explored, the phenotype is most prominent in these lobules, that is why they were originally chosen. We edited the following sentence (lines 578-579):

First, we analyzed the replenishment of the EGL by BgL-NEPs in vermis lobules 3-5, since our previous work showed that these lobules have a prominent defect."*

It has been reported that the anterior part of the cerebellum may have a lower regenerative capacity compared to the posterior lobe. To avoid potential ambiguity, the authors should clarify that "the phenotype" and "prominent defect" refer to more severe EGL depletion at an earlier stage after IR rather than a poorer regenerative outcome. Additionally, they should provide a reference to support their statement or indicate if it is based on unpublished observations.

Reviewer #2 (Public review):

Summary:

The authors have previously shown that the mouse neonatal cerebellum can regenerate damage to granule cell progenitors in the external granular layer, through reprogramming of gliogenic nestin-expressing progenitors (NEPs). The mechanisms of this reprogramming remain largely unknown. Here the authors used scRNAseq and ATACseq of purified neonatal NEPs from P1-P5 and showed that ROS signatures were transiently upregulated in gliogenic NEPs ve neurogenic NEPs 24 hours post injury (P2). To assess the role of ROS, mice transgenic for global catalase activity were assessed to reduce ROS. Inhibition of ROS significantly decreased gliogenic NEP reprogramming and diminished cerebellar growth post-injury. Further, inhibition of microglia across this same time period prevented one of the first steps of repair - the migration of NEPs into the external granule layer. This work is the first demonstration that the tissue microenvironment of the damaged neonatal cerebellum is a major regulator of neonatal cerebellar regeneration. Increased ROS is seen in other CNS damage models, including adults, thus there may be some shared mechanisms across age and regions, although interestingly neonatal cerebellar astrocytes do not upregulate GFAP as seen in adult CNS damage models. Another intriguing finding is that global inhibition of ROS did not alter normal cerebellar development.

Strengths:

This paper presents a beautiful example of using single cell data to generate biologically relevant, testable hypotheses of mechanisms driving important biological processes. The scRNAseq and ATACseq analyses are rigorously conducted and conclusive. Data is very clearly presented and easily interpreted supporting the hypothesis next tested by reduce ROS in irradiated brains.

Analysis of whole tissue and FAC sorted NEPS in transgenic mice where human catalase was globally expressed in mitochondria were rigorously controlled and conclusively show that ROS upregulation was indeed decreased post injury and very clearly the regenerative response was inhibited. The authors are to be commended on the very careful analyses which are very well presented and again, easy to follow with all appropriate data shown to support their conclusions.

Weaknesses:

The authors also present data to show that microglia are required for an early step of mobilizing gliogenic NEPs into the damaged EGL. While the data that PLX5622 administration from P0-P5 or even P0-P8 clearly shows that there is an immediate reduction of NEPs mobilized to the damaged EGL, there is no subsequent reduction of cerebellar growth such that by P30, the treated and untreated irradiated cerebella are equivalent in size. There is speculation in the discussion about why this might be the case. Additional experiments and tools are required to assess mechanisms. Regardless, the data still implicate microglia in the neonatal regenerative response, and this finding remains an important advance.

Reviewer #1 (Public review):

Summary:

Jin et al. investigated how the bacterial DNA damage (SOS) response and its regulator protein RecA affects the development of drug resistance under short-term exposure to beta-lactam antibiotics. Canonically, the SOS response is triggered by DNA damage, which results in the induction of error-prone DNA repair mechanisms. These error-prone repair pathways can increase mutagenesis in the cell, leading to the evolution of drug resistance. Thus, inhibiting the SOS regulator RecA has been proposed as means to delay the rise of resistance.

In this paper, the authors deleted the RecA protein from E. coli and exposed this ∆recA strain to selective levels of the beta-lactam antibiotic, ampicillin. After an 8h treatment, they washed the antibiotic away and allowed the surviving cells to recover in regular media. They then measured the minimum inhibitory concentration (MIC) of ampicillin against these treated strains. They note that after just 8 h treatment with ampicillin, the ∆recA had developed higher MICs towards ampicillin, while by contrast, wild-type cells exhibited unchanged MICs. This MIC increase was also observed in subsequent generations of bacteria, suggesting that the phenotype is driven by a genetic change.

The authors then used whole genome sequencing (WGS) to identify mutations that accounted for the resistance phenotype. Within resistant populations, they discovered key mutations in the promoter region of the beta-lactamase gene, ampC; in the penicillin-binding protein PBP3 which is the target of ampicillin; and in the AcrB subunit of the AcrAB-TolC efflux machinery. Importantly, mutations in the efflux machinery can impact the resistance towards other antibiotics, not just beta-lactams. To test this, they repeated the MIC experiments with other classes of antibiotics, including kanamycin, chloramphenicol, and rifampicin. Interestingly, they observed that the ∆recA strains pre-treated with ampicillin showed higher MICs towards all other antibiotics tested. This suggests that the mutations conferring resistance to ampicillin are also increasing resistance to other antibiotics.

The authors then performed an impressive series of genetic, microscopy, and transcriptomic experiments to show that this increase in resistance is not driven by the SOS response, but by independent DNA repair and stress response pathways. Specifically, they show that deletion of the recA reduces the bacterium's ability to process reactive oxygen species (ROS) and repair its DNA. These factors drive the accumulation of mutations that can confer resistance towards different classes of antibiotics. The conclusions are reasonably well-supported by the data, but some aspects of the data and the model need to be clarified and extended.

Strengths:

A major strength of the paper is the detailed bacterial genetics and transcriptomics that the authors performed to elucidate the molecular pathways responsible for this increased resistance. They systemically deleted or inactivated genes involved in the SOS response in E. coli. They then subjected these mutants to the same MIC assays as described previously. Surprisingly, none of the other SOS gene deletions resulted in an increase in drug resistance, suggesting that the SOS response is not involved in this phenotype. This led the authors to focus on the localization of DNA PolI, which also participates in DNA damage repair. Using microscopy, they discovered that in the RecA deletion background, PolI co-localizes with the bacterial chromosome at much lower rates than wild-type. This led the authors to conclude that deletion of RecA hinders PolI and DNA repair. Although the authors do not provide a mechanism, this observation is nonetheless valuable for the field and can stimulate further investigations in the future.

In order to understand how RecA deletion affects cellular physiology, the authors performed RNA-seq on ampicillin-treated strains. Crucially, they discovered that in the RecA deletion strain, genes associated with antioxidative activity (cysJ, cysI, cysH, soda, sufD) and Base Excision Repair repair (mutH, mutY, mutM), which repairs oxidized forms of guanine, were all downregulated. The authors conclude that down-regulation of these genes might result in elevated levels of reactive oxygen species in the cells, which in turn, might drive the rise of resistance. Experimentally, they further demonstrated that treating the ∆recA strain with an antioxidant GSH prevents the rise of MICs. These observations will be useful for more detailed mechanistic follow-ups in the future.

Weaknesses:

Throughout the paper, the authors use language suggesting that ampicillin treatment of the ∆recA strain induces higher levels of mutagenesis inside the cells, leading to the rapid rise of resistance mutations. However, as the authors note, the mutants enriched by ampicillin selection can play a role in efflux and can thus change a bacterium's sensitivity to a wide range of antibiotics, in what is known as cross-resistance. The current data is not clear on whether the elevated "mutagenesis" is driven by ampicillin selection or by a bona fide increase in mutation rate.

