Reviewer #1 (Public review):

Summary:

This noteworthy paper examines the role of planar cell polarity and Wnt signalling in the body axis formation of the hydrozoan Clytia. In contrast to the freshwater polyp Hydra or the sea anemone Nematostella, Clytia represents a cnidarian model system with a complete life cycle (planula-polyp-medusa). In this species, classical experiments have demonstrated that a global polarity is established from the oral end of the embryos (Freeman, 1981). Prior research has demonstrated that Wnt3 plays a role in the formation of the oral organiser in Clytia and other cnidarians, acting in an autocatalytic feedback loop with β-catenin. However, the question of whether and to what extent an oral-aboral gradient of Wnt activity is established remained unanswered. This gradient is thought to control both tissue differentiation and tissue polarity. The planar cell polarity (PCP) pathway has been linked to this polarity, although it is generally considered to be β-catenin independent.

The authors have conducted a series of sophisticated experiments utilising morpholinos, mRNA microinjection, and immunofluorescent visualisation of PCP. The objective of these experiments was to address the function of Wnt3, β-catenin, and PCP core proteins in the coordination of the global polarity of Clytia embryos. The authors conclude that PCP plays a role in regulating polarity along the oral-aboral axis of embryos and larvae. This offers a conceivable explanation for how polarity information is established and distributed globally during Clytia embryogenesis, with implications for our understanding of axis formation in cnidarians and the evolution of Wnt signalling in general. While the experiments are well-designed and executed, there are some criticisms, questions, or suggestions that should be addressed.

Comments:

Beautiful and solid experiments to clarify the role of canonical Wnt signalling and PCP core factors in coordinating planar cell polarity. However, there are also several points that should be addressed.

(1) Wnt3 cue and global PCP. PCP has been described in detail in a previous paper on Clytia (Momose et al, 2012): its orientation along the oral-aboral body axis (ciliary basal body positioning studies), and its function in directional polarity during gastrulation (Stbm-, Fz1-, and Dsh-MO experiments). I wonder if this part could be shortened. What is new, however, are the knockdown and Wnt3-mRNA rescue experiments, which provide a deeper insight into the link between Wnt3 function in the blastopore organiser as a source or cue for axis formation. These experiments demonstrate that the Wnt3 knockdown induces defects equivalent to PCP factor knockdown, but can be rescued by Wnt3-mRNA injection, even at a distance of 200 µm away from the Wnt-positive area. The experimental set-up of these new molecular experiments follows in important aspects those of Freeman's experiments of 1981 (who in turn was motivated to re-examine Teissier's work of 1931/1933 ...). Freeman did not use the term "global polarity" but the concept of an axis-inducing source and a long-range tissue polarity can be traced back to both researchers.

(2) PCP propagation and β-catenin. The central but unanswered question in this study focuses on the interaction between Wnt3 and PCP and the propagation of PCP. Wnt3 has been described in cnidarians but also in vertebrates and insects as a canonical Wnt interacting with β-catenin in an autocatalytic loop. The surprising result of this study is that the action of Wnt3 on PCP orientation is not inhibited in the presence of a dominant-negative form of CheTCF (dnTCF) ruling out a potential function of β-catenin in PCP. This was supported by studies with constitutively active β-catenin (CA-β-cat) mRNA which was unable to restore PCP coordination nor elongation of Wnt3-depleted embryos but did restore β-catenin-dependent gastrulation. Based on these data, the authors conclude that Wnt3 has two independent roles: Wnt/β-catenin activation and initial PCP orientation (two-step model for PCP formation). However, the molecular basis for the interaction of Wnt3 with the PCP machinery and how the specificity of Wnt3 for both pathways is regulated at the level of Wnt-receiving cells (Fz-Dsh) remain unresolved. Also, with respect to PCP propagation, there is no answer with respect to the underlying mechanisms. The authors found that PCP components are expressed in the mid-blastula stage, but without any further indication of how the signal might be propagated, e.g., by a wavefront of local cell alignment. Here, it is necessary to address the underlying possible cellular interactions more explicitly.

(3) The proposed two-step model for PCP formation has important evolutionary implications in that it excludes the current alternate model according to which a long-range Wnt3-gradient orients PCP ("Wnt/β-catenin-first"). Nevertheless, the initial PCP orientation by Wnt3 - as proposed in the two-step model - is not explained at all on the molecular level. Another possible, but less well-discussed and studied option for linking Wnt3 with PCP action could be the role of other Wnt pathways. The authors present compelling evidence that Wnt3 is the most highly expressed Wnt in Clytia at all stages of development. The authors convincingly show that Wnt3 is the most highly expressed Wnt in Clytia at all stages of development (Figure S1). However, Wnt7 is also more highly expressed, which makes it a candidate for signal transduction from canonical Wnts to PCP Wnts. An involvement of Wnt7 in PCP regulation has been described in vertebrates (http://dx.doi.org/10.1016/j.celrep.2013.12.026). This would challenge the entire discussion and speculation on the evolutionary implications according to which PCP Wnt signaling comes first (PCP-first scenario") and canonical Wnt signaling later in metazoan evolution.

(4) The discussion, including Figure 6, is strongly biased towards the traditional evolutionary scenario postulating a choanzoan-sponge ancestry of metazoans. Chromosome-linkage data of pre-metazoans and metazoans (Schulz et al., 2023; https://doi.org/10 (1038/s41586-023-05936-6) now indicate a radically different scenario according to which ctenophores represent the ancestral form and are sister to sponges, cnidarians and bilaterians (the Ctenophora-sister hypothesis). This has also implications for the evolution of Wnt signalling, as discussed in the recent Nature Genetics Review by Holzem et al. (2024) (https://doi.org/10.1038/s41576-024-00699-w). Furthermore, it calls into question the hypothesis of a filter-feeding multicellular gastrula-like ancestor as proposed by Haeckel (Maegele et al., 2023). These papers have not yet been referenced, but they would provide a more robust discussion.

Reviewer #2 (Public review):

Summary:

Canonical Wnt signaling has previously been shown to be responsible for correct patterning of the oral-aboral axis as well as germ layer formation in several cnidarians. In the post-gastrula stage, the planula larvae are not only elongated, they have a specific swimming direction due to the decentralized cellular positioning and slanted anchoring of the cilia. This in turn is in most other animals the result of a Wnt-Planar-cell polarity pathway. This paper by Uveira et al investigates the role of Wnt3 signaling in serving as a local cue for the PCP pathway which then is responsible for the orientation of the cilia and elongation of the planula larva of the hydrozoan Clytia hemisphaerica. Wnt3 was shown before to activate the canonical pathway via ß-catenin and to act as an axial organizer. The authors provide compelling evidence for this somewhat unusual direct link between the pathways through the same signaling molecule, Wnt3. In conclusion, they propose a two-step model: (1) local orientation by Wnt3 secretion and (2) global propagation by the PCP pathway over the whole embryo.

Strengths:

In a series of elegant and also seemingly sophisticated experiments, they show that Wnt3 activates the PCP pathway directly, as it happens in the absence of canonical Wnt signaling (e.g. through co-expression of dnTCF). Conversely, constitutive active ß-catenin was not able to rescue PCP coordination upon Wnt3 depletion, yet restored gastrulation. This uncouples the effect of Wnt3 on axis specification and morphogenetic movements from the elongation via PCP. Through transplantation of single blastomeres providing a local source of Wnt3, they also demonstrate the reorganization of cellular polarity immediately adjacent to the Wnt3-expressing cell patch. These transplantation experiments also uncover that mechanical cues can also trigger polarization, suggesting a mechanotransduction or direct influence on subcellular structures, e.g. actin fiber orientation.

This is a beautiful and elegant study addressing an important question. The results have significant implications also for our understanding of the evolutionary origin of axis formation and the link of these two ancient pathways, which in most animals are controlled by distinct Wnt ligands and Frizzled receptors. The quality of the data is stunning and the paper is written in a clear and succinct manner. This paper has the potential to become a widely cited milestone paper.

Weaknesses:

I can not detect any major weaknesses. The work only raises a few more follow-up questions, which the authors are invited to comment on.

Reviewer #1 (Public review):

Summary:

In this study, Kroll et al. conduct an in-depth behavioral analysis of F0 knockouts of 4 genes associated with late-onset Alzheimer's Disease (AD), together with 3 genes associated with early-onset AD. Kroll and colleagues developed a web application (ZOLTAR) to compare sleep-associated traits between genetic mutants with those obtained from a panel of small molecules to promote identification of affected pathways and potential therapeutic interventions. The authors make a set of potentially important findings vis-à-vis the relationship between AD-associated genes and sleep. First, they find that loss-of-function in late-onset AD genes universally result in nighttime sleep loss, consistent with the well-supported hypothesis that sleep disruption contributes to Alzheimer's-related pathologies. psen-1, an early-onset associated AD gene, which the authors find is principally responsible for the generation of AB40 and AB42 in zebrafish, also shows a slight increase in activity at night and slight decreases in nighttime sleep. Conversely, psen-2 mutations increase daytime sleep, while appa/appb mutations have no impact on sleep. Finally, using ZOLTAR, the authors identify serotonin receptor activity as potentially disrupted in sorl1 mutants, while betamethasone is identified as a potential therapeutic to promote reversal of psen2 knockout-associated phenotypes.

This is a highly innovative and thorough study, yet a handful of key questions remain. First, are the nighttime sleep loss phenotypes observed in all knockouts for late-onset AD genes in the larval zebrafish a valid proxy for AD risk? Can 5-HT reuptake inhibitors reverse other AD-related pathologies in zebrafish? Can compounds be identified which have a common behavioral fingerprint across all or multiple AD risk genes? Do these modify sleep phenotypes? Finally, the authors propose but do not test the hypothesis that sorl1 might regulate localization/surface expression of 5-HT2 receptors. This could provide exciting / more convincing mechanistic support for the assertion that serotonin signaling is disrupted upon loss of AD-associated genes. Despite these important considerations, this study provides a valuable platform for high-throughput analysis of sleep phenotypes and correlation with small-molecule induced sleep phenotypes. The platform could also be expanded to facilitate comparison of other behavioral phenotypes, including stimulus-evoked behaviors. Moreover, the new analyses looking for pathways that might be co-regulated by AD risk genes and discussion of cholinergic signaling as a potentially meaningful target downstream of 5/7 knockouts are valuable.

Strengths:<br /> - Provides a useful platform for comparison of sleep phenotypes across genotypes/drug manipulations.<br /> - Presents convincing evidence that nighttime sleep is disrupted in mutants for multiple late-onset AD-related genes.<br /> - Provides potential mechanistic insights for how AD-related genes might impact sleep and identifies a few drugs that modify their identified phenotypes.

Weaknesses:<br /> - Exploration of potential mechanisms for serotonin disruption in sorl1 mutants is limited<br /> - The pipeline developed is only used to examine sleep-related / spontaneous movement phenotypes. Stimulus-evoked behaviors are not examined.

Reviewer #2 (Public review):

Summary:

This work delineates the larval zebrafish behavioral phenotypes caused by F0 knockout of several important genes that increase risk for Alzheimer's disease. Using behavioral pharmacology, comparing the behavioral fingerprint of previously assayed molecules to the newly generated knockout data, compounds were discovered that impacted larval movement in ways that suggest interaction with or recovery of disrupted mechanisms.

Strengths:

This is a well-written manuscript that uses newly developed analysis methods to present the findings in a clear, high-quality way. The addition of an extensive behavioral analysis pipeline is of value to the field of zebrafish neuroscience and will be particularly helpful for researchers who prefer the R programming language. Even the behavioral profiling of these AD risk genes, regardless of the pharmacology aspect, is an important contribution. The recovery of most behavioral parameters in the psen2 knockout with betamethasone, predicted by comparing fingerprints, is an exciting demonstration of the approach. The hypotheses generated by this work are important stepping stones to future studies uncovering the molecular basis of the proposed gene-drug interactions and discovering novel therapeutics to treat AD or co-occurring conditions such as sleep disturbance. Most concerns are sufficiently addressed in the revised manuscript or response to reviewers.

Weaknesses:

- The overarching concept of the work is that comparing behavioral fingerprints can align genes and molecules with similarly disrupted molecular pathways. While the recovery of the psen2 phenotypes by one molecule with the opposite phenotype is interesting, as are previous studies that show similar behaviorally-based recoveries, the underlying assumption that normalizing the larval movement normalizes the mechanism still lacks substantial support. While I agree with the authors detailed response that rescuing most behavioral parameters is a good indication that the underlying mechanism is normalized, I disagree that high-throughput larval behavior kinematics is a sufficient enough representation of most behavioral parameters to be indicative of molecular mechanism normalization. There are many instances of mutants with completely normal kinetics at baseline, but a behavioral difference that emerges during stimulation or in a new paradigm such as hunting. Without testing far more behavioral paradigms than are possible in the multi-well plate format, as well as possibly multiple life stages, I remain unconvinced that this approach will yield valuable therapeutic insights. I do agree that it can yield insight for future investigation, such as in the case of cntnap2a/cntnap2b and GABA receptor agonists, but even in that instance is it not clear that such an agonist would rescue abnormalities in a meaningful way. In the case of a disorder such as autism, the early locomotor phenotypes may be disconnected from the molecular mechanisms underlying later social deficits, and it is far more challenging to screen on juvenile behaviors that would be a more appropriate target for a behavior-first approach. The added experiment of testing fluvoxamine, a second SSRI, yielded very different behavioral responses to the SSRI citalopram, supporting my assertion that this approach and the disrupted underlying mechanisms are more complicated than suggested by the authors. I disagree that the connection between sorl1 and serotonin is strengthened by this experiment. The authors suggest that since the knockout larvae react differently than control siblings to both SSRIs, it indicates that serotonin is disrupted. There is no negative control included, where a pathway that is clearly not indicated to be important is pharmacologically manipulated. It is possible that the mutants would also behave differently compared to siblings when other pathways are perturbed. The authors acknowledge in the reviewers that they may not have identified the underlying molecular disruption in this mutant, but they did not substantially alter the Discussion section on this point. I agree with the authors that using a different wild-type strain in a different lab could lead to discrepancies, but these issues could have been experimentally mitigated or more clearly highlighted in the manuscript itself.

Reviewer #1 (Public Review):

In this work, Kanie and colleagues explored the role of NCS1 in capturing the ciliary vesicle. The microscopy was well executed and appropriately quantified. The authors convincingly show that while NCS1 is important for capturing the ciliary vesicle, another unknown distal appendage component is partially redundant in that ciliary vesicle capture and ciliary assembly are not fully dependent on NCS1. Overall, I am convinced by the data, and my only concern is that the discussion of the mouse phenotypes does not do a good job of putting this gene into the greater context of the complexity of mouse mutations.

Interestingly NCS1 has been previously studied in the context of neurotransmission and the new findings raise questions about whether prior findings are actually due to neuronal cilia defects.

Reviewer #2 (Public Review):

Kanie et al have recently characterized DAP protein CEP89 as important for the recruitment of the ciliary vesicle. Here, they describe a novel interacting partner for CEP89 that can bind membranes and therefore mediates its role in ciliary vesicle recruitment. An initial LAP tag pull-down and mass spectrometry experiment finds NCS-1 and C3ORF14 as CEP89 interactors. This interaction is mapped in the context of the ciliary vesicle formation. From the data presented, it is clear that, upon knockout, the function of these proteins might be compensated by others, as the phenotype can eventually recover over time.

In terms of the biological significance of this interaction, it would be good to examine (via co-immunoprecipitation) whether the CEP89/NCS-1/C3ORF14 interaction takes place upon serum starvation. Does the complex change?

Also, for the subdistal appendage localization of NCS-1 and C3ORF14, would this also change upon serum starvation?

For the ciliation results and the recruitment of IFT88 in CEP89 knockout cell lines, this contradicts previous work from Tanos et al (PMID: 23348840), as well as Hou et al (PMID: 36669498). A parallel comparison using siRNA, a transient knockout system, or a degron system would help understand this. A similar point goes for Figure 4, where the effect on ciliogenesis is minimal in knockout cells, but acute siRNA has been shown to have a stronger phenotype.