Furthermore, on a technical level, the authors employed WGS to identify resistance mutations in the ampicillin-treated wild-type and ∆recA strains. However, the WGS methodology described in the paper is inconsistent. Notably, wild-type WGS samples were picked from non-selective plates, while ΔrecA WGS isolates were picked from selective plates with 50 μg/mL ampicillin. Such an approach biases the frequency and identity of the mutations seen in the WGS and cannot be used to support the idea that ampicillin treatment induces higher levels of mutagenesis.

Finally, it is important to establish what the basal mutation rates of both the WT and ∆recA strains are. Currently, only the ampicillin-treated populations were reported. It is possible that the ∆recA strain has inherently higher mutagenesis than WT, with a larger subpopulation of resistant clones. Thus, ampicillin treatment might not, in fact, induce higher mutagenesis in ∆recA.

Summary of revised manuscript:

In their revisions, the authors have addressed my major concerns with additional experiments and changes to the text. Thank you!

Reviewer #3 (Public review):

Summary:

In the present work, Zhang et al investigate the involvement of the bacterial DNA damage repair SOS response in the evolution of beta-lactam drug resistance in Escherichia coli. Using a combination of microbiological, bacterial genetics, laboratory evolution, next-generation, and live-cell imaging approaches, the authors propose short-term (transient) drug resistance evolution can take place in RecA-deficient cells in an SOS response-independent manner. They propose the evolvability of drug resistance is alternatively driven by the oxidative stress imposed by accumulation of reactive oxygen species and compromised DNA repair. Overall, this is a nice study that addresses a growing and fundamental global health challenge (antimicrobial resistance).

Strengths:

The authors introduce new concepts to antimicrobial resistance evolution mechanisms. They show short-term exposure to beta-lactams can induce durably fixed antimicrobial resistance mutations. They propose this is due to compromised DNA repair and oxidative stress. Antibiotic resistance evolution under transient stress is poorly studied, so the authors' work is a nice mechanistic contribution to this field.

Weaknesses:

The authors revisions have significantly addressed weaknesses previously identified earlier in the review process.

Reviewer #1 (Public review):

Summary:

This paper shows that maternal high-fat diet during lactation changes microglia morphology in the PVN, potentially to acquire a more active state. Further, the authors reveal that PVN microglia engulf AgRP terminals in the PVN during postnatal development, a previously unrecognized behavior. A notable finding of this paper is that pharmacological reduction of microglial cells can reverse weight gain and terminal loss in the offspring under maternal high fat diet conditions, even though an increase in microglial engulfment of AgRP+ terminals was not observed, suggesting an alternative mechanism. The data support these findings, although questions remain regarding the efficacy and timing of the pharmacological microglial knockdown.

Strengths

(1) The impact of microglia on hypothalamic synaptic pruning is poorly characterized, and thus, the findings herein are especially of interest.

Weaknesses

(1) Most minor concerns were addressed during revisions, including additional details in the methods and results sections that help interpret the data as presented.

(2) The AgRP staining is unclear. For example, in Figure 2, the figure legend says "labeled AgRP terminals (red)" (Fig 2A-D) but then concludes no difference in the number of "AgRP neurons" (Fig 2J). Is this quantification of AgRP+ neurons, terminals, or both?

(3) The PLX experiments are critical to their conclusion that during lactation, microglia in the PVN sculpt AgRP inputs; however, there is no demonstration that PLX treatment effectively eliminated microglia during this postnatal window. Microglia depletion was only assessed at P55, a month past the PLX treatment window making it unclear when and by what percentage the microglia were eliminated.

Reviewer #2 (Public review):

Hypothalamic neural circuits that control body weight develop during the lactation period in rodents. Exposure to maternal high-fat diet during this period (MHFD-L) program has lasting effects on their neuroanatomical organization and function. Microglia sense environmental signals and can sculpt developing circuits by promoting or pruning synaptic connections. Here, the authors examine the contribution of microglia to the effects of MHFD-L to reduce projections from AgRP neurons in the ARH to the PVH, a critical node in circuits regulating energy balance. Using detailed histomorphometric analyses of Iba-1+ cells in the three brain regions (ARH, PVH, and BNST) at two time points (P16 and P30), the authors show that microglial volume and complexity increase, while cell numbers decrease across this period. Exposure to MHFD-L is associated with a transient increase in microglial complexity/volume at P16 in the PVH but not in the other brain regions or time points assessed. Depleting microglia using a pharmacological approach reversed effects of MHD-L on AgRP outgrowth and body weight.

Strengths:

(1) The Introduction is well-written and provides a good overview of what is known about the roles of microglia in sculpting developing circuits in the hippocampus and cortex. This provides a strong rationale for the current investigations in the hypothalamus.

(2) High-quality imaging and detailed 3-D reconstructions of Iba-1 staining in microglia are used to perform unbiased analyses of microglial complexity and to quantify the spatial relationship between microglial processes and AgRP terminals.

Weaknesses:

(1) The central claim of the manuscript is that microglia in the PVH sculpt the density of AgRP inputs to the PVH in a temporally and spatially restricted manner. While the findings of the microglial ablation experiment are consistent with this hypothesis, they do not prove causality, since their manipulations were not limited to the PVH. Further studies are needed to exclude the possibility that increased outgrowth from AgRP neurons results from direct actions in the ARH or indirect consequences of changes in growth rates.

(2) Impacts of microglial depletion were only assessed in adulthood. Given the hypothesized importance of differences in microglia at P16 and not at P30, it would be helpful to demonstrate that PLX5622 does indeed affect microglia at P16, when the circuit is most sensitive to maternal influences.

Reviewer #3 (Public review):

Summary:

The authors interrogated the putative role of microglia in determining AgRP fiber maturation in offspring exposed to a maternal high-fat diet. They found that changes in specific parts of the hypothalamus (but not in others) occur in microglia and that the effect of microglia on AgRP fibers appears to be beyond synaptic pruning, a classical function of these brain-resident macrophages.

Strengths:

The work is very strong in neuroanatomy. The images are clear and nicely convey the anatomical differences. The microglia depletion study adds functional relevance to the paper; however, the pitfalls of the technology regarding functional relevance should be discussed.

Weaknesses:

There was no attempt to functionally interrogate microglia in different parts of the hypothalamus. Morphology alone does not reflect a potential for significant signaling alterations that may occur within and between these and other cell types.

Comments on revised submission: My advice is to change the title by removing "required" and state what is interrogated and found in the paper. A more accurate title would be (for example): Implication of Microglia for Developmental Specification of AgRP Innervation in the Hypothalamus of Offspring Exposed to Maternal High-Fat Diet During Lactation.

I suggest that the authors discuss the limitations of their approach and findings, and propose future directions to address them

Reviewer #1 (Public review):

Summary:

In this manuscript, the authors used a leucine/pantothenate auxotrophic strain of Mtb to screen a library of FDA-approved compounds for their antimycobacterial activity and found significant antibacterial activity of the inhibitor semapimod. In addition to alterations in pathways, including amino acid and lipid metabolism and transcriptional machinery, the authors demonstrate that semapimod treatment targets leucine uptake in Mtb. The work presents an interesting connection between nutrient uptake and cell wall composition in mycobacteria.

Strengths:

(1) The link between the leucine uptake pathway and PDIM is interesting but has not been characterized mechanistically. The authors discuss that PDIM presents a barrier to the uptake of nutrients and shows binding of the drug with PpsB. However it is unclear why only the leucine uptake pathway was affected. We still do not know what PpsB actually does for amino acid uptake - is it a transporter? Does semapimod binding affect its activity? Does the auxotrophic Mtb have lower PDIM levels compared to wild-type Mtb?

(2) The authors show an interesting result where they observed antibacterial activity of semapimod against H37Rv only in vivo and not in vitro. Why do the authors think this is the basis of this observation? It is possible semapimod has an immunomodulatory effect on the host since leucine is an essential amino acid in mice. The authors could check pro-inflammatory cytokine levels in infected mouse lungs with and without drug treatment.

(3) The authors show that the semapimod-resistant auxotroph lacks PDIM. The conclusions would be further strengthened by including validations using PDIM mutants, including del-ppsB Mtb and other genes of the PDIM locus, whether in vivo this mutant would be more susceptible (or resistant) to semapimod treatment.

(4) Prolonged subculturing can introduce mutations in PDIM, which can be overcome by supplementing with propionate (Mullholland et al, Nat Microbiol, 2024). Did the authors also supplement their cultures with propionate? It would be interesting to see what mutations would result in Semr strains with propionate supplementation along with prolonged semapimod treatment.

Weaknesses:

I have summarized the limitations above in my comments. Overall, it would be helpful to provide more mechanistic details to study the connection between leucine uptake and PDIM.

Reviewer #2 (Public review):

Summary

This important study uncovers a novel mechanism for L-leucine uptake by M. tuberculosis and shows that targeting this pathway with 'Semapimod' interferes with bacterial metabolism and virulence. These results identify the leucine uptake pathway as a potential target to design new anti-tubercular therapy.

Strengths

The authors took numerous approaches to prove that L-leucine uptake of M. tuberculosis is an important physiological phenomenon and may be effectively targeted by 'Semapimod'. This study utilizes a series of experiments using a broad set of tools to justify how the leucine uptake pathway of M. tuberculosis may be targeted to design new anti-tubercular therapy.

Weaknesses

The study does not explain how L-leucine is taken up by M. tuberculosis, leaving the mechanism unclear. Even though 'Semapimod' binds to the PpsB protein, the relevant connection between changes in PDIM and amino acid transport remains incomplete. Also, the fact that the drug does not function on WT bacteria makes it a weak candidate to consider its usefulness for a therapeutic option.

Reviewer #3 (Public review):

Agarwal et al identified the small molecule semapimod from a chemical screen of repurposed drugs with specific antimycobacterial activity against a leucine-dependent strain of M. tuberculosis. To better understand the mechanism of action of this repurposed anti-inflammatory drug, the authors used RNA-seq to reveal a leucine-deficient transcriptomic signature from semapimod challenge. The authors then measured a decreased intracellular concentration of leucine after semapimod challenge, suggesting that semapimod disrupts leucine uptake as the primary mechanism of action. Unexpectedly, however, resistant mutants raised against semapimod had a mutation in the polyketide synthase gene ppsB that resulted in loss of PDIM synthesis. The authors believe growth inhibition is a consequence of decreased accumulation of leucine as a result of an impaired cell wall and a disrupted, unknown leucine transporter. This study highlights the importance of branched-chain amino acids for M. tuberculosis survival, and the chemical genetic interactions between semapimod and ppsB indicate that ppsB is a conditionally essential gene in a medium depleted of leucine.

The conclusions regarding the leucine and PDIM phenotypes are moderately supported by experimental data. The authors do not provide experimental evidence to support a specific link between leucine uptake and impaired PDIM production. Additional work is needed to support these claims and strengthen this mechanism of action.

(1) Since leucine uptake and PDIM synthesis are important concepts of the manuscript, experiments would benefit from exploring other BCAAs to know if the phenotypes observed are specific to leucine, and adding additional strains to the 2D TLC experiments to provide confidence in the absence of the PDIM band.

(2) The intriguing observation that wild-type H37Rv is resistant to semapimod but the leucine-auxotroph is sensitive should be further explored. If the authors are correct and semapimod does inhibit leucine uptake through a specific transporter or disrupted cell wall (PDIM synthesis), testing semapimod activity against the leucine-auxotroph in various concentrations of BCAAs could highlight the importance of intracellular leucine. H37Rv is still able to synthesize endogenous leucine and is able to circumvent the effect of semapimod.

Reviewer #1 (Public review):

Summary:

The manuscript finds a negative relationship between tuberculin skin test-induced type I interferon activity with chest X-ray tuberculosis severity in humans. This evidence is between incomplete and solid. It needs a bioinfomatics/transcriptomics reviewer to make a more insightful judgement. The manuscript demonstrates a convincing role for Stat2 in controlling Mycobacterium marinum infection in zebrafish embryos, incomplete data are presented linking reduced leukocyte recruitment to the infection susceptibility phenotype.

Strengths:

(1) An interesting analysis of TST response correlated with chest X-ray pathology.

(2) Novel data on a protective role for Stat2 in a natural host-mycobacterial species infection pairing.

Weaknesses:

(1) The transcriptional modules are very large sets of genes that do not present a clear picture of what is actually being measured relative to other biological pathways.

(2) The link between infection-Stat2-leukocyte recruitment and containment of infection is plausible, but lacks a specific link to the first part of the manuscript.

Major concerns

(1) Line 158: The two transcriptional modules should be placed in the context of other DEG patterns. The macrophage type I interferon module, in particular, is quite large (361 genes). Can this be made more granular in terms of type I IFN ligands and STAT2-dependent genes?

(2) The ifnphi1 injection into mxa:mCherry stat2 crispants is a nice experiment to demonstrate loss of type I IFN responsiveness. Further data is required to demonstrate if important mycobacterial control pathways (IFNy, TNF, il6?, etc) are intact in stat2 crispants before being able to conclude that these phenotypes are specific to type I IFN.

Reviewer #2 (Public review):

Summary:

This study shows that type I interferon (IFN-I) signaling helps protect against mycobacterial infection. Using human gene expression data and a zebrafish model, the authors find that reduced IFN-I activity is linked to more severe disease. They also show that zebrafish lacking the IFN-I signaling gene stat2 are more vulnerable to infection due to poor macrophage migration. These results suggest a protective role for IFN-I in mycobacterial disease, challenging previous findings from other animal models.

Strengths:

Strengths of the manuscript include the use of human clinical samples to support relevance to disease, along with a genetically tractable zebrafish model that enables mechanistic insight.

Weaknesses:

(1) The manuscript presents intriguing human data showing an inverse correlation between IFN-I gene signatures and TB disease, but the findings remain correlative and may be cohort-specific. Given that the skin is not a primary site of TB and is relatively immunotolerant, the biological relevance of downregulated IFN-I-related genes in this tissue to systemic or pulmonary TB is unclear.

(2) The reliance on stat2 CRISPants in zebrafish offers a limited view of IFN-I signaling. Including additional crispant lines targeting other key regulators (e.g., ifnar1, tyk2, irf3, irf7) would strengthen the interpretation and clarify whether the observed effects reflect broader IFN-I pathway disruption.

(3) The conclusion that IFN-I is protective contrasts with established findings from murine and non-human primate models, where IFN-I is often detrimental. While the authors highlight species differences, the lack of functional human data and reliance on M. marinum in zebrafish limit the translational relevance. A more balanced discussion addressing these discrepancies would improve the manuscript.