An elegant phenotype rescue is shown in Figure 5. An interesting question would be, how does this mutant and/or the myristoylation affect the recruitment of C3ORF14?

For the EF-hand mutants, it would be good to use control mutants, from known Ca2+ binding proteins as a control for the experiment shown.

Reviewer #3 (Public Review):

This work addresses an important question aimed at understanding how membrane docking to the distal appendages is regulated during ciliogenesis. In this study, Tomoharu and colleagues identified interactions between CEP89 (important for RAB34-positive membrane localization to the mother centriole) and NCS1 and C3ORF14. Both these CEP89 interacting proteins were characterized as distal appendage localized proteins between CEP89 and RAB34 based on super-resolution microscopy. Ciliogenesis investigations using knockout cells indicated that NCS1 and CEP89 have similar impaired ciliation due to disruption in vesicle recruitment/RAB34 to the mother centriole, while C3ORF14 had less effect on ciliogenesis. The authors refer to the ciliogenesis requirement for CEP89/NCS1 as ciliary vesicles, which has been previously referred to as preciliary vesicle or distal appendage vesicles. NCS1 distal appendage localization was dependent on CEP89 and TTBK2, but it is not clear how TTBK2 affects NCS1. The authors subsequently performed double knockouts with NCS1 and other distal appendage proteins and showed stronger effects on mother centriole RAB34 levels, suggesting efficient membrane docking during ciliogenesis requires several distal appendage proteins. This is consistent with NCS1 knockout mice which do not display typical ciliopathy phenotypes. These mice do display obesity, which is associated with cilia dysfunction, and show reduced ciliary protein levels. As noted by the authors, the in vivo results for NCS1 knockouts could be affected by the mouse background which was not evaluated. The authors demonstrate the NCS1 myristoylation motif is required for RAB34 localization to the mother centrioles, providing a mechanistic explanation for how distal appendage proteins could interact with membranes during ciliogenesis. Overall the authors' findings support an important role for NCS1 in regulating ciliogenesis via myristoylation-dependent interaction with RAB34-positive membranes docked at the mother centriole.

Reviewer #1 (Public Review):

In this work, Kanie and colleagues explored the composition, structure, and assembly hierarchy of distal appendage proteins. The microscopy was well executed and appropriately quantified. Importantly, the quality of individual antibodies was documented with a discussion of how this might complicate results. The hierarchy of assembly was established by careful quantification of assembly in an extensive set of knockout cell lines. This work will be of interest to cell biologists exploring organelle assembly as well as human geneticists trying to understand the clinical implications of mutations.

Reviewer #2 (Public Review):

Kanie et all have carried out a tour-de-force effort to further understand the hierarchy and function of centriole distal appendages in ciliogenesis. They made a thorough effort to understand the localization of all the known distal appendage proteins. To examine the distal appendage hierarchy, they used an automated analysis of centrosomal localization. It is not clear how this was quantified and pictures are not shown. They used CEP170, a marker for subdistal appendages, to define a mask around centrioles. It is not clear how the experiment was analyzed and normalized. The techniques used in this study cannot be compared with those commonly used in the field which normally include storm and other super-resolution techniques (which are less prone to artifacts) and correlated electron microscopy. Thus, it is not possible to make a head-to-head comparison. The lack of rescue experiments further weakens the conclusions of this paper.

Reviewer #3 (Public Review):

Distal appendages are multiprotein complexes that are only present on the mother centriole as a 9-fold symmetric structure that functions in ciliogenesis. How distal appendage proteins are organized and assembled still remains poorly understood. In this manuscript, Kanie et al. comprehensively analyzed the localizations of known and newly described distal appendage proteins using super-resolution microscopy. They investigated mechanisms associated with distal appendage assembly and their roles in the early stages of ciliogenesis in CRISPR-Cas9 knockout cells, which enabled a clearer investigation of these structures compared to previous RNAi depletion studies. These studies confirm previous findings for distal appendage protein ciliogenesis function and demonstrate the CEP83-SCLT1-CEP164-TTBK2 module is critical for both distal appendage assembly and the initiation of ciliogenesis. Notably, they find that CEP89 is dispensable for distal appendage assembly, but is needed for the recruitment of RAB34-positive ciliary vesicles to the mother centriole for ciliogenesis. Finally, this work introduces the application of single-molecule 3D super-resolution microscopy as a tool for interrogating the relationship between membranes and distal appendages. Overall this work extends our fundamental understanding of distal appendage structure/function in ciliogenesis.

An interesting observation from this work is that CEP83 is found localized both at the innermost region and the outermost region of the distal appendages when detected by antibodies that recognize a different epitope of CEP83 (Figure 1A), suggesting a helical structure that could serve as a platform for distal appendage assembly. A previous study using STORM imaging also showed that another distal appendage protein CEP164 occupies a wider region of the distal appendages when using an antibody recognizing the N-terminal residues of Cep164 (M Bowler et al. 2019). Together these studies show the importance of evaluating the structure of distal appendage proteins and the challenges of using antibody detection to reveal distal appendage hierarchy.

This work also highlights the potential differences in functional conclusions that can be drawn when comparing RNAi and CRISPR knockout depletion approaches. The latter which expectedly can lead to a more precise functional analysis of these small distal appendage structures, albeit with the potential for knockout cells to display compensatory regulation. Although not directly addressed in the text, the authors find that RPE-1 MYO5A knockout cells could ciliate which differs from a report by Wu et al. (2018). Furthermore, in the case of RAB34 knockout cells, the authors find CP110 removal from the mother centriole, while in previously published RAB34 KO studies this was not observed. In the case of the. RAB34 data a plausible explanation for the results given by the authors is that different assay conditions were used as was noted by the authors.

Reviewer #1 (Public review):

Summary:

The manuscript asks the question of whether astrocytes contribute to behavioral deficits triggered by early life stress. This question is tested by experiments that monitor the effects of early life stress on anxiety-like behaviors, long-term potentiation in the lateral amygdala, and immunohistochemistry of astrocyte-specific (GFAP, Cx43, GLT-1) and general activity (c-Fos ) markers. Secondarily, astrocyte activity in the lateral amygdala is impaired by viruses that suppress gap-junction coupling or reduce astrocyte Ca2+ followed by behavioral, synaptic plasticity, and c-Fos staining. Early life stress is found to reduce expression of GFAP, Cx43 and induce translocation of the glucocorticoid receptor to astrocytic nuclei. Both early life stress and astrocyte manipulations are found to result in generalization of fear to neutral auditory cues. All of the experiments are done well with appropriate statistics and control groups. The manuscript is very well-written and the data are presented clearly. The authors' conclusion that lateral amygdala astrocytes regulate amygdala-dependent behaviors is strongly supported by the data as is the conclusion that cellular and behavioral outcomes provoked by early life stress are similar to the outcomes provoked by astrocyte dysfunction. However, the extent to which early life stress requires astrocytes to generate these outcomes remains open to debate.

Strengths:

A strong combination of behavioral, electrophysiology, and immunostaining approaches is utilized and possible sex-differences in behavioral data are considered. The experiments clearly demonstrate that disruption of astrocyte networks or reduction of astrocyte Ca2+ provoke generalization of fear and impair long-term potentiation in lateral amygdala. The provocative finding that astrocyte dysfunction accounts for a subset of behavioral effects of early life stress (e.g. not elevated plus or distance traveled observations) is also perceived as a strength.

Weaknesses:

The main weakness is absence of direct evidence that behavioral and neuronal plasticity after early life stress can be attributed to astrocytes. It remains unknown what would happen if astrocyte activity were disrupted concurrently with early life stress or if changes in astrocyte Ca2+ could attenuate early life stress outcomes. As is, the only presented evidence that early life stress involves astrocytes is nuclear translocation of GR and downregulation of GFAP and Cx43 in Figure 3 which may or may not cause the reported astrocyte activity changes.

Reviewer #2 (Public review):

Summary:

In this manuscript, Guayasamin et al. show that early-life stress (ELS) can induce a shift in fear generalisation in mice. They took advantage of a fear conditioning paradigm followed by a discrimination test and complement learning and memory findings with measurements for anxiety-like behaviors. Next, astrocytic dysfunction in the lateral amygdala was investigated at the cellular level by combining staining for c-Fos with astrocyte-related proteins. Changes in excitatory neurotransmission were observed in acute brains slices after ELS suggesting impaired communication between neurons and astrocytes. To confirm causality of astrocytic-neuronal dysfunction in behavioral changes, viral manipulations were performed in unstressed mice. Occlusion of functional coupling with a dominant negative construct for gap junction connexin 43 or reduction in astrocytic calcium with CalEx mimicked the behavioral changes observed after ELS suggesting that dysfunction of the astrocytic network underlies ELS-induced memory impairments.

Strengths:

Overall, this well written manuscript highlights a key role for astrocytes in regulating stress-induced behavioral and synaptic deficits in the lateral amygdala in the context of ELS. Results are innovative, and methodological approaches relevant to decipher the role of astrocytes in behaviors. As mentioned by the authors, non-neuronal cells are receiving increasing attention in the neuroscience, stress and psychiatry fields.

Weaknesses:

I did have several suggestions and comments that were addressed during the review process. I believe that it improved clarity and will increase the impact of the work.

Reviewer #3 (Public review):

Summary:

The authors show that ELS induces a number of brain and behavioral changes in the adult lateral amygdala. These changes include enduring astrocytic dysfunction, and inducing astrocytic dysfunction via genetic interventions is sufficient to phenocopy the behavioral and neural phenotypes suggesting astrocyte dysfunction may play a causal role in ELS-associated pathologies.

Strengths:

A strength is the shift in focus to astrocytes to understand how ELS alters adult behavior.

Weaknesses:

The mechanistic links between some of the correlates - altered astrocytic function, changes in neural excitability and synaptic plasticity in the lateral amygdala and behavior - are underdeveloped.

Comments on revisions:

The authors have significantly improved the paper with the addition of new experimental data, analyses, and textual changes.

Reviewer #1 (Public review):

Summary:

The authors attempt to validate Fisher Kernels on the top of HMM as a way to better describe human brain dynamics at resting-state. The objective criterion was the better prediction of the proposed pipeline of the individual traits.

Comments on revisions:

The authors addressed adequately all my comments.

Reviewer #3 (Public review):

Summary:

In this work, the authors use a Hidden Markov Model (HMM) to describe dynamic connectivity and amplitude patterns in fMRI data, and propose to integrate these features with the Fisher kernel to improve the prediction of individual traits. The approach is tested using a large sample of healthy young adults from the Human Connectome Project. The HMM-Fisher Kernel approach was shown to achieve higher prediction accuracy with lower variance on many individual traits compared to alternate kernels and measures of static connectivity. As an additional finding, the authors demonstrate that parameters of the HMM state matrix may be more informative in predicting behavioral/cognitive variables in this data compared to state-transition probabilities.

Comments on revisions:

The authors have now addressed my comments, and I believe this work will be an interesting contribution to the literature.

Reviewer #1 (Public review):

Summary:

This study adapts a previously published model of the cat spinal locomotor network to make predictions of how phase durations of swing and stance at different treadmill speeds in tied-belt and split-belt conditions would be altered following a lateral hemisection. The simulations make several predictions that are replicated in experimental settings. This updated manuscript addressed well many of the reviewer comments made to the first version.

Strengths:

-Despite only altering the connections in the model, the model is able to replicate very well several experimental findings. This provides strong validation for the model and highlights its utility as a tool to investigate the operations of mammalian spinal locomotor networks.

-The study provides insights about interactions between the left and right side of the spinal locomotor networks, and how these interactions depend on the mode of operation, as determined by speed and state of the nervous system.

-The writing is logical, clear and easy to follow.

Comments on revisions:

My concerns were well addressed by the authors. I have no additional concerns

Reviewer #2 (Public review):

This is a nice article that presents interesting findings. The model's predictions match the data, which is good. The discussion points to modeling plasticity after SCI, which will be important.

The manuscript is well-written and interesting, and the putative neural circuit mechanisms that the model uncovers are super cool if they can be tested in an animal.

Reviewer #1 (Public review):

Summary:

This is a high-quality, well-thought through analysis of STEC transmission in Alberta, Canada.

Strengths:

* The combined human and animal sampling is a great foundation for this kind of study.<br /> * Phylogenetic analyses seem to have been carried out in a high quality fashion.

Comments on the revised version:

I'd like to thank the authors for the diligence with which they addressed my comments. I agree with their points and am happy for the manuscript to proceed.

Reviewer #1 (Public review):

Summary:

Can a plastic RNN serve as a basis function for learning to estimate value. In previous work this was shown to be the case, with a similar architecture to that proposed here. The learning rule in previous work was back-prop with an objective function that was the TD error function (delta) squared. Such a learning rule is non-local as the changes in weights within the RNN, and from inputs to the RNN depends on the weights from the RNN to the output, which estimates value. This is non-local, and in addition, these weights themselves change over learning. The main idea in this paper is to examine if replacing the values of these non-local changing weights, used for credit assignment, with random fixed weights can still produce similar results to those obtained with complete bp. This random feedback approach is motivated by a similar approach used for deep feed-forward neural networks.

This work shows that this random feedback in credit assignment performs well but is not as well as the precise gradient-based approach. When more constraints due to biological plausibility are imposed performance degrades. These results are not surprising given previous results on random feedback. This work is incomplete because the delay times used were only a few time steps, and it is not clear how well random feedback would operate with longer delays. Additionally, the examples simulated with a single cue and a single reward are overly simplistic and the field should move beyond these exceptionally simple examples.

Strengths:

• The authors show that random feedback can approximate well a model trained with detailed credit assignment.<br /> • The authors simulate several experiments including some with probabilistic reward schedules and show results similar to those obtained with detailed credit assignments as well as in experiments.<br /> • The paper examines the impact of more biologically realistic learning rules and the results are still quite similar to the detailed back-prop model.

Weaknesses:

• The authors also show that an untrained RNN does not perform as well as the trained RNN. However, they never explain what they mean by an untrained RNN. It should be clearly explained. These results are actually surprising. An untrained RNN with enough units and sufficiently large variance of recurrent weights can have a high-dimensionality and generate a complete or nearly complete basis, though not orthonormal (e.g: Rajan&Abbott 2006). It should be possible to use such a basis to learn this simple classical conditioning paradigm. It would be useful to measure the dimensionality of network dynamics, in both trained and untrained RNN's.

• The impact of the article is limited by using a network with discrete time-steps, and only a small number of time steps from stimulus to reward. What is the length of each time step? If it's on the order of the membrane time constant, then a few time steps are only tens of ms. In the classical conditioning experiments typical delays are of the order to hundreds of milliseconds to seconds. Authors should test if random feedback weights work as well for larger time spans. This can be done by simply using a much larger number of time steps.

• In the section with more biologically constrained learning rules, while the output weights are restricted to only be positive (as well as the random feedback weights), the recurrent weights and weights from input to RNN are still bi-polar and can change signs during learning. Why is the constraint imposed only on the output weights? It seems reasonable that the whole setup will fail if the recurrent weights were only positive as in such a case most neurons will have very similar dynamics, and the network dimensionality would be very low. However, it is possible that only negative weights might work. It is unclear to me how to justify that bipolar weights that change sign are appropriate for the recurrent connections and inappropriate for the output connections. On the other hand, an RNN with excitatory and inhibitory neurons in which weight signs do not change could possibly work.

• Like most papers in the field this work assumes a world composed of a single cue. In the real world there many more cues than rewards, some cues are not associated with any rewards, and some are associated with other rewards or even punishments. In the simplest case, it would be useful to show that this network could actually work if there are additional distractor cues that appear at random either before the CS, or between the CS and US. There are good reasons to believe such distractor cues will be fatal for an untrained RNN, but might work with a trained RNN, either using BPPT or random feedback. Although this assumption is a common flaw in most work in the field, we should no longer ignore these slightly more realistic scenarios.

Reviewer #2 (Public review):

Summary:

Tsurumi et al. show that recurrent neural networks can learn state and value representations in simple reinforcement learning tasks when trained with random feedback weights. The traditional method of learning for recurrent network in such tasks (backpropagation through time) requires feedback weights which are a transposed copy of the feed-forward weights, a biologically implausible assumption. This manuscript builds on previous work regarding "random feedback alignment" and "value-RNNs", and extends them to a reinforcement learning context. The authors also demonstrate that certain non-negative constraints can enforce a "loose alignment" of feedback weights. The author's results suggest that random feedback may be a powerful tool of learning in biological networks, even in reinforcement learning tasks.

Strengths:

The authors describe well the issues regarding biologically plausible learning in recurrent networks and in reinforcement learning tasks. They take care to propose networks which might be implemented in biological systems and compare their proposed learning rules to those already existing in literature. Further, they use small networks on relatively simple tasks, which allows for easier intuition into the learning dynamics.

Weaknesses:

The principles discovered by the authors in these smaller networks are not applied to deeper networks or more complicated tasks, so it remains unclear to what degree these methods can scale up, or can be used more generally.

Reviewer #3 (Public review):

Summary:

The paper studies learning rules in a simple sigmoidal recurrent neural network setting. The recurrent network has a single layer of 10 to 40 units. It is first confirmed that feedback alignment (FA) can learn a value function in this setting. Then so-called bio-plausible constraints are added: (1) when value weights (readout) is non-negative, (2) when the activity is non-negative (normal sigmoid rather than downscaled between -0.5 and 0.5), (3) when the feedback weights are non-negative, (4) when the learning rule is revised to be monotic: the weights are not downregulated. In the simple task considered all four biological features do not appear to impair totally the learning.

Strengths:

(1) The learning rules are implemented in a low-level fashion of the form: (pre-synaptic-activity) x (post-synaptic-activity) x feedback x RPE. Which is therefore interpretable in terms of measurable quantities in the wet-lab.

(2) I find that non-negative FA (FA with non negative c and w) is the most valuable theoretical insight of this paper: I understand why the alignment between w and c is automatically better at initialization.

(3) The task choice is relevant since it connects with experimental settings of reward conditioning with possible plasticity measurements.

Weaknesses:

(4) The task is rather easy, so it's not clear that it really captures the computational gap that exists with FA (gradient-like learning) and simpler learning rule like a delta rule: RPE x (pre-synpatic) x (post-synaptic). To control if the task is not too trivial, I suggest adding a control where the vector c is constant c_i=1.

(5) Related to point 3), the main strength of this paper is to draw potential connection with experimental data. It would be good to highlight more concretely the prediction of the theory for experimental findings. (Ideally, what should be observed with non-negative FA that is not expected with FA or a delta rule (constant global feedback) ?).

(6a) Random feedback with RNN in RL have been studied in the past, so it is maybe worth giving some insights how the results and the analyzes compare to this previous line of work (for instance in this paper [1]). For instance, I am not very surprised that FA also works for value prediction with TD error. It is also expected from the literature that the RL + RNN + FA setting would scale to tasks that are more complex than the conditioning problem proposed here, so is there a more specific take-home message about non-negative FA? or benefits from this simpler toy task?<br /> (6b) Related to task complexity, it is not clear to me if non-negative value and feedback weights would generally scale to harder tasks. If the task in so simple that a global RPE signal is sufficient to learn (see 4 and 5), then it could be good to extend the task to find a substantial gap between: global RPE, non-negative FA, FA, BP. For a well chosen task, I expect to see a performance gap between any pair of these four learning rules. In the context of the present paper, this would be particularly interesting to study the failure mode of non-negative FA and the cases where it does perform as well as FA.

(7) I find that the writing could be improved, it mostly feels more technical and difficult than it should. Here are some recommendations:<br /> (7a) for instance the technical description of the task (CSC) is not fully described and requires background knowledge from other paper which is not desirable.<br /> (7b) Also the rationale for the added difficulty with the stochastic reward and new state is not well explained.<br /> (7c) In the technical description of the results I find that the text dives into descriptive comments of the figures but high-level take home messages would be helpful to guide the reader. I got a bit lost, although I feel that there is probably a lot of depth in these paragraphs.

(8) Related to the writing issue and 5), I wished that "bio-plausibility" was not the only reason to study positive feedback and value weights. Is it possible to develop a bit more specifically what and why this positivity is interesting? Is there an expected finding with non-negative FA both in the model capability? or maybe there is a simpler and crisp take-home message to communicate the experimental predictions to the community would be useful?

(1) https://www.nature.com/articles/s41467-020-17236-y

Reviewer #1 (Public review):

This is an interesting manuscript where the authors systematically measure rG4 levels in brain samples at different ages of patients affected by AD. To the best of my knowledge this is the first time that BG4 staining is used in this context and the authors provide compelling evidence to show an association with BG4 staining and age or AD progression, which interestingly indicates that such RNA structure might play a role in regulating protein homeostasis as previously speculated. The methods used and the results reported seems robust and reproducible. There were two main things that needed addressing:

(1) Usually in BG4 staining experiments to ensure that the signal detected is genuinely due to rG4 an RNase treatment experiment is performed. This does not have to be extended to all the samples presented but having a couple of controls where the authors observe loss of staining upon RNase treatment will be key to ensure with confidence that rG4s are detected under the experimental conditions. This is particularly relevant for this brain tissue samples where BG4 staining has never been performed before.

(2) The authors have an association between rG4-formation and age/disease progression. They also observe distribution dependency of this, which is great. However, this is still an association which does not allow the model to be supported. This is not something that can be fixed with an easy experiment and it is what it is, but my point is that the narrative of the manuscript should be more fair and reflect the fact that, although interesting, what the authors are observing is a simple correlation. They should still go ahead and propose a model for it, but they should be more balanced in the conclusion and do not imply that this evidence is sufficient to demonstrate the proposed model. It is absolutely fine to refer to the literature and comment on the fact that similar observations have been reported and this is in line with those, but still this is not an ultimate demonstration.

Comments on current version:

The authors have now addressed my concerns.

Reviewer #2 (Public review):

RNA guanine-rich G-quadruplexes (rG4s) are non-canonical higher order nucleic acid structures that can form under physiological conditions. Interestingly, cellular stress is positively correlated with rG4 induction.

In this study, the authors examined human hippocampal postmortem tissue for the formation ofrG4s in aging and Alzheimer Disease (AD). rG4 immunostaining strongly increased in the hippocampus with both age and with AD severity. 21 cases were used in this study (age range 30-92).

This immunostaining co-localized with hyper-phosphorylated tau immunostaining in neurons. The BG4 staining levels were also impacted by APOE status. rG4 structure was previously found to drive tau aggregation. Based on these observations, the authors propose a model of neurodegeneration in which chronic rG4 formation drives proteostasis collapse.

This model is interesting, and would explain different observations (e.g., RNA is present in AD aggregates and rG4s can enhance protein oligomerization and tau aggregation).

Main issue from the previous round of review:

There is indeed a positive correlation between Braak stage severity and BG4 staining, but this correlation is relatively weak and borderline significant ((R = 0.52, p value = 0.028). This is probably the main limitation of this study, which should be clearly acknowledged (together with a reminder that "correlation is not causality"). Related to this, here is no clear justification to exclude the four individuals in Fig 1d (without them R increases to 0.78). Please remove this statement. On the other hand, the difference based on APOE status is more striking.

Comments on current version:

The authors have made laudable efforts to address the criticisms I made in my evaluation of the original manuscript.

Reviewer #2 (Public review):

Summary:

This paper by Olah et al., uncovers a previously unknown role of HCN channels in shaping synaptic inputs to L2/3 cortical neurons. The authors demonstrate using slice electrophysiology and computational modeling that unlike layer 5 pyramidal neurons, L2/3 neurons have an enrichment of HCN channels in the proximal dendrites. This location provides a locus of neuromodulation for inputs onto the proximal dendrites from L4 without an influence on distal inputs from L1. the authors use pharmacology to demonstrate the effect of HCN channels on NMDA-mediated synaptic inputs from L4. The authors further demonstrate the developmental time course of HCN function in L2/3 pyramidal neurons. Taken together, this a well constructed investigation of HCN channel function and the consequences of these channels on synaptic integration in L2/3 pyramidal neurons.

Strengths:

The authors use careful, well-constrained experiments using multiple pharmacological agents to asses HCN channel contributions to synaptic integrations. The authors also use voltage-clamp to directly measure the current through HCN channels across developmental ages. The authors also provide supplemental data showing that their observation is consistent across multiple areas of the cerebral cortex.

Weaknesses:

The gradient of HCN channel function is based almost exclusively on changes in EPSP width measured at the soma. While providing strong evidence for the presence of HCN current in L2/3 neurons, there are space clamp issues related to the use of somatic whole-cell voltage clamp that should be considered in the discussion. One omission by the authors is related to cell morphology. They make a point of normalizing the current injections to cell capacitance to account for variability in neuronal morphology. It is not clear however, how, if at all, this variability would affect EPSP propagation and modulation by proximal HCN channels. This should at least be discussed. Also, if there is high variability in cell morphology, was this considered in the modeling experiments?

Reviewer #3 (Public review):

Summary:

The authors study the function of HCN channels in L2/3 pyramidal neurons, employing somatic whole-cell recordings in acute slices of visual cortex in adult mice and a bevy of technically challenging techniques. Their primary claim is a non-uniform HCN distribution across the dendritic arbor with greater density closer to the soma (roughly opposite of the gradient found in L5 PT-type neurons). The second major claim is that multiple sources of long-range excitatory input (cortical and thalamic) are differentially affected by the HCN distribution. They further describe an interesting interplay of NMDAR and HCN, serotonergic modulation of HCN, and compare HCN-related properties at 1-, 2- and 6-weeks of age. Several results are accompanied by biophysical simulations.

Strengths:

The authors collected data from both male and female mice, at an age (6-10 weeks) that permits comparison with in vivo studies, in sufficient numbers for each condition, and they collected a good number of data points for almost all figure panels. This is all the more positive, considering the demanding nature of multi-electrode recording configurations and pipette-perfusion. The main strength of the study is the question and focus.

Weaknesses:

Unfortunately, in its present form, the main claims are not adequately supported by the experimental evidence: primarily because the evidence is indirect and circumstantial, but also because multiple unusual experimental choices (along with poor presentation of results) undermine the reader's confidence. Additionally, the authors overstate the novelty of certain results and fail to cite important related publications. Some of these weaknesses can be addressed by improved analysis, statistics, resolving inconsistent data across figures, reorganizing/improving figure panels, more complete methods, improved citations, and proofreading. In particular, given the emphasis on EPSPs, the primary data (example EPSPs, overlaid conditions) should be shown much more.

However on the experimental side, addressing the reviewer's concerns would require a very substantial additional effort: direct measurement of HCN density at different points in the dendritic arbor and soma; the internal solution chosen here (K-gluconate) is reported to inhibit HCN; bath-applied cesium at the concentrations used blocks multiple potassium channels, i.e. is not selective for HCN (the authors have concerns about using the more selective blocker ZD7288, but did use it in a subset of experiments, some of which show quantitatively different results). In response to initial review, the authors performed pathway-specific synaptic stimulation, via optogenetic activation of specific long-range inputs - this approach is valuable and interesting, however the results are presented very minimally and only partially match those obtained by layer-specific electrical stimulation.

Reviewer #1 (Public review):

The hypothesis is based on the idea that inversions capture genetic variants that have antagonistic effects on male sexual success (via some display traits) and survival of females (or both sexes) until reproduction. Furthermore, a sufficiently skewed distribution of male sexual success will tend to generate synergistic epistasis for male fitness even if the individual loci contribute to sexually selected traits in an additive way. This should favor inversions that keep these male-beneficial alleles at different loci together at a cis-LD. A series of simulations are presented and show that the scenario works at least under some conditions. While a polymorphism at a single locus with large antagonistic effects can be maintained for a certain range of parameters, a second such variant with somewhat smaller effects tends to be lost unless closely linked. It becomes much more likely for genomically distant variants that add to the antagonism to spread if they get trapped in an inversion; the model predicts this should drive accumulation of sexually antagonistic variants on the inversion versus standard haplotype, leading to the evolution of haplotypes with very strong cumulative antagonistic pleiotropic effects. This idea has some analogies with one of predominant hypotheses for the evolution of sex chromosomes, and the authors discuss these similarities. The model is quite specific, but the basic idea is intuitive and thus should be robust to the details of model assumption. It makes perfect sense in the context of the geographic pattern of inversion frequencies. One prediction of the models (notably that leads to the evolution of nearly homozygously lethal haplotypes) does not seem to reflect the reality of chromosomal inversions in Drosophila, as the authors carefully discuss, but it is the case of some other "supergenes", notably in ants. So the theoretical part is a strong novel contribution,

To provide empirical support for this idea, the authors study the dynamics of inversions in population cages over one generation, tracking their frequencies through amplicon sequencing at three time points: (young adults), embryos and very old adult offspring of either sex (>2 months from adult emergence). Out of four inversions included in the experiment, two show patterns consistent with antagonistic effects on male sexual success (competitive paternity) and the survival of offspring, especially females, until an old age, which the authors interpret as consistent with their theory.

As I have argued in my comments on previous versions, the experiment only addresses one of the elements of the theoretical hypothesis, namely antagonistic effects of inversions on male reproductive success and other fitness components, in particular of females. Furthermore, the design of this experiment is not ideal from the viewpoint of the biological hypothesis it is aiming to test. This is in part because, rather than testing for the effects of inversion on male reproductive success versus the key fitness components of survival to maturity and female reproductive output, it looks at the effects on male reproductive success versus survival to a rather old age of 2 months. The relevance of survival until old age to fitness under natural conditions is unclear, as the authors now acknowledge. Furthermore, up to 15% of males that may have contributed to the next generation did not survive until genotyping, and thus the difference between these males' inversion frequency and that in their offspring may be confounded by this potential survival-based sampling bias. The experiment does not test for two other key elements of the proposed theory: the assumption of frequency-dependence of selection on male sexual success, and the prediction of synergistic epistasis for male fitness among genetic variants in the inversion. To be fair, particularly testing for synergistic epistasis would be exceedingly difficult, and the authors have now included a discussion of the above caveats and limitations, making their conclusions more tentative. This is good but of course does not make these limitations of the experiment go away. These limitations mean that the paper is stronger as a theoretical than as an empirical contribution.

Reviewer #2 (Public review):

Summary:

In their manuscript the authors address the question whether the inversion polymorphism in D. melanogaster can be explained by sexually antagonistic selection. They designed a new simulation tool to perform computer simulations, which confirmed their hypothesis. They also show a tradeoff between male reproduction and survival. Furthermore, some inversions display sex-specific survival.

Strengths:

It is an interesting idea on how chromosomal inversions may be maintained

Weaknesses:

The authors motivate their study by the observation that inversions are maintained in D. melanogaster and because inversions are more frequent closer to the equator, the authors conclude that it is unlikely that the inversion contributes to adaptation in more stressful environments. Rather the inversion seems to be more common in habitats that are closer to the native environment of ancestral Drosophila populations.<br /> While I do agree with the authors that this observation is interesting, I do not think that it rules out a role in local adaptation. After all, the inversion is common in Africa, so it is perfectly conceivable that the non-inverted chromosome may have acquired a mutation contributing to the novel environment.

Based on their hypothesis, the authors propose an alternative strategy, which could maintain the inversion in a population. They perform some computer simulations, which are in line with the predicted behavior. Finally, the authors perform experiments and interpret the results as empirical evidence for their hypothesis. While the reviewer is not fully convinced about the empirical support, the key problem is that the proposed model does not explain the patterns of clinal variation observed for inversions in D. melanogaster. According to the proposed model, the inversions should have a similar frequency along latitudinal clines. So in essence, the authors develop a complicated theory because they felt that the current models do not explain the patterns of clinal variation, but this model also fails to explain the pattern of clinal variation.

Reviewer #3 (Public review):

Summary:

In this study, McAllester and Pool develop a new model to explain the maintenance of balanced inversion polymorphism, based on (sexually) antagonistic alleles and a trade-off between male reproduction and survival (in females or both sexes). Simulations of this model support the plausibility of this mechanism. In addition, the authors use experiments on four naturally occurring inversion polymorphisms in D. melanogaster and find tentative evidence for one aspect of their theoretical model, namely the existence of the above-mentioned trade-off in two out of the four inversions.