(4) Quantification of bacterial burden using fluorescence intensity alone may not accurately reflect bacterial viability. Complementary methods, such as qPCR for bacterial DNA, would provide a more robust assessment of antimicrobial activity.

(5) Finally, the authors should clarify whether impaired macrophage recruitment in stat2 crispants results from defects in chemotaxis, differentiation, or survival, and address discrepancies between their human blood findings and prior studies.

Reviewer #3 (Public review):

Summary:

In this manuscript, the authors presented an interesting study providing an insight into the role of Type-I interferon responses in tuberculosis (TB) pathogenesis by combining transcriptome analysis of PBMCs and TST from tuberculosis patients. The zebrafish model was used to identify the changes in the innate immune cell population of macrophages and neutrophils. The findings suggested that Type-I interferon signatures inversely correlated with disease severity in the TST transcriptome data. The authors validated the observations by CRISPR-mediated disruption of stat2 (a critical transcription factor for type I interferon signaling) in zebrafish larvae, showing increased susceptibility to M. marinum infection. Traditionally, type-I interferon responses have been viewed as detrimental in mycobacterial infections, with studies suggesting enhanced susceptibility in certain mouse models. The study tried to identify and further characterize the understanding of the role of type-I interferons in TB.

Strengths:

Traditionally, type-I interferon responses have been viewed as detrimental in mycobacterial infections, with studies suggesting enhanced susceptibility in certain mouse models. The study tried to further understand the role of type-I interferons in TB pathogenesis.

Weaknesses:

Though the study showed an inverse correlation of Type-I interferon with radiological features of TB, the molecular mechanism is largely unexplored in the study, which is making it difficult to understand the basis of the results shown in the manuscript by the authors.

Reviewer #1 (Public review):

Summary:

A fundamental technique for the identification of peptide-specific CD8 T cells is the use of fluorophore-conjugated and peptide loaded MHC tetramers. Classically, refolding of specific peptides with MHC monomers can be labour intensive, and not optimal for screening large numbers of different peptides. Hence, UV-exchanged tetramers have been developed to upscale this, however, still has some associated challenges such as UV-mediated damage to peptide complexes. Here, Pothast, C.R. et al demonstrate the efficacy of using temperature exchanged tetramers for the prevalent alleles HLA-A*03:01, A*11:01, B*07:02, and C*07:02. Building upon their previous work with HLA-A*02:01, H-2Kb, and HLA-E. They first demonstrate the complex stability of tetramers with different affinity peptides at high temperature, showing complex destabilisation can be rescued with higher affinity peptides. This is followed by an optimisation of peptide exchange temperatures, tailored for each allele. The authors then demonstrate successful binding to clonal T cell lines, and then a step further with viral peptides against PBMCs from individuals with confirmed infection history. For the latter they compare to conventional tetramers and demonstrate comparable signal.<br /> Due to the prevalence of these 4 alleles, the ease-of-handling, and short time requirements, these tetramers are likely to show high utility.

Strengths:

The manuscript is well-written and the results are solid, although more detail may add clarity to some of the results, in particular Figures 1 and 2. Other than the points reported below, the study uses accurate controls to demonstrate the specificity of the tetramers, and the data are convincing.

Overall, the interpretation of the results is accurate, and the discussion is thorough. Additional comments may be included to cover potential tetramer batch variability and differences in the stability of different alleles. Specifically, whether certain alleles require higher-affinity peptides to be stable, compared to others.

Weaknesses:

The authors demonstrate the equivalence of temperature-exchanged tetramers to conventional ones, however, as they are an advancement on UV-exchange, it would be useful to show data on how their stability, exchange efficacy, and binding to T cell lines compare to UV-based tetramers. It would be supportive to show that temperature does not impact fluorophore intensity as well.

Reviewer #2 (Public review):

Summary:

The majority of CD8+ T cell responses rely on the proper presentation of antigens through stable MHC-I (but not requiring a stable immunological synapse). This work highlights a new approach to build an array of stable peptide MHC-I using temperature exchange, which can be used to identify antigen-specific CD8+ T cells.

Strengths:

In this work, the authors have proposed an alternative method to reload the peptide MHC-I molecule. Their temperature-exchange approach is distinct from current reloadable peptide MHC technologies involving photolabile peptide, empty MHC-I (Nat Commun 11, 1314 (2020). https://doi.org/10.1038/s41467-020-14862-4), tapasin/TAPBPR chaperone-assisted (eLife 7:e40126.), enzyme exchangeable (WO2020226570) and small alcohol (Curr Res Immunol. 2022 Aug 18;3:167-174. doi: 10.1016/j.crimmu.2022.08.002) approaches.

Weaknesses:

However, the proposed temperature-exchange approach does not substantially improve the quality of antigen-specific T cells that can be identified using the photolabile peptide MHC-I molecules.

The time saved using the temperature-exchange protocol may not be a pull factor as the photolabile peptide MHC-I approach is not unreasonably laborious.

Reviewer #3 (Public review):

Summary:

The study by Pothast and colleagues outlines an extension of their previously described temperature-based MHC-I peptide exchange method on 4 common HLA alleles, to enable the generation of peptide/MCH-I tetramers for characterization of antigen-specific T cells by flow cytometry.

Strengths:

This work outlines a protocol for generating MHC-I tetramers on 4 common HLA allotypes, which can then be applied to monitor T cell responses by flow cytometry studies. The work provides conditional ligands for exchange on each HLA and demonstrates proof of concept studies using clonotypic T cells and CD8+ PBMCs.

The results support that the temperature-exchanged tetramers can perform similarly to conventional tetramers in some settings.

Weaknesses:

Given that there are several proposed methodologies addressing the same task (including UV-mediated, disulfide-bond based stabilization of empty MHC-I conformers, and chaperone-based methods), the relevance of the proposed temperature-mediated technology is questionable.

More specifically, important limitations of the study include:

(1) A lack of quantification of exchanged molecules relative to molecules that retain the original placeholder peptides, or completely empty molecules present in the same sample.

(2) A lack of validation that peptide exchange has occurred in the absence of a reporter T cell line appears to be a significant limitation of the methodology for antigen / T cell discovery.

(3) The sub-optimal exchange efficiency relative to conventional prepared pMHC-I molecules, shown in Figure 4, is a significant limitation of the approach.

(4) There are no data to support that exchange proceeds through the generation of empty molecules during the temperature cycle, or by peptide binding on empty molecules that are already present in the sample. Understanding the mechanism of exchange is important for the necessary improvements to the methodology.

(5) It is possible that the temperature cycle causes protein aggregation or other irreversible changes to the sample - this should be explicitly quantified and addressed in the paper, since misfolded MHC-I molecules can lead to high levels of background staining.

(6) These potential limitations should limit detection of low-affinity/low-avidity interactions between TCRs and their cognate pMHC antigens - this should be addressed explicitly in a model antigen setting.

(7) The approach appears to be limited to the HLAs showing high thermal stability, which have been explored in this study. However, a large fraction of HLAs show sub-optimal thermal stabilities. It seems that explicit validation of peptide exchange would be required for any new HLA allele introduced into this process.

(8) Whether the approach can be used to load suboptimal peptides with lower thermal stabilities that are emerging immunotherapy targets is not addressed in the present study.