Strengths:

(1) The study develops and analyzes a new (Drosophila melanogaster-inspired) model for the maintenance of balanced inversion polymorphism, combining elements of (sexually) antagonistically (pleiotropic) alleles, negative frequency-dependent selection and synergistic epistasis. Simulations of the model suggest that the hypothesized mechanism might be plausible.

(2) The above-mentioned model assumes, as a specific example, a trade-off between male reproductive display and survival; in the second part of their study, the authors perform laboratory experiments on four common D. melanogaster inversions to study whether these polymorphisms may be subject to such a trade-off. The authors observe that two of the four inversions show suggestive evidence that is consistent with a trade-off between male reproduction and survival.

Open issues:

(1) A gap in the current modeling is that, while a diploid situation is being studied, the model does not investigate the effects of varying degrees of dominance. It would thus be important and interesting, as the authors mention, to fill this gap in future work,

(2) It will also be important to further explore and corroborate the potential importance and generality of trade-offs between different fitness components in maintaining inversion polymorphisms in future work.

Reviewer #1 (Public review):

Summary:

The use of antalarmin, a selective CRF1 receptor antagonist, prevents the deficits in sociability in (acutely) morphine-treated males, but not in females. In addition, cell attached experiments show a rescue to control levels of the morphine-induced increased firing in PVN neurons from morphine-treated males. Similar results are obtained in CRF receptor 1-/- male mice, confirming the involvement of CRF receptor 1-mediated signaling in both sociability deficits and neuronal firing changes in morphine-treated male mice.

Strengths:

In the revised version of the paper the authors respond to some reviewers's points with a new statistical analysis of behavioral data and a new discussion of previous literature.

Weaknesses:

Following reviewers' comments, the authors provided mechanistic insights of their findings with new experiments.

Reviewer #1 (Public Review):

Summary:

This manuscript from Clayton and co-authors aims to clarify the molecular mechanism of BRAF dimer selectivity. Indeed, first generation BRAF inhibitors, targeting monomeric BRAFV600E, are ineffective in treating resistant dimeric BRAF isoforms. Here, the authors employed molecular dynamics simulations to study the conformational dynamics of monomeric and dimeric BRAF, in the presence and absence of inhibitors. Multi-microseconds MD simulations showed an inward shift of the αC helix in the BRAFV600E mutant dimer. This helped identify a hydrogen bond between the inhibitors and the BRAF residue Glu501 as critical for dimer compatibility. The stability of the aforementioned interaction seems to be important to distinguish between dimer-selective and equipotent inhibitors.

Strengths:

The study is overall valuable and robust. The authors used the recently developed particle mesh Ewald constant pH molecular dynamics, a state-of-the-art method, to investigate the correct histidines protonation considering the dynamics of the protein. Then, multi-microsecond simulations showed differences in the flexibility of the αC helix and DFG motif. The dimerization restricts the αC position in the inward conformation, in agreement with the result that dimer-compatible inhibitors are able to stabilize the αC-in state. Noteworthy, the MD simulations were used to study the interactions between the inhibitors and the protein, suggesting a critical role for a hydrogen bond with Glu501. Finally, simulations of a mixed state of BRAF (one protomer bound to the inhibitor and the other apo) indicate that the ability to stabilize the inward αC state of the apo protomer could be at the basis of the positive cooperativity of PHI1.

Reviewer #2 (Public Review):

Summary:

The authors employ molecular dynamics simulations to understand the selectivity of FDA approved inhibitors within dimeric and monomeric BRAF species. Through these comprehensive simulations, they shed light on the selectivity of BRAF inhibitors by delineating the main structural changes occurring during dimerization and inhibitor action. Notably, they identify the two pivotal elements in this process: the movement and conformational changes involving the alpha-C helix and the formation of a hydrogen bond involving the Glu-501 residue. These findings find support in the analyses of various structures crystallized from dimers and co-crystallized monomers in the presence of inhibitors. The elucidation of this mechanism holds significant potential for advancing our understanding of kinase signalling and the development of future BRAF inhibitor drugs.

Strengths:

The authors employ a diverse array of computational techniques to characterize the binding sites and interactions between inhibitors and the active site of BRAF in both dimeric and monomeric forms. They combine traditional and advanced molecular dynamics simulation techniques such as CpHMD (All-atom continuous constant pH molecular dynamics) to provide mechanistic explanations. Additionally, the paper introduces methods for identifying and characterizing the formation of the hydrogen bond involving the Glu501 residue without the need for extensive molecular dynamics simulations. This approach facilitates the rapid identification of future BRAF inhibitor candidates.

Reviewer #1 (Public review):

Summary:

The authors test the "OHC-fluid-pump" hypothesis by assaying the rates of kainic acid dispersal both in quiet and in cochleae stimulated by sounds of different levels and spectral content. The main result is that sound (and thus, presumably, OHC contractions and expansions) result in faster transport along the duct. OHC involvement is corroborated using salicylate, which yielded results similar to silence. Especially interesting is the fact that some stimuli (e.g., tones) seem to provide better/faster pumping than others (e.g., noise), ostensibly due to the phase profile of the resulting cochlear traveling-wave response.

Strengths:

The experiments appear well controlled and the results are novel and interesting. Some elegant cochlear modeling that includes coupling between the organ of Corti and the surrounding fluid as well as advective flow supports the proposed mechanism.

The current limitations and future directions of the study, including possible experimental tests, extensions of the modeling work, and practical applications to drug delivery, are thoughtfully discussed.

Reviewer #2 (Public review):

Although recent cochlear micromechanical measurements in living animals have shown that outer hair cells drive broadband vibration of the reticular lamina, the role of this vibration in cochlear fluid circulation remains unclear. The authors hypothesized that motile outer hair cells facilitate cochlear fluid circulation. To test this, they investigated the effects of acoustic stimuli and salicylate on kainic acid-induced changes in the cochlear nucleus activities. The results reveal that low-frequency tones accelerate the effect of kainic acid, while salicylate reduces the impact of acoustic stimuli, indicating that outer hair cells actively drive cochlear fluid circulation.

The major strengths of this study lie in its high significance and the synergistic use of both electrophysiological recording and computational modeling. Recent in vivo observations of the broadband reticular lamina vibration challenge the traditional view of frequency-specific cochlear amplification. Furthermore, there is currently no effective noninvasive method to deliver the drugs or genes to the cochlea. This study addresses these important questions by observing outer hair cells' roles in the cochlear transport of kainic acid. The author utilized a well-established electrophysiological method to produce valuable new data and a custom-developed computational model to enhanced the interpretation of their experimental results.

The authors successfully validated their hypothesis, showing through the experimental and modeling results that active outer hair cells enhance cochlear fluid circulation in the living cochlea.

These findings have significant implications for advancing our understanding of cochlear amplification and offer promising clinical applications for treating hearing loss by accelerating cochlear drug delivery.

Reviewer #3 (Public review):

Summary:

This study reveals that sound exposure enhances drug delivery to the cochlea through the non-selective action of outer hair cells. The efficiency of sound-facilitated drug delivery is reduced when outer hair cell motility is inhibited. Additionally, low-frequency tones were found to be more effective than broadband noise for targeting substances to the cochlear apex. Computational model simulations support these findings.

Strengths:

The study provides compelling evidence that the broad action of outer hair cells is crucial for cochlear fluid circulation, offering a novel perspective on their function beyond frequency-selective amplification. Furthermore, these results could offer potential strategies for targeting and optimizing drug delivery throughout the cochlear spiral.

Reviewer #1 (Public review):

Summary:

The Major Histocompatibility Complex (MHC) region is a collection of numerous genes involved in both innate and adaptive immunity. MHC genes are famed for their role in rapid evolution and extensive polymorphism in a variety of vertebrates. This paper presents a summary of gene-level gain and loss of orthologs and paralogs within MHC across the diversity of primates, using publicly available data.

Strengths:

This paper provides a strong case that MHC genes are rapidly gained (by paralog duplication) and lost over millions of years of macroevolution. The authors are able to identify MHC loci by homology across species, and from this infer gene duplications and losses using phylogenetic analyses. There is a remarkable amount of genic turnover, summarized in Figure 6 and Figure 7, either of which might be a future textbook figure of immune gene family evolution. The authors draw on state-of-the-art phylogenetic methods, and their inferences are robust insofar as the data might be complete enough to draw such conclusions.

Weaknesses:

One concern about the present work is that it relies on public databases to draw inferences about gene loss, which is potentially risky if the publicly available sequence data are incomplete. To say, for example, that a particular MHC gene copy is absent in a taxon (e.g., Class I locus F absent in Guenons according to Figure 1), we need to trust that its absence from the available databases is an accurate reflection of its absence in the genome of the actual organisms. This may be a safe assumption, but it rests on the completeness of genome assembly (and gene annotations?) or people uploading relevant data. This reviewer would have been far more comfortable had the authors engaged in some active spot-checking, doing the lab work to try to confirm absences at least for some loci and some species. Without this, a reader is left to wonder whether gene loss is simply reflecting imperfect databases, which then undercuts confidence in estimates of rates of gene loss.

Some context is useful for comparing rates of gene turnover in MHC, to other loci. Changing gene copy numbers, duplications, and loss of duplicates, are common it seems across many loci and many organisms; is MHC exceptional in this regard, or merely behaving like any moderately large gene family? I would very much have liked to see comparable analyses done for other gene families (immune, like TLRs, or non-immune), and quantitative comparisons of evolutionary rates between MHC versus other genes. Does MHC gene composition evolve any faster than a random gene family? At present readers may be tempted to infer this, but evidence is not provided.

While on the topic of making comparisons, the authors make a few statements about relative rates. For instance, lines 447-8 compare gene topology of classical versus non-classical genes; and line 450 states that classical genes experience more turnover. But there are no quantitative values given to these rates to provide numerical comparisons, nor confidence intervals provided (these are needed, given that they are estimates), nor formal statistical comparisons to confirm our confidence that rates differ between types of genes.

More broadly, the paper uses sophisticated phylogenetic methods, but without taking advantage of macroevolutionary comparative methods that allow model-based estimation of macroevolutionary rates. I found the lack of quantitative measurements of rates of gene gain/loss to be a weakness of the present version of the paper, and something that should be readily remedied. When claiming that MHC Class I genes "turn over rapidly" (line 476) - what does rapidly mean? How rapidly? How does that compare to rates of genetic turnover at other families? Quantitative statements should be supported by quantitative estimates (and their confidence intervals).

The authors refer to 'shared function of the MHC across species' (e.g. line 22); while this is likely true, they are not here presenting any functional data to confirm this, nor can they rule out neofunctionalization or subfunctionalization of gene duplicates. There is evidence in other vertebrates (e.g., cod) of MHC evolving appreciably altered functions, so one may not safely assume the function of a locus is static over long macroevolutionary periods, although that would be a plausible assumption at first glance.

Reviewer #2 (Public review):

Summary:

The authors aim to provide a comprehensive understanding of the evolutionary history of the Major Histocompatibility Complex (MHC) gene family across primate species. Specifically, they sought to:

(1) Analyze the evolutionary patterns of MHC genes and pseudogenes across the entire primate order, spanning 60 million years of evolution.

(2) Build gene and allele trees to compare the evolutionary rates of MHC Class I and Class II genes, with a focus on identifying which genes have evolved rapidly and which have remained stable.

(3) Investigate the role of often-overlooked pseudogenes in reconstructing evolutionary events, especially within the Class I region.

(4) Highlight how different primate species use varied MHC genes, haplotypes, and genetic variation to mount successful immune responses, despite the shared function of the MHC across species.

(5) Fill gaps in the current understanding of MHC evolution by taking a broader, multi-species perspective using (a) phylogenomic analytical computing methods such as Beast2, Geneconv, BLAST, and the much larger computing capacities that have been developed and made available to researchers over the past few decades, (b) literature review for gene content and arrangement, and genomic rearrangements via haplotype comparisons.

(6) The authors overall conclusions based on their analyses and results are that 'different species employ different genes, haplotypes, and patterns of variation to achieve a successful immune response'.

Strengths:

Essentially, much of the information presented in this paper is already well-known in the MHC field of genomic and genetic research, with few new conclusions and with insufficient respect to past studies. Nevertheless, while MHC evolution is a well-studied area, this paper potentially adds some originality through its comprehensive, cross-species evolutionary analysis of primates, focus on pseudogenes and the modern, large-scale methods employed. Its originality lies in its broad evolutionary scope of the primate order among mammals with solid methodological and phylogenetic analyses.

The main strengths of this study are the use of large publicly available databases for primate MHC sequences, the intensive computing involved, the phylogenetic tool Beast2 to create multigene Bayesian phylogenetic trees using sequences from all genes and species, separated into Class I and Class II groups to provide a backbone of broad relationships to investigate subtrees, and the presentation of various subtrees as species and gene trees in an attempt to elucidate the unique gene duplications within the different species. The study provides some additional insights with summaries of MHC reference genomes and haplotypes in the context of a literature review to identify the gene content and haplotypes known to be present in different primate species. The phylogenetic overlays or ideograms (Figures 6 and 7) in part show the complexity of the evolution and organisation of the primate MHC genes via the orthologous and paralogous gene and species pathways progressively from the poorly-studied NWM, across a few moderately studied ape species, to the better-studied human MHC genes and haplotypes.

Weaknesses:

The title 'The Primate Major Histocompatibility Complex: An Illustrative Example of Gene Family Evolution' suggests that the paper will explore how the Major Histocompatibility Complex (MHC) in primates serves as a model for understanding gene family evolution. The term 'Illustrative Example' in the title would be appropriate if the paper aimed to use the primate Major Histocompatibility Complex (MHC) as a clear and representative case to demonstrate broader principles of gene family evolution. That is, the MHC gene family is not just one instance of gene family evolution but serves as a well-studied, insightful example that can highlight key mechanisms and concepts applicable to other gene families. However, this is not the case, this paper only covers specific details of primate MHC evolution without drawing broader lessons to any other gene families. So, the term 'Illustrative Example' is too broad or generalizing. In this case, a term like 'Case Study' or simply 'Example' would be more suitable. Perhaps, 'An Example of Gene Family Diversity' would be more precise. Also, an explanation or 'reminder' is suggested that this study is not about the origins of the MHC genes from the earliest jawed vertebrates per se (~600 mya), but it is an extension within a subspecies set that has emerged relatively late (~60 mya) in the evolutionary divergent pathways of the MHC genes, systems, and various vertebrate species.

Phylogenomics. Particular weaknesses in this study are the limitations and problems associated with providing phylogenetic gene and species trees to try and solve the complex issue of the molecular mechanisms involved with imperfect gene duplications, losses, and rearrangements in a complex genomic region such as the MHC that is involved in various effects on the response and regulation of the immune system. A particular deficiency is drawing conclusions based on a single exon of the genes. Different exons present different trees. Which are the more reliable? Why were introns not included in the analyses? The authors attempt to overcome these limitations by including genomic haplotype analysis, duplication models, and the supporting or contradictory information available in previous publications. They succeed in part with this multidiscipline approach, but much is missed because of biased literature selection. The authors should include a paragraph about the benefits and limitations of the software that they have chosen for their analysis, and perhaps suggest some alternative tools that they might have tried comparatively. How were problems with Bayesian phylogeny such as computational intensity, choosing probabilities, choosing particular exons for analysis, assumptions of evolutionary models, rates of evolution, systemic bias, and absence of structural and functional information addressed and controlled for in this study?

Gene families as haplotypes. In the Introduction, the MHC is referred to as a 'gene family', and in paragraph 2, it is described as being united by the 'MHC fold', despite exhibiting 'very diverse functions'. However, the MHC region is more accurately described as a multigene region containing diverse, haplotype-specific Conserved Polymorphic Sequences, many of which are likely to be regulatory rather than protein-coding. These regulatory elements are essential for controlling the expression of multiple MHC-related products, such as TNF and complement proteins, a relationship demonstrated over 30 years ago. Non-MHC fold loci such as TNF, complement, POU5F1, lncRNA, TRIM genes, LTA, LTB, NFkBIL1, etc, are present across all MHC haplotypes and play significant roles in regulation. Evolutionary selection must act on genotypes, considering both paternal and maternal haplotypes, rather than on individual genes alone. While it is valuable to compile databases for public use, their utility is diminished if they perpetuate outdated theories like the 'birth-and-death model'. The inclusion of prior information or assumptions used in a statistical or computational model, typically in Bayesian analysis, is commendable, but they should be based on genotypic data rather than older models. A more robust approach would consider the imperfect duplication of segments, the history of their conservation, and the functional differences in inheritance patterns. Additionally, the MHC should be examined as a genomic region, with ancestral haplotypes and sequence changes or rearrangements serving as key indicators of human evolution after the 'Out of Africa' migration, and with disease susceptibility providing a measurable outcome. There are more than 7000 different HLA-B and -C alleles at each locus, which suggests that there are many thousands of human HLA haplotypes to study. In this regard, the studies by Dawkins et al (1999 Immunol Rev 167,275), Shiina et al. (2006 Genetics 173,1555) on human MHC gene diversity and disease hitchhiking (haplotypes), and Sznarkowska et al. (2020 Cancers 12,1155) on the complex regulatory networks governing MHC expression, both in terms of immune transcription factor binding sites and regulatory non-coding RNAs, should be examined in greater detail, particularly in the context of MHC gene allelic diversity and locus organization in humans and other primates.

Diversifying and/or concerted evolution. Both this and past studies highlight diversifying selection or balancing selection model is the dominant force in MHC evolution. This is primarily because the extreme polymorphism observed in MHC genes is advantageous for populations in terms of pathogen defence. Diversification increases the range of peptides that can be presented to T cells, enhancing the immune response. The peptide-binding regions of MHC genes are highly variable, and this variability is maintained through selection for immune function, especially in the face of rapidly evolving pathogens. In contrast, concerted evolution, which typically involves the homogenization of gene duplicates through processes like gene conversion or unequal crossing-over, seems to play a minimal role in MHC evolution. Although gene duplication events have occurred in the MHC region leading to the expansion of gene families, the resulting paralogs often undergo divergent evolution rather than being kept similar or homozygous by concerted evolution. Therefore, unlike gene families such as ribosomal RNA genes or histone genes, where concerted evolution leads to highly similar copies, MHC genes display much higher levels of allelic and functional diversification. Each MHC gene copy tends to evolve independently after duplication, acquiring unique polymorphisms that enhance the repertoire of antigen presentation, rather than undergoing homogenization through gene conversion. Also, in some populations with high polymorphism or genetic drift, allele frequencies may become similar over time without the influence of gene conversion. This similarity can be mistaken for gene conversion when it is simply due to neutral evolution or drift, particularly in small populations or bottlenecked species. Moreover, gene conversion might contribute to greater diversity by creating hybrids or mosaics between different MHC genes. In this regard, can the authors indicate what percentage of the gene numbers in their study have been homogenised by gene conversion compared to those that have been diversified by gene conversion?

Duplication models. The phylogenetic overlays or ideograms (Figures 6 and 7) show considerable imperfect multigene duplications, losses, and rearrangements, but the paper's Discussion provides no in-depth consideration of the various multigenic models or mechanisms that can be used to explain the occurrence of such events. How do their duplication models compare to those proposed by others? For example, their text simply says on line 292, 'the proposed series of events is not always consistent with phylogenetic data'. How, why, when? Duplication models for the generation and extension of the human MHC class I genes as duplicons (extended gene or segmental genomic structures) by parsimonious imperfect tandem duplications with deletions and rearrangements in the alpha, beta, and kappa blocks were already formulated in the late 1990s and extended to the rhesus macaque in 2004 based on genomic haplotypic sequences. These studies were based on genomic sequences (genes, pseudogenes, retroelements), dot plot matrix comparisons, and phylogenetic analyses of gene and retroelement sequences using computer programs. It already was noted or proposed in these earlier 1999 studies that (1) the ancestor of HLA-P(90)/-T(16)/W(80) represented an old lineage separate from the other HLA class I genes in the alpha block, (2) HLA-U(21) is a duplicated fragment of HLA-A, (3) HLA-F and HLA-V(75) are among the earliest (progenitor) genes or outgroups within the alpha block, (4) distinct Alu and L1 retroelement sequences adjoining HLA-L(30), and HLA-N genomic segments (duplicons) in the kappa block are closely related to those in the HLA-B and HLA-C in the beta block; suggesting an inverted duplication and transposition of the HLA genes and retroelements between the beta and kappa regions. None of these prior human studies were referenced by Fortier and Pritchard in their paper. How does their human MHC class I gene duplication model (Fig. 6) such as gene duplication numbers and turnovers differ from those previously proposed and described by Kulski et al (1997 JME 45,599), (1999 JME 49,84), (2000 JME 50,510), Dawkins et al (1999 Immunol Rev 167,275), and Gaudieri et al (1999 GR 9,541)? Is this a case of reinventing the wheel?

Results. The results are presented as new findings, whereas most if not all of the results' significance and importance already have been discussed in various other publications. Therefore, the authors might do better to combine the results and discussion into a single section with appropriate citations to previously published findings presented among their results for comparison. Do the trees and subsets differ from previous publications, albeit that they might have fewer comparative examples and samples than the present preprint? Alternatively, the results and discussion could be combined and presented as a review of the field, which would make more sense and be more honest than the current format of essentially rehashing old data.

Minor corrections:

(1) Abstract, line 19: 'modern methods'. Too general. What modern methods?

(2) Abstract, line 25: 'look into [primate] MHC evolution.' The analysis is on the primate MHC genes, not on the entire vertebrate MHC evolution with a gene collection from sharks to humans. The non-primate MHC genes are often differently organised and structurally evolved in comparison to primate MHC.

(3) Introduction, line 113. 'In a companion paper (Fortier and Pritchard, 2024)' This paper appears to be unpublished. If it's unpublished, it should not be referenced.

(4) Figures 1 and 2. Use the term 'gene symbols' (circle, square, triangle, inverted triangle, diamond) or 'gene markers' instead of 'points'. 'Asterisks "within symbols" indicate new information.

(5) Figures. A variety of colours have been applied for visualisation. However, some coloured texts are so light in colour that they are difficult to read against a white background. Could darker colours or black be used for all or most texts?

(6) Results, line 135. '(Fortier and Pritchard, 2024)' This paper appears to be unpublished. If it's unpublished, it should not be referenced.

(7) Results, lines 152 to 153, 164, 165, etc. 'Points with an asterisk'. Use the term 'gene symbols' (circle, square, triangle, inverted triangle, diamond) or 'gene markers' instead of 'points'. A point is a small dot such as those used in data points for plotting graphs .... The figures are so small that the asterisks in the circles, squares, triangles, etc, look like points (dots) and the points/asterisks terminology that is used is very confusing visually.

(8) Line 178 (BEA, 2024) is not listed alphabetically in the References.

(9) Lines 188-190. 'NWM MHC-G does not group with ape/OWM MHC-G, instead falling outside of the clade containing ape/OWM MHC-A, -G, -J and -K.' This is not surprising given that MHC-A, -G, -J, and -K are paralogs of each other and that some of them, especially in NWM have diverged over time from the paralogs and/or orthologs and might be closer to one paralog than another and not be an actual ortholog of OWM, apes or humans.

(10) Line 249. Gene conversion: This is recombination between two different genes where a portion of the genes are exchanged with one another so that different portions of the gene can group within one or other of the two gene clades. Alternatively, the gene has been annotated incorrectly if the gene does not group within either of the two alternative clades. Another possibility is that one or two nucleotide mutations have occurred without a recombination resulting in a mistaken interpretation or conclusion of a recombination event. What measures are taken to avoid false-positive conclusions? How many MHC gene conversion (recombination) events have occurred according to the authors' estimates? What measures are taken to avoid false-positive conclusions?

(11) Lines 284-286. 'The Class I MHC region is further divided into three polymorphic blocks-alpha, beta, and kappa blocks-that each contains MHC genes but are separated by well-conserved non-MHC genes.' The MHC class I region was first designated into conserved polymorphic duplication blocks, alpha and beta by Dawkins et al (1999 Immunol Rev 167,275), and kappa by Kulski et al (2002 Immunol Rev 190,95), and should be acknowledged (cited) accordingly.

(12) Lines 285-286. 'The majority of the Class I genes are located in the alpha-block, which in humans includes 12 MHC genes and pseudogenes.' This is not strictly correct for many other species, because the majority of class I genes might be in the beta block of new and old-world monkeys, and the authors haven't provided respective counts of duplication numbers to show otherwise. The alpha block in some non-primate mammalian species such as pigs, rats, and mice has no MHC class I genes or only a few. Most MHC class I genes in non-primate mammalian species are found in other regions. For example, see Ando et al (2005 Immunogenetics 57,864) for the pig alpha, beta, and kappa regions in the MHC class I region. There are no pig MHC genes in the alpha block.

(13) Line 297 to 299. 'The alpha-block also contains a large number of repetitive elements and gene fragments belonging to other gene families, and their specific repeating pattern in humans led to the conclusion that the region was formed by successive block duplications (Shiina et al., 1999).' There are different models for successive block duplications in the alpha block and some are more parsimonious based on imperfect multigenic segmental duplications (Kulski et al 1999, 2000) than others (Shiina et al., 1999). In this regard, Kulski et al (1999, 2000) also used duplicated repetitive elements neighbouring MHC genes to support their phylogenetic analyses and multigenic segmental duplication models. For comparison, can the authors indicate how many duplications and deletions they have in their models for each species?

(14) Lines 315-315. 'Ours is the first work to show that MHC-U is actually an MHC-A-related gene fragment.' This sentence should be deleted. Other researchers had already inferred that MHC-U is actually an MHC-A-related gene fragment more than 25 years ago (Kulski et al 1999, 2000) when the MHC-U was originally named MHC-21.

(15) Lines 361-362. 'Notably, our work has revealed that MHC-V is an old fragment.' This is not a new finding or hypothesis. Previous phylogenetic analysis and gene duplication modelling had already inferred HLA-V (formerly HLA-75) to be an old fragment (Kulski et al 1999, 2000).

(16) Line 431-433. 'the Class II genes have been largely stable across the mammals, although we do see some lineage-specific expansions and contractions (Figure 2 and Figure 2-gure Supplement 2).' Please provide one or two references to support this statement. Is 'gure' a typo?

(17) Line 437. 'We discovered far more "specific" events in Class I, while "broad-scale" events were predominant in Class II.' Please define the difference between 'specific' and 'broad-scale'.<br /> 450-451. 'This shows that classical genes experience more turnover and are more often affected by long-term balancing selection or convergent evolution.' Is balancing selection a form of divergent evolution that is different from convergent evolution? Please explain in more detail how and why balancing selection or convergent evolution affects classical and nonclassical genes differently.

References. Some references in the supplementary materials such as Alvarez (1997), Daza-Vamenta (2004), Rojo (2005), Aarnink (2014), Kulski (2022), and others are missing from the Reference list. Please check that all the references in the text and the supplementary materials are listed correctly and alphabetically.

Reviewer #3 (Public review):

Summary:

The article provides the most comprehensive overview of primate MHC class I and class II genes to date, combining published data with an exploration of the available genome assemblies in a coherent phylogenetic framework and formulating new hypotheses about the evolution of the primate MHC genomic region.

Strengths:

I think this is a solid piece of work that will be the reference for years to come, at least until population-scale haplotype-resolved whole-genome resequencing of any mammalian species becomes standard. The work is timely because there is an obvious need to move beyond short amplicon-based polymorphism surveys and classical comparative genomic studies. The paper is data-rich and the approach taken by the authors, i.e. an integrative phylogeny of all MHC genes within a given class across species and the inclusion of often ignored pseudogenes, makes a lot of sense. The focus on primates is a good idea because of the wealth of genomic and, in some cases, functional data, and the relatively densely populated phylogenetic tree facilitates the reconstruction of rapid evolutionary events, providing insights into the mechanisms of MHC evolution. Appendices 1-2 may seem unusual at first glance, but I found them helpful in distilling the information that the authors consider essential, thus reducing the need for the reader to wade through a vast amount of literature. Appendix 3 is an extremely valuable companion in navigating the maze of primate MHC genes and associated terminology.

Weaknesses:

I have not identified major weaknesses and my comments are mostly requests for clarification and justification of some methodological choices.

Reviewer #1 (Public review):

The authors present their new bioinformatic tool called TEKRABber, and use it to correlate expression between KRAB ZNFs and TEs across different brain tissues, and across species. While the aims of the authors are clear and there would be significant interest from other researchers in the field for a program that can do such correlative gene expression analysis across individual genomes and species, the presented approach and work display significant shortcomings. In the current state of the analysis pipeline, the biases and shortcomings mentioned below, for which I have seen no proof that they are accounted for by the authors, are severely impacting the presented results and conclusions. It is therefore essential that the points below are addressed, involving significant changes in the TEKRABber program as well as the analysis pipeline, to prevent the identification of false positive and negative signals, that would severely affect the conclusions one can raise about the analysis.

My main concerns are provided below:

One important shortcoming of the biocomputational approach is that most TEs are not actually expressed, and others (Alus) are not a proxy of the activity of the TE class at all. I will explain: While specific TE classes can act as (species-specific) promoters for genes (such as LTRs) or are expressed as TE derived transcripts (LINEs, SVAs), the majority of other older TE classes do not have such behavior and are either neutral to the genome or may have some enhancer activity (as mapped in the program they refer to 'TEffectR'. A big focus is on Alus, but Alus contribute to a transcriptome in a different way too: They often become part of transcripts due to alternative splicing. As such, the presence of Alu derived transcripts is not a proxy for the expression/activity of the Alu class, but rather a result of some Alus being part of gene transcripts (see also next point). The bottom line is that the TEKRABber software/approach is heavily prone to picking up both false positives (TEs being part of transcribed loci) and false negatives (TEs not producing any transcripts at all), which has a big implication for how reads from TEs as done in this study should be interpreted: The TE expression used to correlate the KRAB ZNF expression is simply not representing the species-specific influences of TEs where the authors are after.

With the strategy as described, a lot of TE expression is misinterpreted: TEs can be part of gene-derived transcripts due to alternative splicing (often happens for Alus) or as a result of the TE being present in an inefficiently spliced out intron (happens a lot) which leads to TE-derived reads as a result of that TE being part of that intron, rather than that TE being actively expressed. As a result, the data as analysed is not reliably indicating the expression of TEs (as the authors intend to) and should be filtered for any reads that are coming from the above scenarios: These reads have nothing to do with KRAB ZNF control, and are not representing actively expressed TEs and therefore should be removed. Given that from my lab's experience in the brain (and other) tissues, the proportion of RNA sequencing reads that are actually derived from active TEs is a stark minority compared to reads derived from TEs that happen to be in any of the many transcribed loci, applying this filtering is expected to have a huge impact on the results and conclusions of this study.

Another potential problem that I don't see addressed is that due to the high level of similarity of the many hundreds of KRAB ZNF genes in primates and the reads derived from them, and the inaccurate annotations of many KZNFs in non-human genomes, the expression data derived from RNA-seq datasets cannot be simply used to plot KZNF expression values, without significant work and manual curation to safeguard proper cross species ortholog-annotation: The work of Thomas and Schneider (2011) has studied this in great detail but genome-assemblies of non-human primates tend to be highly inaccurate in appointing the right ortholog of human ZNF genes. The problem becomes even bigger when RNA-sequencing reads are analyzed: RNA-sequencing reads from a human ZNF that emerged in great apes by duplication from an older parental gene (we have a decent number of those in the human genome) may be mapped to that older parental gene in Macaque genome: So, the expression of human-specific ZNF-B, that derived from the parental ZNF-A, is likely to be compared in their DESeq to the expression of ZNF-A in Macaque RNA-seq data. In other words, without a significant amount of manual curation, the DE-seq analysis is prone to lead to false comparisons which make the strategy and KRABber software approach described highly biased and unreliable.

There is no doubt that there are differences in expression and activity of KRAB-ZNFs and TEs respectively that may have had important evolutionary consequences. However, because all of the network analyses in this paper rely on the analyses of RNA-seq data and the processing through the TE-KRABber software with the shortcomings and potential biases that I mentioned above, I need to emphasize that the results and conclusions are likely to be significantly different if the appropriate measures are taken to get more accurate and curated TE and KRAB ZNF expression data.