Because of these limitations, the present manuscript does not conclusively support the claim that temperature-based exchange can be used as a robust methodology to generate pMHC-I tetramers with desired peptide specificities.

As a result, the scope of applications using these suboptimal exchanged pHLA tetramers is limited, and should be addressed with further improvements of the methodology, including better characterization of exchange efficiency, demonstration of functionality across a broader range of HLA allotypes with varying thermal stability profiles, and validation with clinically relevant low-affinity peptides that would strengthen the potential utility of this approach in immunotherapy development and basic T cell biology research.

Reviewer #1 (Public review):

Summary:

This study focuses on the bacterial metabolite TMA, generated from dietary choline. These authors and others have previously generated foundational knowledge about the TMA metabolite TMAO, and its role in metabolic disease. This study extends those findings to test whether TMAO's precursor, TMA, and its receptor TAAR5 are also involved and necessary for some of these metabolic phenotypes. They find that mice lacking the host TMA receptor (Taar5-/-) have altered circadian rhythms in gene expression, metabolic hormones, gut microbiome composition, and olfactory and innate behavior. In parallel, mice lacking bacterial TMA production or host TMA oxidation have altered circadian rhythms.

Strengths:

These authors use state-of-the-art bacterial and murine genetics to dissect the roles of TMA, TMAO, and their receptor in various metabolic outcomes (primarily measuring plasma and tissue cytokine/gene expression). They also follow a unique and unexpected behavioral/olfactory phenotype. Statistics are impeccable.

Weaknesses:

Enthusiasm for the manuscript is dampened by some ambiguous writing and the presentation of ideas in the introduction, both of which could easily be improved upon revision.

Reviewer #2 (Public review):

Summary:

In the manuscript by Mahen et al., entitled "Gut Microbe-Derived Trimethylamine Shapes Circadian Rhythms Through the Host Receptor TAAR5," the authors investigate the interplay between a host G protein-coupled receptor (TAAR5), the gut microbiota-derived metabolite trimethylamine (TMA), and the host circadian system. Using a combination of genetically engineered mouse and bacterial models, the study demonstrates a link between microbial signaling and circadian regulation, particularly through effects observed in the olfactory system. Overall, this manuscript presents a novel and valuable contribution to our understanding of host-microbe interactions and circadian biology. However, several sections would benefit from improved clarity, organization, and mechanistic depth to fully support the authors' conclusions.

Strengths:

(1) The manuscript addresses an important and timely topic in host-microbe communication and circadian biology.

(2) The studies employ multiple complementary models, e.g., Taar5 knockout mice, microbial mutants, which enhance the depth of the investigation.

(3) The integration of behavioral, hormonal, microbial, and transcript-level data provides a multifaceted view of the observed phenotype.

(4) The identification of olfactory-linked circadian changes in the context of gut microbes adds a novel perspective to the field.

Weaknesses:

While the manuscript presents compelling data, several weaknesses limit the clarity and strength of the conclusions.

(1) The presentation of hormonal, cytokine, behavioral, and microbiome data would benefit from clearer organization, more detailed descriptions, and functional grouping to aid interpretation.

(2) Some transitions-particularly from behavioral to microbiome data-are abrupt and would benefit from better contextual framing.

(3) The microbial rhythmicity analyses lack detail on methods and visualization, and the sequencing metadata (e.g., sample type, sex, method) are not clearly stated.

(4) Several figures are difficult to interpret due to dense layouts or vague legends, and key metabolites and gene expression comparisons are either underexplained or not consistently assessed across models.

(5) Finally, while the authors suggest a causal role for TAAR5 and its ligand in circadian regulation, the current data remain correlative; mechanistic experiments or stronger disclaimers are needed to support these claims.

Reviewer #3 (Public review):

Summary:

Deletion of the TMA-sensor TAAR5 results in circadian alterations in gene expression, particularly in the olfactory bulb, plasma hormones, and neurobehaviors.

Strengths:

Genetic background was rigorously controlled.

Comprehensive characterization.

Weaknesses:

The weaknesses identified by this reviewer are minor.

Overall, the studies are very nicely done. However, despite careful experimentation, I note that even the controls vary considerably in their gene expression, etc, across time (eg, compare control graphs for Cry 1 in IB, 4B). It makes me wonder how inherently noisy these measurements are. While I think that the overall point that the Taar5 KO shows circadian changes is robust, future studies to dissect which changes are reproducible over the noise would be helpful.

Impact:

These data add to the growing literature pointing to a role for the TMA/TMAO pathway in olfaction and neurobehavioral.

Reviewer #1 (Public review):

Summary:

This manuscript analyses primarily the effects of deleting the TgfbR1 and TgfbR2 receptors from endothelial cells at postnatal stages of vascular development and blood-retina barrier maturation in the retina. The authors find that deletion of these receptors affects vascular development in the retina, but importantly, it affects the infiltration of immune cells across the vessels in the retina. The findings demonstrate that Tgfb signaling through TgfbR1/R2 heterodimers regulates primarily the immune phenotypes of endothelial cells in addition to regulating vascular development. The data provided by the authors provide a solid support for their conclusions.

Strengths:

(1) The manuscript uses a variety of elegant genetic studies in mice to analyze the role of TgfbR1 and TgfbR2 receptors in endothelial cells at postnatal stages of vascular development and blood-retina barrier maturation in the retina.

(2) The authors provide a nice comparison of the vascular phenotypes in endothelial-specific knockout of TgfbR1 and TgfbR2 in the retina (and to a lesser degree in the brain) with those from Npd KO mice (loss of Ndp/Fzd signaling) or loss of VEGF-A signaling to dissect the specific roles of Tgf signaling for vascular development in the retina.

(3) The snRNAseq data of vessel segments from the brains of WT versus TgfbR1 -iECKO mice provides a nice analysis of pathways and transcripts that are regulated by Tgfb signaling in endothelial cells.

Weaknesses:

(1) The authors claim that choroidal neovascular tuft phenotypes are similar in TgfbrR1 KO and TgfbrR2 KO mice. However, the phenotypes look more severe in the TgfbrR1 KO rather than TgfbrR2 KO mice. Can the authors show a quantitative comparison of the number of choroidal neovascular tufts per whole eye cross-section in both genotypes?

(2) In the analysis of Sulfo-NHS-Biotin leakage in the retina to assess blood-retina barrier maturation. The authors claim that there is increased vascular leakage in the TgfbR1 KO mice. However, it does not seem like Sulfo-NHS-biotin is leaking outside the vessels. Therefore, it cannot be increased vascular permeability. Can the authors provide a detailed quantification of the leakage phenotype?

(3) The immune cell phenotyping by snRNAseq is premature, as the number of cells is very small. The authors should sort for CD45+ cells and perform single-cell RNA sequencing.

(4) The analysis of BBB leakage phenotype in TgfbR1 KO mice needs to be more detailed and include tracers as well as serum IgG leakage.

(5) A previous study (Zarkada et al., 2021, Developmental Cell) showed that EC-deletion of Alk5 affects the D tip cells. The phenotypes of those mice look very similar to those shown for TgfbrR1 KO mice. Are D-tip cells lost in these mutants by snRNAseq?

Reviewer #2 (Public review):

Summary:

The authors meticulously characterized EC-specific Tgfbr1, Tgfbr2, or double knockout in the retina, demonstrating through convincing immunostaining data that loss of TGF-β signaling disrupts retinal angiogenesis and choroidal neovascularization. Compared to other genetic models (Fzd4 KO, Ndp KO, VEGF KO), the Tgfbr1/2 KO retina exhibits the most severe immune cell infiltration. The authors proposed that TGF-β signaling loss triggers vascular inflammation, attracting immune cells - a phenotype specific to CNS vasculature, as non-CNS organs remain unaffected.

Strengths:

The immunostaining results presented are clear and robust. The authors performed well-controlled analyses against relevant mouse models. snRNA-seq corroborates immune cell leakage in the retina and vascular inflammation in the brain.

Weaknesses:

The causal link between TGF-β loss, vascular inflammation, and immune infiltration remains unresolved. The authors' model posits that EC-specific TGF-β loss directly causes inflammation, which recruits immune cells. However, an alternative explanation is plausible: Tgfbr1/2 KO-induced developmental defects (e.g., leaky vessels) permit immune extravasation, subsequently triggering inflammation. The observations that vein-specific upregulation of ICAM1 staining and the lack of immune infiltration phenotypes in the non-CNS tissues support the alternative model. Late-stage induction of Tgfbr1/2 KO (avoiding developmental confounders) could clarify TGF-β's role in retinal angiogenesis versus anti-inflammation.

Reviewer #1 (Public review):

Summary:

This paper examines how geometric regularities in abstract shapes (e.g., parallelograms, kites) are perceived and processed in the human brain. The manuscript contains multimodal data (behavior, fMRI, MEG) from adults and additional fMRI data from 6-year-old children. The key findings show that (1) processing geometric shapes lead to reduced activity in ventral areas in comparison to complex stimuli and increased activity in intraparietal and inferior temporal regions, (2) the degree of geometric regularity modulates activity in intraparietal and inferior temporal regions, (3) similarity in neural representation of geometric shapes can be captured early by using CNN models and later by models of geometric regularity. In addition to these novel findings, the paper also includes a replication of behavioral data, showing that the perceptual similarity structure amongst the geometric stimuli used can be explained by a combination of visual similarities (as indexed by a feedforward CNN model of the ventral visual pathway) and geometric features.

Strengths:

(1) The study incorporates multi-modal data that uses more than one task and different populations of participants (adults and children).

(2) It replicates behavioral findings of an earlier study in a larger cohort.

(3) The paper comes with openly accessible code in a well-documented GitHub repository, and the data will be published with the paper on OpenNeuro.

Weaknesses:

I wonder how task difficulty and linguistic labels interact with the current findings. Based on the behavioral data, shapes with more geometric regularities are easier to detect when surrounded by other shapes. Do shape labels that are readily available (e.g., "square") help in making accurate and speedy decisions? Can the sensitivity to geometric regularity in intraparietal and inferior temporal regions be attributed to differences in task difficulty? Similarly, are the MEG oddball detection effects that are modulated by geometric regularity also affected by task difficulty?

Reviewer #2 (Public review):

Summary:

The current study seeks to understand the neural mechanisms underlying geometric reasoning. Using fMRI with both children and adults, the authors found that contrasting simple geometric shapes with naturalistic images (faces, tools, houses) led to responses in the dorsal visual stream, rather than ventral regions that are generally thought to represent shape properties. The authors followed up on this result using computational modeling and MEG to show that geometric properties explain distinct variance in the neural response beyond what is captured by a CNN.

Strengths:

These findings contribute much-needed neural and developmental data to the ongoing debate regarding shape processing in the brain and offer additional insights into why CNNs may have difficulty with shape processing. The motivation and discussion for the study are appropriately measured, and I appreciate the authors' use of multiple populations, neuroimaging modalities, and computational models to explore this question.

Weaknesses:

Given that the primary take away from this study is that geometric shape information is found in the dorsal stream, rather than the ventral stream there is very little there is very little discussion of prior work in this area (for reviews, see Freud et al., 2016; Orban, 2011; Xu, 2018). Indeed, there is extensive evidence of shape processing in the dorsal pathway in human adults (Freud, Culham, et al., 2017; Konen & Kastner, 2008; Romei et al., 2011), children (Freud et al., 2019), patients (Freud, Ganel, et al., 2017), and monkeys (Janssen et al., 2008; Sereno & Maunsell, 1998; Van Dromme et al., 2016), as well as the similarity between models and dorsal shape representations (Ayzenberg & Behrmann, 2022; Han & Sereno, 2022).

The presence of activation in aIPS led the authors to interpret their results to mean that geometric reasoning draws on the same processes as mathematical thinking. However, there is not enough evidence in the current study to support this claim.

Reviewer #3 (Public review):

Summary:

The authors report converging evidence from several brain-imaging techniques that geometric figures, notably quadrilaterals, are processed differently in visual (lower activation) and spatial (greater) areas of the human brain than representative figures. Comparison of mathematical models to fit activity for geometric figures shows the best fit for abstract geometric features like parallelism and symmetry. The brain areas active for geometric figures are also active in processing mathematical concepts, even in blind mathematicians, linking geometric shapes to abstract math concepts. The effects are stronger in adults than in 6-year-old Western children. Similar phenomena do not appear in great apes, suggesting that this is uniquely human and developmental.

Strengths:

Multiple converging techniques of brain imaging and testing of mathematical models. Careful reasoning at every step of research and presentation of research, anticipating and addressing possible reservations. Connecting these findings to other findings, brain, behavior, and historical/anthropological, to suggest broad and important fundamental connections between abstract visual-spatial forms and mathematical reasoning, further suggesting visual-spatial origins of mathematical reasoning.

Weaknesses:

Perhaps the manuscript could emphasize that the areas recruited by geometric figures but not objects are spatial, with reduced processing in visual areas. It also seems important to say that the images of real objects are interpreted as representations of 3D objects, as they activate the same visual areas as real objects. By contrast, the images of geometric forms are not interpreted as representations of real objects but rather perhaps as 2D abstractions. The authors use the term "symbolic." That use of that term could usefully be expanded here.

Pigeons have remarkable visual systems. According to my fallible memory, Herrnstein investigated visual categories in pigeons. They can recognize individual people from fragments of photos, among other feats. I believe pigeons failed at geometric figures and also at cartoon drawings of things they could recognize in photos. This suggests they did not interpret line drawings of objects as representations of objects.

Categories are established in part by contrast categories; are quadrilaterals, triangles, and circles different categories?

It would be instructive to investigate stimuli that are on a continuum from representational to geometric, e.g., table tops or cartons under various projections, or balls or buildings that are rectangular or triangular. Building parts, inside and out. like corners. Objects differ from geometric forms in many ways: 3D rather than 2D, more complicated shapes, and internal texture. The geometric figures used are flat, 2-D, but much geometry is 3-D (e. g. cubes) with similar abstract features. The feature space of geometry is more than parallelism and symmetry; angles are important, for example. Listing and testing features would be fascinating. Similarly, looking at younger or preferably non-Western children, as Western children are exposed to shapes in play at early ages.