Finally, there are some minor but important notes I want to share:

The association with certain variations in ZNF genes with neurological disorders such as AD, as reported in the introduction is not entirely convincing without further functional support. Such associations could merely happen by chance, given the high number of ZNF genes in the human genome and the high chance that variations in these loci happen to associate with certain disease-associated traits. So using these associations as an argument that changes in TEs and KRAB ZNF networks are important for diseases like AD should be used with much more caution.

There are a number of papers where KRAB ZNF and TE expression are analysed in parallel in human brain tissues. So the novelty of that aspect of the presented study may be limited.

Reviewer #2 (Public review):

Summary:

The aim was to decipher the regulatory networks of KRAB-ZNFs and TEs that have changed during human brain evolution and in Alzheimer's disease.

Strengths:

This solid study presents a valuable analysis and successfully confirms previous assumptions, but also goes beyond the current state of the art.

Weaknesses:

The design of the analysis needs to be slightly modified and a more in-depth analysis of the positive correlation cases would be beneficial. Some of the conclusions need to be reinterpreted.

Reviewer #1 (Public review):

In this manuscript, Hoon Cho et al. presents a novel investigation into the role of PexRAP, an intermediary in ether lipid biosynthesis, in B cell function, particularly during the Germinal Center (GC) reaction. The authors profile lipid composition in activated B cells both in vitro and in vivo, revealing the significance of PexRAP. Using a combination of animal models and imaging mass spectrometry, they demonstrate that PexRAP is specifically required in B cells. They further establish that its activity is critical upon antigen encounter, shaping B cell survival during the GC reaction.

Mechanistically, they show that ether lipid synthesis is necessary to modulate reactive oxygen species (ROS) levels and prevent membrane peroxidation.

Highlights of the Manuscript:

The authors perform exhaustive imaging mass spectrometry (IMS) analyses of B cells, including GC B cells, to explore ether lipid metabolism during the humoral response. This approach is particularly noteworthy given the challenge of limited cell availability in GC reactions, which often hampers metabolomic studies. IMS proves to be a valuable tool in overcoming this limitation, allowing detailed exploration of GC metabolism.

The data presented is highly relevant, especially in light of recent studies suggesting a pivotal role for lipid metabolism in GC B cells. While these studies primarily focus on mitochondrial function, this manuscript uniquely investigates peroxisomes, which are linked to mitochondria and contribute to fatty acid oxidation (FAO). By extending the study of lipid metabolism beyond mitochondria to include peroxisomes, the authors add a critical dimension to our understanding of B cell biology.

Additionally, the metabolic plasticity of B cells poses challenges for studying metabolism, as genetic deletions from the beginning of B cell development often result in compensatory adaptations. To address this, the authors employ an acute loss-of-function approach using two conditional, cell-type-specific gene inactivation mouse models: one targeting B cells after the establishment of a pre-immune B cell population (Dhrs7b^f/f, huCD20-CreERT2) and the other during the GC reaction (Dhrs7b^f/f; S1pr2-CreERT2). This strategy is elegant and well-suited to studying the role of metabolism in B cell activation.

Overall, this manuscript is a significant contribution to the field, providing robust evidence for the fundamental role of lipid metabolism during the GC reaction and unveiling a novel function for peroxisomes in B cells. However, several major points need to be addressed:

Major Comments:

Figures 1 and 2

The authors conclude, based on the results from these two figures, that PexRAP promotes the homeostatic maintenance and proliferation of B cells. In this section, the authors first use a tamoxifen-inducible full Dhrs7b knockout (KO) and afterwards Dhrs7bΔ/Δ-B model to specifically characterize the role of this molecule in B cells. They characterize the B and T cell compartments using flow cytometry (FACS) and examine the establishment of the GC reaction using FACS and immunofluorescence. They conclude that B cell numbers are reduced, and the GC reaction is defective upon stimulation, showing a reduction in the total percentage of GC cells, particularly in the light zone (LZ).

The analysis of the steady-state B cell compartment should also be improved. This includes a more detailed characterization of MZ and B1 populations, given the role of lipid metabolism and lipid peroxidation in these subtypes.

Suggestions for Improvement:

- B Cell compartment characterization: A deeper characterization of the B cell compartment in non-immunized mice is needed, including analysis of Marginal Zone (MZ) maturation and a more detailed examination of the B1 compartment. This is especially important given the role of specific lipid metabolism in these cell types. The phenotyping of the B cell compartment should also include an analysis of immunoglobulin levels on the membrane, considering the impact of lipids on membrane composition.

- GC Response Analysis Upon Immunization: The GC response characterization should include additional data on the T cell compartment, specifically the presence and function of Tfh cells. In Fig. 1H, the distribution of the LZ appears strikingly different. However, the authors have not addressed this in the text. A more thorough characterization of centroblasts and centrocytes using CXCR4 and CD86 markers is needed.<br /> The gating strategy used to characterize GC cells (GL7+CD95+ in IgD− cells) is suboptimal. A more robust analysis of GC cells should be performed in total B220+CD138− cells.

- The authors claim that Dhrs7b supports the homeostatic maintenance of quiescent B cells in vivo and promotes effective proliferation. This conclusion is primarily based on experiments where CTV-labeled PexRAP-deficient B cells were adoptively transferred into μMT mice (Fig. 2D-F). However, we recommend reviewing the flow plots of CTV in Fig. 2E, as they appear out of scale. More importantly, the low recovery of PexRAP-deficient B cells post-adoptive transfer weakens the robustness of the results and is insufficient to conclusively support the role of PexRAP in B cell proliferation in vivo.

- In vitro stimulation experiments: These experiments need improvement. The authors have used anti-CD40 and BAFF for B cell stimulation; however, it would be beneficial to also include anti-IgM in the stimulation cocktail. In Fig. 2G, CTV plots do not show clear defects in proliferation, yet the authors quantify the percentage of cells with more than three divisions. These plots should clearly display the gating strategy. Additionally, details about histogram normalization and potential defects in cell numbers are missing. A more in-depth analysis of apoptosis is also required to determine whether the observed defects are due to impaired proliferation or reduced survival.

Reviewer #2 (Public review):

Summary:

In this study, Cho et al. investigate the role of ether lipid biosynthesis in B cell biology, particularly focusing on GC B cell, by inducible deletion of PexRAP, an enzyme responsible for the synthesis of ether lipids.

Strengths:

Overall, the data are well-presented, the paper is well-written and provides valuable mechanistic insights into the importance of PexRAP enzyme in GC B cell proliferation.

Weaknesses:

More detailed mechanisms of the impaired GC B cell proliferation by PexRAP deficiency remain to be further investigated. In the minor part, there are issues with the interpretation of the data which might cause confusion for the readers.

Reviewer #1 (Public review):

Summary:

The authors present an interesting study using RL and Bayesian modelling to examine differences in learning rate adaptation in conditions of high and low volatility and noise respectively. Through "lesioning" an optimal Bayesian model, they reveal that apparently a suboptimal adaptation of learning rates results from incorrectly detecting volatility in the environment when it is not in fact present.

Strengths:

The experimental task used is cleverly designed and does a good job of manipulating both volatility and noise. The modelling approach takes an interesting and creative approach to understanding the source of apparently suboptimal adaptation of learning rates to noise, through carefully "lesioning" and optimal Bayesian model to determine which components are responsible for this behaviour.

Weaknesses:

The study has a few substantial weaknesses; the data and modelling both appear robust and informative, and it tackles an interesting question. The model space could potentially have been expanded, particularly with regard to the inclusion of alternative strategies such as those that estimate latent states and adapt learning accordingly.

Reviewer #2 (Public review):

Summary:

In this study, the authors aimed to investigate how humans learn and adapt their behavior in dynamic environments characterized by two distinct types of uncertainty: volatility (systematic changes in outcomes) and noise (random variability in outcomes). Specifically, they sought to understand how participants adjust their learning rates in response to changes in these forms of uncertainty.

To achieve this, the authors employed a two-step approach:

(1) Reinforcement Learning (RL) Model: They first used an RL model to fit participants' behavior, revealing that the learning rate was context-dependent. In other words, it varied based on the levels of volatility and noise. However, the RL model showed that participants misattributed noise as volatility, leading to higher learning rates in noisy conditions, where the optimal strategy would be to be less sensitive to random fluctuations.

(2) Bayesian Observer Model (BOM): To better account for this context dependency, they introduced a Bayesian Observer Model (BOM), which models how an ideal Bayesian learner would update their beliefs about environmental uncertainty. They found that a degraded version of the BOM, where the agent had a coarser representation of noise compared to volatility, best fit the participants' behavior. This suggested that participants were not fully distinguishing between noise and volatility, instead treating noise as volatility and adjusting their learning rates accordingly.

The authors also aimed to use pupillometry data (measuring pupil dilation) as a physiological marker to arbitrate between models and understand how participants' internal representations of uncertainty influenced both their behavior and physiological responses. Their objective was to explore whether the BOM could explain not just behavioral choices but also these physiological responses, thereby providing stronger evidence for the model's validity.

Overall, the study sought to reconcile approximate rationality in human learning by showing that participants still follow a Bayesian-like learning process, but with simplified internal models that lead to suboptimal decisions in noisy environments.

Strengths:

The generative model presented in the study is both innovative and insightful. The authors first employ a Reinforcement Learning (RL) model to fit participants' behavior, revealing that the learning rate is context-dependent-specifically, it varies based on the levels of volatility and noise in the task. They then introduce a Bayesian Observer Model (BOM) to account for this context dependency, ultimately finding that a degraded BOM - in which the agent has a coarser representation of noise compared to volatility - provides the best fit for the participants' behavior. This suggests that participants do not fully distinguish between noise and volatility, leading to the misattribution of noise as volatility. Consequently, participants adopt higher learning rates even in noisy contexts, where an optimal strategy would involve being less sensitive to new information (i.e., using lower learning rates). This finding highlights a rational but approximate learning process, as described in the paper.

Weaknesses:

While the RL and Bayesian models both successfully predict behavior, it remains unclear how to fully reconcile the two approaches. The RL model captures behavior in terms of a fixed or context-dependent learning rate, while the BOM provides a more nuanced account with dynamic updates based on volatility and noise. Both models can predict actions when fit appropriately, but the pupillometry data offers a promising avenue to arbitrate between the models. However, the current study does not provide a direct comparison between the RL framework and the Bayesian model in terms of how well they explain the pupillometry data. It would be valuable to see whether the RL model can also account for physiological markers of learning, such as pupil responses, or if the BOM offers a unique advantage in this regard. A comparison of the two models using pupillometry data could strengthen the argument for the BOM's superiority, as currently, the possibility that RL models could explain the physiological data remains unexplored.

The model comparison between the Bayesian Observer Model and the self-defined degraded internal model could be further enhanced. Since different assumptions about the internal model's structure lead to varying levels of model complexity, using a formal criterion such as Bayesian Information Criterion (BIC) or Akaike Information Criterion (AIC) would allow for a more rigorous comparison of model fit. Including such comparisons would ensure that the degraded BOM is not simply favored due to its flexibility or higher complexity, but rather because it genuinely captures the participants' behavioral and physiological data better than alternative models. This would also help address concerns about overfitting and provide a clearer justification for using the degraded BOM over other potential models.

Reviewer #1 (Public review):

Summary:

In this study, the authors advance our understanding of neurodevelopmental changes in the brain's structural and functional connectivity, as well as their coupling. The paper presents evidence of alterations in and stability of the principal organizational gradients of structure and function across development (age) and contrasts them between neurotypical and neurodivergent individuals. The authors further extend their findings by exploring links with graph theory measures of brain connectivity and indices of nodal structure-function coupling. Finally, the developmental shifts in structural and functional brain organization are examined for potential associations with cognitive and psychopathological markers. The results suggest that structure-function coupling, both brain-wide and within specific functional networks, is associated with certain cognitive dimensions but not with measures of psychopathology.

Strengths:

This manuscript makes a significant contribution to the field by synthesizing previous research while offering novel insights into the developmental trajectories of brain organization. A key strength of this study lies in its integration of both structural and functional connectivity data, providing a comprehensive view of brain changes throughout development. The authors present findings that challenge earlier reports of shifts in principal gradients during late childhood and early adolescence (e.g., Dong et al., 2021; Xia et al., 2022), underscoring an important inconsistency that could have broader implications for our understanding of developmental brain reorganization. The introduction and discussion sections are well-crafted, offering a thorough review of relevant prior studies and effectively situating the current findings within the broader context of the literature. Additionally, the study design and methodology are detailed and adhere to recommended best practices, demonstrating a commendable level of rigor in the formulation of the study and its various assessments.

Weaknesses:

Despite these strengths, I think there are aspects of the manuscript that would benefit from further refinement. Below is detailed feedback and suggestions provided point-by-point.

Lack of Sensitivity Analyses for some Key Methodological Decisions:<br /> Certain methodological choices in this manuscript diverge from approaches used in previous works. In these cases, I recommend the following: (i) The authors could provide a clear and detailed justification for these deviations from established methods, and (ii) supplementary sensitivity analyses could be included to ensure the robustness of the findings, demonstrating that the results are not driven primarily by these methodological changes. Below, I outline the main areas where such evaluations are needed:<br /> - Use of Communicability Matrices for Structural Connectivity Gradients: The authors chose to construct structural connectivity gradients using communicability matrices, arguing that diffusion map embedding "requires a smooth, fully connected matrix." However, by definition, the creation of the affinity matrix already involves smoothing and ensures full connectedness. I recommend that the authors include an analysis of what happens when the communicability matrix step is omitted. This sensitivity test is crucial, as it would help determine whether the main findings hold under a simpler construction of the affinity matrix. If the results significantly change, it could indicate that the observations are sensitive to this design choice, thereby raising concerns about the robustness of the conclusions. Additionally, if the concern is related to the large range of weights in the raw structural connectivity (SC) matrix, a more conventional approach is to apply a log-transformation to the SC weights (e.g., log(1+𝑆𝐶𝑖𝑗)), which may yield a more reliable affinity matrix without the need for communicability measures.<br /> - Individual-Level Gradients vs. Group-Level Gradients: Unlike previous studies that examined alterations in principal gradients (e.g., Xia et al., 2022; Dong et al., 2021), this manuscript focuses on gradients derived directly from individual-level data. In contrast, earlier works have typically computed gradients based on grouped data, such as using a moving window of individuals based on age (Xia et al.) or evaluating two distinct age groups (Dong et al.). I believe it is essential to assess the sensitivity of the findings to this methodological choice. Such an evaluation could clarify whether the observed discrepancies with previous reports are due to true biological differences or simply a result of different analytical strategies.<br /> - Procrustes Transformation: It is unclear why the authors opted to include a Procrustes transformation in this analysis, especially given that previous related studies (e.g., Dong et al.) did not apply this step. I believe it is crucial to evaluate whether this methodological choice influences the results, particularly in the context of developmental changes in organizational gradients. Specifically, the Procrustes transformation may maximize alignment to the group-level gradients, potentially masking individual-level differences. This could result in a reordering of the gradients (e.g., swapping the first and second gradients), which might obscure true developmental alterations. It would be informative to include an analysis showing the impact of performing vs. omitting the Procrustes transformation, as this could help clarify whether the observed effects are robust or an artifact of the alignment procedure. (Please also refer to my comment on adding a subplot to Figure 1)<br /> - SC-FC Coupling Metric: The approach used to quantify nodal SC-FC coupling in this study appears to deviate from previously established methods in the field. The manuscript describes coupling as the "Spearman-rank correlation between Euclidean distances between each node and all others within structural and functional manifolds," but this description is unclear and lacks sufficient detail. Furthermore, this differs from what is typically referred to as SC-FC coupling in the literature. For instance, the cited study by Park et al. (2022) utilizes a multiple linear regression framework, where communicability, Euclidean distance, and shortest path length are independent variables predicting functional connectivity (FC), with the adjusted R-squared score serving as the coupling index for each node. On the other hand, the Baum et al. (2020) study, also cited, uses Spearman correlation, but between raw structural connectivity (SC) and FC values. If the authors opt to introduce a novel coupling metric, it is essential to demonstrate its similarity to these previous indices. I recommend providing an analysis (supplementary) showing the correlation between their chosen metric and those used in previous studies (e.g., the adjusted R-squared scores from Park et al. or the SC-FC correlation from Baum et al.). Furthermore, if the metrics are not similar and results are sensitive to this alternative metric, it raises concerns about the robustness of the findings. A sensitivity analysis would therefore be helpful (in case the novel coupling metric is not similar to previous ones) to determine whether the reported effects hold true across different coupling indices.