What in human experience but not the experience of close primates would drive the abstraction of these geometric properties? It's easy to make a case for elaborate brain processes for recognizing and distinguishing things in the world, shared by many species, but the case for brain areas sensitive to processing geometric figures is harder. The fact that these areas are active in blind mathematicians and that they are parietal areas suggests that what is important is spatial far more than visual. Could these geometric figures and their abstract properties be connected in some way to behavior, perhaps with fabrication and construction as well as use? Or with other interactions with complex objects and environments where symmetry and parallelism (and angles and curvature--and weight and size) would be important? Manual dexterity and fabrication also distinguish humans from great apes (quantitatively, not qualitatively), and action drives both visual and spatial representations of objects and spaces in the brain. I certainly wouldn't expect the authors to add research to this already packed paper, but raising some of the conceptual issues would contribute to the significance of the paper.

Reviewer #1 (Public review):

Lipid transfer proteins (LTPs) play a crucial role in the intramembrane lipid exchange within cells. However, the molecular mechanisms that govern this activity remain largely unclear. Specifically, the way in which LTPs surmount the energy barrier to extract a single lipid molecule from a lipid bilayer is not yet fully understood. This manuscript investigates the influence of membrane properties on the binding of Ups1 to the membrane and the transfer of phosphatidic acid (PA) by the LTP. The findings reveal that Ups1 shows a preference for binding to membranes with positive curvature. Moreover, coarse-grained molecular dynamics simulations indicate that positive curvature decreases the energy barrier associated with PA extraction from the membrane. Additionally, lipid transfer assays conducted with purified proteins and liposomes in vitro demonstrate that the size of the donor membrane significantly impacts lipid transfer efficiency by Ups1-Mdm35 complexes, with smaller liposomes (characterized by high positive curvature) promoting rapid lipid transfer.

This study offers significant new insights into the reaction cycle of phosphatidic acid (PA) transfer by Ups1 in mitochondria. Notably, the authors present compelling evidence that, alongside negatively charged phospholipids, positive membrane curvature enhances lipid transfer - an effect that is particularly relevant at the mitochondrial outer membrane. The experiments are technically robust, and my primary feedback pertains to the interpretation of specific results.

(1) The authors conclude from the lipid transfer assays (Figure 5) that lipid extraction is the rate-limiting step in the transfer cycle. While this conclusion seems plausible, it should be noted that the authors employed high concentrations of Ups1-Mdm35 along with less negatively charged phospholipids in these reactions. This combination may lead to binding becoming the rate-limiting factor. The authors should take this point into consideration. In this type of assay, it is challenging to clearly distinguish between binding, lipid extraction, and membrane dissociation as separate processes.

(2) The authors should discuss that variations in the size of liposomes will also affect the distance between them at a constant concentration, which may affect the rate of lipid transfer. Therefore, the authors should determine the average size and size distribution of liposomes after sonication (by DLS or nanoparticle analyzer, etc.).

(3) The authors use NBD-PA in the lipid transfer assays. Does the size of the donor liposomes affect the transfer of NBD-PA and DOPA similarly? Since NBD-labeled lipids are somewhat unstable within lipid bilayers (as shown by spontaneous desorption in Figure 5B), monitoring the transfer of unlabeled PA in at least one setting would strengthen the conclusion of the swap experiments.

(4) The present study suggests that membrane domains with positive curvature at the outer membrane may serve as starting points for lipid transport by Ups1-Mdm35. Is anything known about the mechanisms that form such structures? This should be discussed in the text.

Reviewer #2 (Public review):

Summary:

Lipid transfer between membranes is essential for lipid biosynthesis across different organelle membranes. Ups1-Mdm35 is one of the best-characterized lipid transfer proteins, responsible for transferring phosphatidic acid (PA) between the mitochondrial outer membrane (OM) and inner membrane (IM), a process critical for cardiolipin (CL) synthesis in the IM. Upon dissociation from Mdm35, Ups1 binds to the intermembrane space (IMS) surface of the OM, extracts a PA molecule, re-associates with Mdm35, and moves through the aqueous IMS to deliver PA to the IM. Here, the authors analyzed the early steps of this PA transfer - membrane binding and PA extraction - using a combination of in vitro biochemical assays with lipid liposomes and purified Ups1-Mdm35 to measure liposome binding, lipid transfer between liposomes, and lipid extraction from liposomes. The authors found that membrane curvature, a previously overlooked property of the membrane, significantly affects PA extraction but not PA insertion into liposomes. These findings were further supported by MD simulations.

Strengths:

The experiments are well-designed, and the data are logically interpreted. The present study provides an important basis for understanding the mechanism of lipid transfer between membranes.　

Weaknesses:

The physiological relevance of membrane curvature in lipid extraction and transfer still remains open.

Reviewer #3 (Public review):

The manuscript by Sadeqi et al. studies the interactions between the mitochondrial protein Ups1 and reconstituted membranes. The authors apply synthetic liposomal vesicles to investigate the role of pH, curvature, and charge on the binding of Ups1 to membranes and its ability to extract PA from them. The manuscript is well written and structured. With minor exceptions, the authors provide all relevant information (see minor points below) and reference the appropriate literature in their introduction. The underlying question of how the energy barrier for lipid extraction from membranes is overcome by Ups1 is interesting, and the data presented by the authors could offer a valuable new perspective on this process. It is also certainly a challenging in vitro reconstitution experiment, as the authors aim to disentangle individual membrane properties (e.g., curvature, charge, and packing density) to study protein adsorption and lipid transfer. I have one major suggestion and a few minor ones that the authors might want to consider to improve their manuscript and data interpretation:

Major Comments:

The experiments are performed with reconstituted vesicles, which are incubated with recombinant protein variants and quantitatively assessed in flotation and pelleting assays. According to the Materials and Methods section, the lipid concentration in these assays is kept constant at 5 µM. However, the authors change the size of the vesicles to tune their curvature. Using the same lipid concentration but varying vesicle sizes results in different total vesicle concentrations. Moreover, larger vesicles (produced by freeze-thawing and extrusion) tend to form a higher proportion of multilamellar vesicles, thus also altering the total membrane area available for binding. Could these differences in the experimental system account for the variation in binding? To address this, the authors would need to perform the experiments either under saturation (excess protein) conditions or find an experimental approach to normalize for these differences.

Reviewer #1 (Public review):

Summary:

The nuclear protein SATB1 was originally identified as a protein of the 'nuclear matrix', an aggregate of nuclear components that arose upon extracting nuclei with high salt. While the protein was assumed to have a global function in chromatin organization, it has subsequently been linked to a variety of pathological conditions, notably cancer. The mapping of the factor by conventional ChIP procedures showed strong enrichment in active, accessible chromatin, suggesting a direct role in gene regulation, perhaps in enhancer-promoter communication. These findings did not explain why SATB1-chromatin interaction resisted the 2 M salt extraction during early biochemical fractionation of nuclei.

The authors, who have studied SATB1 for many years, now developed an unusual variation of the ChIP procedure, in which they purify crosslinked chromatin by centrifugation through 8 M urea. Remarkably, while they lose all previously mapped signals for SATB1 in active chromatin, they now gain many binding events in silent regions of the genome, represented by lamin-associated domains (LADs).

SATB1 had previously been shown by the authors and others to bind to DNA with special properties, termed BUR for 'base-unpairing regions'). BURs are AT-rich and apparently enriched in equally AT-rich LADs. The 'urea-ChIP' pattern is essentially complementary to the classical ChIP pattern. The authors now speculate that the previously known SATB1 binding pattern determined by standard ChIP, which does not overlap BURs particularly well, is due to indirect chromatin binding, whereas they consider the urea-ChIP profile, which fits better to the BUR distribution on the chromosome, to be due to direct binding.

Building on the success with urea-ChIP the authors adapted the 4C-procedure of chromosome conformation mapping to work with urea-purified chromatin. The data suggest a model according to which BUR-bound SATB1 mediates long-distance interaction between active loci and some kind of scaffold structure formed by SATB1. Because cell type-specific differences are observed, they suggest that the SATB1 interactions are functionally relevant.

Strengths:

Given the unusual findings of essentially mutually exclusive 'standard ChIP' and 'urea-ChIP' profiles, the authors conducted many appropriate controls. They showed that all SATB1 peaks in urea-ChIP and 96% of peaks in standard-ChIP represent true signals, as they are not observed in a SATB1 knockout cell line. They also show that the urea-ChIP and standard ChIP yield similar profiles for CTCF and polycomb complex subunits. The data appear reproducible judged by at least two replicates and triangulation. The SATB1 KO cells provide a nice control for the specificity of signals, including those that arise from their elaborately modified 4C protocol.

In their revised manuscript the authors provide relevant background information concerning the effect of urea on the denaturation of macromolecules. Importantly, they argue convincingly that urea does not denature DNA under their conditions.

Weaknesses:

Despite the authors' efforts to explain their findings along with a lot of background information, some readers may be left confused due to the complexity of the system. BURs are found enriched in LADs, but are also present in active chromatin. SATB1 binds a subset of BURs, but the reason for discrimination remains unclear. SATB1 appears to bind chromatin in at least two modes with differing diffusion properties and exactly how this relates to the indirect and direct chromatin binding modes is mechanistically unclear.

The authors resort to the term 'SATB1-enriched subnuclear structure' to describe the profile gained through denaturing ChIP, thus avoiding strong statements about involvement of known nuclear structures (such as LADs or heterochromatin) and about functional implications.

The authors acknowledge a potential for RNA to be involved in modulating SATB1 interactions with chromatin, but leave this for future investigation.

Comment on revised version:

The authors revised their manuscript to my satisfaction.

Reviewer #2 (Public review):

Summary:

This study describes the key observation that SATB1 binds directly to so-called BUR elements. This is in contrast to several other reports describing SATB1 binding to promoters and enhancers. This discrepancy is explained by the authors to depend on the features of the ChIP technique being used. Urea-ChIP, innovated by the authors, strips off protein-protein interactions that compound conventional ChIP methods. The authors convincingly make the case that SATB1 and a key genome organiser, CTCF, largely bind different sites, as particularly evident in Figure 2A. In contrast, standard ChIP shows considerable overlap between their sites (Figure 2-figure supplement 1). The report documents convincingly that SATB1 partitions the genome independent of so-called TADs to influence expression patterns. SATB1 controls long-range interactions in thymocytes, and knock down of SATB1 does not affect the TAD patterns.

Strengths:

A new and innovative adaptation of ChIP-seq (urea ChIP-seq) has enabled the authors to successfully question existing data on the patterns of SATB1 binding to the genome. The authors provide a wealth of data to reinforce their claims. This report thus rectifies misconceptions about SATB1 function, which is particularly important given its role in metastasising cancer cells.

Weaknesses:

None

Reviewer #1 (Public review):

Summary:

This work studies representations in a network with one recurrent layer and one output layer that needs to path-integrate so that its position can be accurately decoded from its output. To formalise this problem, the authors define a cost function consisting of the decoding error and a regularisation term. They specify a decoding procedure that, at a given time, averages the output unit center locations, weighted by the activity of the unit at that time. The network is initialised without position information, and only receives a velocity signal (and a context signal to index the environment) at each timestep, so to achieve low decoding error it needs to infer its position and keep it updated with respect to its velocity by path integration.

The authors take the trained network and let it explore a series of environments with different geometries while collecting unit activities to probe learned representations. They find localised responses in the output units (resembling place fields) and border responses in the recurrent units. Across environments, the output units show global remapping and the recurrent units show rate remapping. Stretching the environment generally produces stretched responses in output and recurrent units. Ratemaps remain stable within environments and stabilise after noise injection. Low-dimensional projections of the recurrent population activity forms environment-specific clusters that reflect the environment's geometry, which suggests independent rather than generalised representations. Finally, the authors discover that the centers of the output unit ratemaps cluster together on a triangular lattice (like the receptive fields of a single grid cell), and find significant clustering of place cell centers in empirical data as well.

The model setup and simulations are clearly described, and are an interesting exploration of the consequences of a particular set of training requirements - here: path integration and decodability. But it is not obvious to what extent the modelling choices are a realistic reflection of how the brain solves navigation. Therefore, it is not clear whether the results generalize beyond the specifics of the setup here.

Strengths:

The authors introduce a very minimal set of model requirements, assumptions, and constraints. In that sense, the model can function as a useful 'baseline', that shows how spatial representations and remapping properties can emerge from the requirement of path integration and decodability alone. Moreover, the authors use the same formalism to relate their setup to existing spatial navigation models, which is informative.

The global remapping that the authors show is convincing and well-supported by their analyses. The geometric manipulations and the resulting stretching of place responses, without additional training, are interesting. They seem to suggest that the recurrent network may scale the velocity input by the environment dimensions so that the exact same path integrator-output mappings remain valid (but maybe there are other mechanisms too that achieve the same).

The simulations and analyses in the appendices serve as insightful controls for the main results.

The clustering of place cell peaks on a triangular lattice is intriguing, given there is no grid cell input. It could have something to do with the fact that a triangular lattice provides optimal coverage of 2d space? The included comparison with empirical data is valuable as a first exploration, showing a promising example, but doesn't robustly support the modelling results.

Weaknesses:

The navigation problem that needs to be solved by the model is a bit of an odd one. Without any initial position information, the network needs to figure out where it is, and then path-integrate with respect to a velocity signal. As the authors remark in Methods 4.2, without additional input, the only way to infer location is from border interactions. It is like navigating in absolute darkness. Therefore, it seems likely that the salient wall representations found in the recurrent units are just a consequence of the specific navigation task here; it is unclear if the same would apply in natural navigation. In natural navigation, there are many more sensory cues that help inferring location, most importantly vision, but also smell and whiskers/touch (which provides a more direct wall interaction; here, wall interactions are indirect by constraining velocity vectors). There is a similar but weaker concern about whether the (place cell like) localised firing fields of the output units are a direct consequence of the decoding procedure that only considers activity center locations.

The conclusion that 'representations are attractive' (heading of section 2) is not entirely supported. The authors show 'attractor-like behaviour' within a single context, but there could be alternative explanations for the recovery of stable ratemaps after noise injection. For example, the noise injection could scramble the network's currently inferred position, so that it would need to re-infer its position from boundary interactions along the trajectory. In that case the stabilisation would be driven by the input, not just internal attractor dynamics. Indeed, the useful control analysis in Appendix D suggests such a mechanism: without a velocity signal, only for small noise injections the network returns to a high correlation state. Correlated representations are recovered for larger noise injections due to the same mechanism that allow the network to determine its position upon from an uninformative initial hidden state upon entering a new environment, i.e. boundary interactions.

The authors report empirical data that shows clustering of place cell centers like they find for their output units. They report that 'there appears to be a tendency for the clusters to arrange in hexagonal fashion, similar to our computational findings'. This is an interesting observation on the distribution of place field centres which seems justified based on the example animal shown, but not across the population of animals included.