Methodological ambiguity/lack of clarity in the description of certain evaluation steps:<br /> Some aspects of the manuscript's methodological descriptions are ambiguous, making it challenging for future readers to fully reproduce the analyses based on the information provided. I believe the following sections would benefit from additional detail and clarification:<br /> - Computation of Manifold Eccentricity: The description of how eccentricity was computed (both in the results and methods sections) is unclear and may be problematic. The main ambiguity lies in how the group manifold origin was defined or computed. Specifically:<br /> (1) In the results section, it appears that separate manifold origins were calculated for the NKI and CALM groups, suggesting a dataset-specific approach.<br /> (2) Conversely, the methods section implies that a single manifold origin was obtained by somehow combining the group origins across the three datasets, which seems contradictory.<br /> Moreover, including neurodivergent individuals in defining the central group manifold origin is conceptually problematic. Given that neurodivergent participants might exhibit atypical brain organization (as suggested by Fig. 1), this inclusion could skew the definition of what should represent a typical or normative brain manifold. A more appropriate approach might involve constructing the group manifold origin using only the neurotypical participants from both the NKI and CALM datasets. Given the reported similarity between group-level manifolds of neurotypical individuals in CALM and NKI, it would be reasonable to expect that this combined origin should be close to the origin computed within neurotypical samples of either NKI or CALM. As a sanity check, I recommend reporting the distance of the combined neurotypical manifold origin to the centers of the neurotypical manifolds in each dataset. Moreover, if the manifold origin was constructed while utilizing all samples (including neurodivergent samples) I think this needs to be reconsidered.<br /> - Computation of SC-FC coupling: As noted in a previous comment, the explanation of this procedure is vague. The description lacks detail on the specific steps taken and differs from previous standard approaches in the field. I suggest clarifying the methodology and comparing with previous SC-FC coupling metrics.<br /> - Performing Procrustes transformation: The brief explanation in the first paragraph of page 30 does not provide enough information about the procedure or its justification. Since the Procrustes transformation alters the shape of individual gradients, it could artificially inflate consistency across development. I recommend including a rationale for using the Procrustes transformation and conducting a sensitivity analysis to assess its impact on the findings. Additionally, clarifying how exactly the transformation was applied to align gradients across hemispheres, individuals, and or datasets would help resolve ambiguity.

Insufficient Supporting Evaluations for Certain Claims:<br /> There are instances where additional analyses are necessary to substantiate the claims made in the manuscript. Without these evaluations, some conclusions may be premature or potentially misleading. I believe the following points need further analysis or, alternatively, adjustments to the claims:<br /> - Evaluating the Consistency of Gradients Across Development: The results shown in Fig. 1.e are used as evidence suggesting that gradients are consistent across ages. However, I believe additional analyses are required to identify potential sources of the observed inconsistency compared to previous works. The claim that the principal gradient explains a similar degree of variance across ages does not necessarily imply that the spatial structure of the gradient remains stable. The observed variance explanation is hence not enough to ascertain inconsistency with findings from Dong et al., as the spatial configuration of gradients may still change over time. Moreover, the introduction of the Procrustes transformation (not used by Dong et al.) further ambiguates the cause of this inconsistency. I suggest the following additional analyses to strengthen this claim: (1) Alignment to Group-Level Gradients: Assess how much of the variance in individual FC matrices is explained by each of the group-level gradients (G1, G2, and G3, for both FC and SC). This analysis could be visualized similarly to Fig. 1.e, with age on the x-axis and variance explained on the y-axis. If the explained variance varies as a function of age, it may indicate that the gradients are not as consistent as currently suggested. (2) For each individual's gradients (G1, G2, and G3, separately for FC and SC, without Procrustes transformation), evaluate their spatial similarity to the corresponding group-level gradients using a similarity metric (e.g., correlation coefficient). High spatial similarity, without a Procrustes transformation, would support the claim of stable gradient structures across development. On the other hand, if the similarities alter during development (e.g. such that at a certain age, individual G1 is less similar to group G1) this would contradict the stability of gradients during development. These additional analyses could potentially be included as additional panels in Fig. 1. In case significant deviations are observed, it might help refine the interpretation of the results and provide a more nuanced understanding of developmental changes in gradient organization.<br /> - Prediction vs. Association Analysis: The term "prediction" is used throughout the manuscript to describe what appear to be in-sample association tests. This terminology may be misleading, as prediction generally implies an out-of-sample evaluation where models trained on a subset of data are tested on a separate, unseen dataset. If the goal of the analyses is to assess associations rather than make true predictions, I recommend refraining from using the term "prediction" and instead clarifying the nature of the analysis. Alternatively, if prediction is indeed the intended aim (which would be more compelling), I suggest conducting the evaluations using a k-fold cross-validation framework. This would involve training the Generalized Additive Mixed Models (GAMMs) on a portion of the data and testing their predictive accuracy on a held-out sample (i.e., different individuals). Additionally, the current design appears to focus on predicting SC-FC coupling using cognitive or pathological dimensions. This is contrary to the more conventional approach of predicting behavioral or pathological outcomes from brain markers like coupling. Could the authors clarify why this reverse direction of analysis was chosen? Understanding this choice is crucial, as it impacts the interpretation and potential implications of the findings.

Methodological considerations<br /> - In typical applications of diffusion map embedding, sparsification (e.g., retaining only the top 10% of the strongest connections) is often employed at the vertex-level resolution to ensure computational feasibility. However, since the present study performs the embedding at the level of 200 brain regions (a considerably coarser resolution), this step may not be necessary or justifiable. Specifically, for FC, it might be more appropriate to retain all positive connections rather than applying sparsification, which could inadvertently eliminate valuable information about lower-strength connections. Whereas for SC, as the values are strictly non-negative, retaining all connections should be feasible and would provide a more complete representation of the structural connectivity patterns. Given this, it would be helpful if the authors could clarify why they chose to include sparsification despite the coarser regional resolution, and whether they considered this alternative approach (using all available positive connections for FC and all non-zero values for SC). It would be interesting if the authors could provide their thoughts on whether the decision to run evaluations at the resolution of brain regions could itself impact the functional and structural manifolds, their alteration with age, and or their stability (in contrast to Dong et al. which tested alterations in high-resolution gradients).

The Issue of Abstraction and Benefits of the Gradient-Based View:<br /> - The manuscript interprets the eccentricity findings as reflecting changes along the segregation-integration spectrum. Given this, it is unclear why a more straightforward analysis using established graph-theory measures of segregation-integration was not pursued instead. Mapping gradients and computing eccentricity adds layers of abstraction and complexity. If similar interpretations can be derived directly from simpler graph metrics, what additional insights does the gradient-based framework offer? While the manuscript argues that this approach provides "a more unifying account of cortical reorganization," it is not evident why this abstraction is necessary or advantageous over traditional graph metrics. Clarifying these benefits would strengthen the rationale for using this method.

Reviewer #2 (Public review):

Summary:

This study aims to show how structural and functional brain organization develops during childhood and adolescence using two large neuroimaging datasets. It addresses whether core principles of brain organization are stable across development, how they change over time, and how these changes relate to cognition and psychopathology. The study finds that brain organization is established early and remains stable but undergoes gradual refinement, particularly in higher-order networks. Structural-functional coupling is linked to better working memory but shows no clear relationship with psychopathology.

Strengths:

This study effectively integrates two different modalities (structural and functional) to identify shared patterns. It is supported by a relatively large dataset, which enhances its value and robustness.

Weaknesses:

General Comments:<br /> - The introduction is overly long and includes numerous examples that can distract readers unfamiliar with the topic from the main research questions.

- While the methods are thorough, it is not always clear whether the optimal approaches were chosen for each step, considering the available data.<br /> Detailed Comments:<br /> - The use of COMBAT may have excluded extreme participants from both datasets, which could explain the lack of correlations found with psychopathology.<br /> - Some differences in developmental trajectories between CALM and NKI (e.g., Figure 4d) are not explained. Are these differences expected, or do they suggest underlying factors that require further investigation?<br /> - There is no discussion of whether the stable patterns of brain organization could result from preprocessing choices or summarizing data to the mean. This should be addressed to rule out methodological artifacts.

Reviewer #1 (Public review):

Summary:

The study dissects distinct pools of diacylglycerol (DAG), continuing a line of research on the central concept that there is a major lipid metabolism DAG pool in cells, but also a smaller signaling DAG pool. It tests the hypothesis that the second pool is regulated by Dip2, which influences Pkc1 signaling. The group shows that stressed yeast increase specific DAG species C36:0 and 36:1, and propose this promotes Pkc1 activation via Pck1 binding 36:0. The study also examines how perturbing the lipid metabolism DAG pool via various deletions such as lro1, dga1, and pah1 deletion impacts DAG and stress signaling. Overall this is an interesting study that adds new data to how different DAG pools influence cellular signaling.

Strengths:

The study nicely combined lipidomic profiling with stress signaling biochemistry and yeast growth assays.

Weaknesses:

One suggestion to improve the study is to examine the spatial organization of Dip2 within cells, and how this impacts its ability to modulate DAG pools. Dip2 has previously been proposed to function at mitochondria-vacuole contacts (Mondal 2022). Examining how Dip2 localization is impacted when different DAG pools are manipulated such as by deletion Pah1 (also suggested to work at yeast contact sites such as the nucleus-vacuole junction), or with Lro1 or Dga1 deletion would broaden the scope of the study.

Reviewer #2 (Public review):

Summary:

The authors use yeast genetics, lipidomic and biochemical approaches to demonstrate the DAG isoforms (36:0 and 36:1) can specifically activate PKC. Further, these DAG isoforms originate from PI and PI(4,5)P2. The authors propose that the Psi1-Plc1-Dip2 functions to maintain a normal level of specific DAG species to modulate PKC signalling.

Strengths:

Data from yeast genetics are clear and strong. The concept is potentially interesting and novel.

Weaknesses:

More evidence is needed to support the central hypothesis. The authors may consider the following:

(1) Figure 2: the authors should show/examine C36:1 DAG. Also, some structural evidence would be highly useful here. What is the structural basis for the assertion that the PKC C1 domain can only be activated by C36:0/1 DAG but not other DAGs? This is a critical conclusion of this work and clear evidence is needed.

(2) Does Dip2 colocalize with Plc1 or Pkc1? Does Dip2 reach the plasma membrane upon Plc activation?

Reviewer #1 (Public review):

Summary:

This manuscript by Alonso-Caraballo et al, is a novel piece of work that examines the impact of oxycodone self-administration on neural plasticity within the paraventricular thalamic (PVT) to nucleus accumbens shell (Shell) pathway - two regions shown to play a key role in cue-induced drug seeking on their own, and whether this plasticity varies based on abstinence period and biological sex.

Strengths:

The authors show using a clinically relevant long-access model of opioid self-administration promotes dependence and acute withdrawal in both male and female rats. During subsequent cue-induced relapse tests at 1 or 14 days following the conclusion of self-administration, data show that while both males and females demonstrate drug-seeking behavior at both time points, females show a further elevation in responding on day 14 versus day 1 which is not observed in the males. When accounting for past work showing elevations in drug-seeking in males after 30 days, these data indicate that craving-induced relapse for opioids may develop faster and may be more pronounced in females compared to males.

These behavioral findings were paralleled by the use of ex vivo acute slice electrophysiology and circuit-specific ex vivo optogenetics to examine the impact of oxycodone self-administration on synaptic strength within the paraventricular thalamus (PVT) to nucleus accumbens shell (NAcSh) pathway(s). Data support a time-dependent but sex-independent strengthening of glutamatergic signaling at PVT-to-NAcSh medium spiny neurons (MSNs) that is only present following a relapse test at 14 days post abstinence in males versus females, providing the first evidence that opioid self-administration and/or cue-induced drug-seeking augments this pathway. Using an extensive set of physiological measures, the authors show that this increased synaptic strength reflects an upregulation of presynaptic release probability. Further, this upregulation of excitatory signaling aligned temporally with an increase in MSN excitability, as assessed by increases in action potential firing frequency. Finally, the authors provide the first evidence that similar to other inputs to the NAcSh, PVT projections innervate both MSN as well as local interneurons, promoting a GABA-A-specific feedforward inhibitory circuit. Interestingly, unlike direct excitatory inputs to MSNs, no changes were observed ostensibly within this feedforward circuit, highlighting a selective enhancement of excitatory drive and output of MSNs with protracted abstinence.

Overall, these data highlight a potential role for heightened synaptic strength within the PVT-NAcSh pathway in cue-induced relapse behavior during protracted abstinence and identify a potential therapeutic target during abstinence to reduce relapse risk in abstaining individuals.

Weaknesses:

Overall, the experimental approach and data provided appear rigorous and support their overall conclusions and achieve their goal of understanding how opioid self-administration impacts synaptic strength within the PVT-NAcSh pathway. Although not undermining these data, there are a few potential weaknesses that reduce the impact of the work. For example, the inability to directly assess whether cue-induced drug-seeking is in fact augmented compared to daily intake during self-administration in the maintenance face only permits the authors to denote that reexposure to cues and the context is sufficient to promote active lever pressing without demonstrating whether seeking behavior is in fact elevated further during a cue test. This is notably understandable as drug available sessions were 6-hours versus a 1-hour relapse test. Importantly, it is clearly demonstrated that drug seeking is higher on average in female mice after 14 days versus 1 day.

With regard to the interpretation of electrophysiology findings, the lack of inclusion of an abstinence-only group does not permit interpretations to parse out whether observed increases in synaptic strength (or the lack of) reflect abstinence or an interaction between abstinence period and re-exposure to the operant chamber, as slices were taken 30-45 min post relapse test. While much literature has shown that drug-induced adaptations in the NAc require a post-drug period for plasticity to measurably emerge, studies have also shown that re-exposure to heroin-associated cues following abstinence seemingly "reverses" increases in cell excitability in prelimbic-NAc pyramidal neurons (Kokane et al., 2023) and that depotentiation of morphine-induced increases in synaptic strength in the NAc shell can be depotentiated by drug re-exposure - an effect also observed with cocaine re-exposure (Madayag et al., 2019). Notably, the lack of effect at 14 but not 1 day supports the likelihood that the relapse test does not in fact influence the plasticity within the PVT-NAcSh circuit.

While the lack of effect on AMPAR:NMDAR ratio and rectification indices do support the notion that enhanced EPSC amplitudes in input-output curves do not reflect a change in AMPAR subunit expression (i.e., increased GluA2-lacking receptors that exhibit inward rectification at depolarized potential) nor a change in postsynaptic sensitivity to glutamate, without direct assessment of AMPAR-specific and NMDAR-specific input-output curves, it doesn't definitively exclude the possibility that both AMPA and NMDA receptor currents are being upregulated, thus negating an observable change in postsynaptic strength.

Overall, these findings provide novel insight into how the PVT-NAcSh pathway is altered by opioid self-administration and whether this is unique based on abstinence period and sex. Importantly, these were the primary objectives stated by the author. Data highlight a potential role for the observed adaptations in relapse behavior and identify a potential therapeutic target during abstinence to reduce relapse risk in abstaining individuals. However, it should be noted that no causal link is demonstrated without experiments to reduce/prevent relapse.

Reviewer #2 (Public review):

This is an interesting paper from Alonso-Caraballo and colleagues that examines the influence of opioid use, abstinence, and sex on paraventricular thalamus (PVT) to nucleus accumbens shell (NAcSh) medium spiny neurons circuit physiology. The authors first find that prolonged abstinence from extended access to oxycodone self-administration leads to profoundly increased cue-induced reinstatement in females. Next, they found that prolonged abstinence increased PVT-NAcSh MSN synaptic strength, an effect that was likely due to presynaptic adaptation (paired-pulse ratio was decreased in both sexes).

While this paper is certainly interesting, and well-written, and the experiments seem to be well performed, the behavioral and physiological effects observed are somewhat divorced. Specifically, what accounts for the heightened relapse in females? Since no opioid-related sex differences were observed in PVT-NAcSh neurophysiology, it is unclear how the behavioral and neurophysiological data fit together. Furthermore, the lack of functional manipulation of PVT-NAcSh circuitry leaves one to wonder if this circuit is even important for the behavior that the authors are measuring. I would be more positive about this study if the authors were able to resolve either of the two issues noted above.

I also noted more moderate weaknesses that the authors should consider:

(1) There are insufficient animals in some cases. For example, in Figure 4, the Male Saline 14-day abstinence group (n = 3 rats) has less than half of the excitability as compared to the Male Saline 1-day abstinence group (n = 7 rats). This is likely due to variance between animals and, possibly, oversampling. Thus, more rats need to be added to the 14-day abstinence group. Additionally, the range of n neurons/rat should be reported for each experiment to ensure readers that oversampling from single animals is not occurring.

(2) The IPSC data, for example in Figure 4, is one of the more novel experiments in the manuscript. However, it is quite challenging to see the difference between males and females, saline and oxycodone, at low stimulation intensities within the graph. Authors should expand this so that reviewers/readers can see those data, especially considering other work suggesting that PVT synaptic input onto select NAc interneurons is disrupted following opioid self-administration. Additional comment: It's also interesting that the IPSC amplitude seems to be maximal at ~2mW of light, whereas ~11 mW is required to evoke maximal EPSC amplitude. It would be interesting to know the authors' thoughts on why this may be.

(3) There is an inadequate description of what has been done to date on the PVT-NAc projection regarding opioid withdrawal, seeking, disinhibition, and the effects on synaptic physiology therein. For example, a critical paper, Keyes et al., 2020 Neuron, is not cited. Additionally, Paniccia et al., 2024 Neuron is inaccurately cited and insufficiently described. Both manuscripts should be described in some detail within the introduction, and the findings should be accurately contextualized within the broader circuit within the discussion.

(4) Related to the above, the authors should provide a more comprehensive description of how PVT synapses onto cell-type specific neurons in the NAc which expands beyond MSNs, especially considering that PVT has been shown to influence drug/opioid seeking through the innervation of NAc neurons that are not MSNs. For example, see PMIDs 33947849, 36369508, 28973852, 38141605.

Reviewer #3 (Public review):

Summary:

In this paper, Alonso-Caraballo et al. investigate sex-specific differences in oxycodone self-administration, withdrawal, and relapse behaviors in rats, as well as associated synaptic plasticity in the paraventricular thalamus to nucleus accumbens shell (PVT-NAcSh) circuit. The authors employ a combination of behavioral paradigms and ex vivo electrophysiology to examine how acute (1-day) and prolonged (14-day) abstinence from oxycodone self-administration affect cue-induced drug-seeking and synaptic transmission in male and female rats. Their findings reveal that while both sexes show similar oxycodone self-administration and acute withdrawal symptoms, females exhibit enhanced cue-induced relapse after prolonged abstinence. Furthermore, they show that prolonged abstinence is associated with increased synaptic strength in the PVT-NAcSh circuit (reduced paired-pulse ratio) and enhanced intrinsic excitability of NAcSh medium spiny neurons in both sexes. This study provides important insights into the sex-specific neural adaptations that may underlie vulnerability to opioid relapse and highlights the PVT-NAcSh circuit as a potential target for therapeutic interventions. However, although this study is well designed, no sex differences were observed in the synaptic activity within this pathway that could explain increased oxycodone seeking in females versus male rats. Additional experiments could strengthen the results and help clarify synaptic mechanisms underpinning behavioral sex differences.

Strengths:

The study exhibits several strengths. It provides a comprehensive behavioral analysis of oxycodone self-administration, withdrawal, and cue-induced relapse in both male and female rats at different time points (acute vs. protracted withdrawal) offering valuable insights into sex-specific differences (i.e., increased oxycodone seeking in females over time but not males). The authors examine synaptic plasticity in the PVT-NAcSh circuit at different abstinence time points, integrating behavioral and electrophysiological data to link circuit adaptations with relapse behaviors, although no sex differences in the electrophysiological parameters examined were evident. The investigation of intrinsic excitability changes in NAcSh medium spiny neurons further enhances the study's depth. Overall, the well-designed experiments provide important insights into the neural adaptations that may underlie vulnerability to opioid relapse, highlighting the PVT-NAcSh circuit as a potential target for therapeutic interventions in opioid use disorder.

Weaknesses:

Despite its strengths, the study has several notable limitations. A key weakness is the lack of observed sex differences in synaptic activity within the PVT-NAcSh pathway that could explain the behavioral results. The authors' failure to differentiate between D1 and D2 medium spiny neurons (MSNs) in the nucleus accumbens represents a missed opportunity to identify potential sex-specific differences at the cellular level, although they do discuss reasons for this omission. The only significant synaptic change observed - reduced paired-pulse ratio indicating increased synaptic strength - occurs in both males and females, failing to explain the sex-specific behavioral differences. Furthermore, the investigation of intrinsic excitability in NAc MSNs adds complexity to data interpretation, as the authors neither differentiate between D1 and D2 MSNs nor confirm that recorded neurons receive direct inputs from the PVT. This assumption potentially confounds the results. Overall, while the study provides valuable insights, additional experiments targeting specific cell populations and more detailed synaptic analyses are needed to elucidate the mechanisms underlying the observed behavioral sex differences in opioid relapse vulnerability.

Reviewer #1 (Public review):

In this manuscript, the role of orexin receptors in dopamine transmission is studied. It extends previous findings suggesting an interplay between these two systems in regulating behaviour by first characterizing the expression of orexin receptors in the midbrain and then disrupting orexin transmission in dopaminergic neurons by deleting its predominant receptor, OX1R (Ox1R fl/fl, Dat-Cre tg/wt mice). Electrophysiological and calcium imaging data suggest that orexin A acutely and directly stimulates SN and VTA dopaminergic neurons but does not seem to induce c-Fos expression. Behavioral effects of depleting OX1R from dopaminergic neurons include enhanced novelty-induced locomotion and exploration, relative to littermate controls (Ox1R fl/fl, Dat-Cre wt/wt). However, no difference between groups is observed in tests that measure reward processing, anxiety, and energy homeostasis. To test whether the depletion of OX1R alters overall orexin-triggered activation across the brain, PET imaging is used in OX1R∆DAT knockout and control mice. This analysis reveals that several regions show higher neuronal activation after orexin injection in OX1R∆DAT mice, but the authors focus their follow-up study on the dorsal bed nucleus of the stria terminalis (BNST) and lateral paragigantocellular nucleus (LPGi). Dopaminergic inputs and expression of dopamine receptors type-1 and -2 (DRD1 & DRD2) are assessed and compared to control demonstrating a moderate decrease in DRD1 and DRD2 expression in the BNST of OX1R∆DAT mice and unaltered expression of DRD2, with absence of DRD1 expression in LPGi of both groups. Overall, this study is valuable for the information it provides on orexin receptor expression and function in behaviour, as well as for the new tools it generated for the specific study of this receptor in dopaminergic circuits.

Strengths:

The use of a transgenic line that lacks OX1R in dopamine-transporter expressing neurons is a strong approach to dissect the direct role of orexin in modulating dopamine signaling in the brain. The battery of behavioral assays used to study this line provides valuable information for researchers interested in the interplay between dopamine and orexin systems and their role in animal physiology.

Weaknesses:

This study falls short in providing evidence for an anatomical substrate and mechanism underlying the altered behavior observed in mice lacking orexin receptor subtype 1 in dopaminergic neurons. How orexin transmission in dopaminergic neurons regulates the expression of postsynaptic dopamine receptors (as observed in the BNST of OX1R∆DAT mice) is an intriguing question not addressed in this study. An important aspect not investigated in this study is whether the disruption of orexin activity affects dopamine release in target areas.

Reviewer #2 (Public review):

Summary:

This manuscript examines expression of orexin receptors in midbrain - with a focus on dopamine neurons - and uses several fairly sophisticated manipulation techniques to explore the role of this peptide neurotransmitter in reward-related behaviors. Specifically, in situ hybridization is used to show that substantia nigra dopamine neurons predominantly express orexin receptor 1 subtype and then go on to delete this receptor in dopamine transporter-expressing neurons using a transgenic strategy. Ex vivo calcium imaging of midbrain neurons is used to show that, in the absence of this receptor, orexin is no longer able to excite dopamine neurons of the substantia nigra.

The authors proceed to use this same model to study the effect of orexin receptor 1 deletion on a series of behavioral tests, namely, novelty-induced locomotion and exploration, anxiety-related behavior, preference for sweet solutions, cocaine-induced conditioned place preference, and energy metabolism. Of these, the most consistent effects are seen in the tests of novelty-induced locomotion and exploration in which the mice with orexin 1 receptor deletion are observed to show greater levels of exploration, relative to wild-type, when placed in a novel environment, an effect that is augmented after icv administration of orexin.

In the final part of the paper, the authors use PET imaging to compare brain-wide activity patterns in the mutant mice compared to wildtype. They find differences in several areas both under control conditions (i.e., after injection of saline) as well as after injection of orexin. They focus in on changes in dorsal bed nucleus of stria terminalis (dBNST) and the lateral paragigantocellular nucleus (LPGi) and perform analysis of the dopaminergic projections to these areas. They provide anatomical evidence that these regions are innervated by dopamine fibers from midbrain, are activated by orexin in control, but not mutant mice, and that dopamine receptors are present. They also show changes in receptor expression in the transgenic mice. Thus, they argue these anatomical data support the hypothesis that behavioral effects of orexin receptor 1 deletion in dopamine neurons are due to changes in dopamine signaling in these areas.

Strengths:

Understanding how orexin interacts with the dopamine system is an important question and this paper contains several novel findings along these lines. Specifically:<br /> (1) Distribution of orexin receptor subtypes in VTA and SN is explored thoroughly.<br /> (2) Use of the genetic model that knocks out a specific orexin receptor subtype from dopamine-transporter-expressing neurons is a useful model and helps to narrow down the behavioral significance of this interaction.<br /> (3) PET studies showing how central administration of orexin evokes dopamine release across the brain is intriguing, especially since two key areas are pursued - BNST and LPGi - where the dopamine projection is not as well described/understood.

Weaknesses:

The role of the orexin-dopamine interaction is not explored in enough detail. The manuscript presents several related findings, but the combination of anatomy and manipulation studies do not quite tell a cogent story. Ideally, one would like to see the authors focus on a specific behavioral parameter and show that one of their final target areas (dBNST or LPGi) was responsible or at least correlated with this behavioral readout. In addition, the authors' working model for how they think orexin-dopamine interactions contribute to behavior under normal physiological conditions is not well-described.

Reviewer #1 (Public review):

Summary:

This study sought to reveal the potential roles of m6A RNA methylation in gene dosage regulatory mechanisms, particularly in the context of aneuploid genomes in Drosophila. Specifically, this work looked at the relationships between expression of m6A regulatory factors, RNA methylation status, classical and inverse dosage effects, and dosage compensation. Using RNA sequencing and m6A mapping experiments, an in depth analysis was performed to reveal changes in m6A status and expression changes across multiple aneuploid Drosophila models. The authors propose that m6A methylation regulates MOF and, in turn, deposition of H4K16Ac, critical regulators of gene dosage in the context of genomic imbalance.

Strengths:

This study seeks to address an interesting question with respect to gene dosage regulation and the possible roles of m6A in that process. Previous work has linked m6A to X-inactivation in humans through the Xist lncRNA, and to the regulation of the Sxl in flies. This study seeks to broaden that understanding beyond these specific contexts to more broadly understand how m6A impacts imbalanced genomes in other contexts.

Weaknesses:

The methods being used particularly for analysis of m6A at both the bulk and transcript-specific level are not sufficiently specific or quantitative to be able to confidently draw the conclusions the authors seek to make. MeRIP m6A mapping experiments can be very valuable, but differential methylation is difficult to assess when changes are small (as they often are, in this study but also m6A studies more broadly). For instance based on the data presented and the methods described, it is not clear that the statement that "expression levels at m6A sites in aneuploidies are significantly higher than that in wildtype" is supported. In my initial review I pointed out that MeRIP experiments are not quantitative and can be difficult to interpret when small changes are present. The data as presented still show only RPKM in IP samples, and the text alludes to changes in IP enrichment that are significant but the data do not appear to have been included in the figure. Concerns about the bulk-level m6A measurements also remain, as the new data showing m6A levels in mRNA show changes that are even smaller than those initially demonstrated in total RNA. Yet the data are still presented as significant, biologically relevant changes. The conclusions about mRNA m6A levels are not strengthened by measurements.

Reviewer #2 (Public review):

Summary:

The authors have tested effects of partial- or whole-chromosome aneuploidy on the m6A RNA modification in Drosophila. The data reveal that overall m6A levels trend up but that the number of sites found by meRIP-seq trend down, which seems to suggest that aneuploidy causes a subset of sites become hyper-methylated. Subsequent bioinformatic analysis of other published datasets establish correlations between activity of the H4K16 acetyltransferase dosage compensation complex (DCC) and expression of m6A components and m6A abundance, suggesting that DCC and m6A can act in a feedback loop. Western blots confirm that Msl2 and MOF alleles alter levels of Mettl3 complex components, but the underlying mechanism remains undefined.

Strengths:

• Thorough bioinformatic analysis of their data<br /> • Incorporation of other published datasets that enhances scope and rigor<br /> • Finds trends that suggest that a chromosome counting mechanism can control m6A, as fits with pub data that the Sxl mRNA is m6A modified in XX females and not XY males<br /> • Provides preliminary evidence that this counting mechanism may be due to DCC effects on expression of m6A components.

Weaknesses:

• The linkage between H4K16 machinery and m6A levels on specific sites remains unclear in this revision.<br /> • The paper relies on m6A comparisons across tissues and developmental stages, which introduces some uncertainty about where and when the DCC-m6A loop acts.

Reviewer #1 (Public review):

Summary:

How reconsolidation works - particularly in humans - remains largely unknown. With an elegant, 3-day design, combining fMRI and psychopharmacology, the authors provide evidence for a certain role for noradrenaline in the reconsolidation of memory for neutral stimuli. All memory tasks were performed in the context of fMRI scanning, with additional resting state acquisitions performed before and after recall testing on Day 2. On Day 1, 3 groups of healthy participants encoded word-picture associates (with pictures being either scenes or objects) and then performed an immediate cued recall task to presentation of the word (answering is the word old or new, and was it paired with a scene or an object). On Day 2, the cued recall task was repeated using half of the stimulus set words encoded on Day 1 (only old words were presented, with subjects required to indicate prior scene vs object pairing). This test was immediately preceded by the oral administration of placebo, cortisol, or yohimibine (to raise noradrenaline levels) depending on group assignment. On Day 3, all words presented on Day 1 were presented. As expected, on Day 3, memory was significantly enhanced for associations that were cued and successfully retrieved on Day 2 compared to uncued associations. However, for associative d', there was no Cued × Group interaction nor a main effect of Group, i.e., on the standard measure of memory performance, post-retrieval drug presence on Day 2 did not affect memory reconsolidation. As further evidence for a null result, fMRI univariate analyses showed no Cued × Group interactions in whole-brain or ROI activity.

Strengths:

There are some aspects of this study that I find impressive. The study is well-designed and the fMRI analysis methodology innovative and sound. The authors have made meticulous and thorough physiological measurements, and assays of mood, throughout the experiment. By doing so, they have overcome, to a considerable extent, the difficulties inherent in timing of human oral drug delivery in reconsolidation tasks, where it is difficult to have drug present in the immediate recall period without affecting recall itself. This is beautifully shown in Fig. 3. I also think that having some neurobiological assay of memory reactivation when studying reconsolidation in humans is critical, and the authors provide this. While multi-voxel patterns of hemodynamic responses are, in my view, very difficult to equate with an "engram", these patterns do have something to do with memory.

Weaknesses:

I have major issues regarding the behavioral results and the framing of the manuscript:

(1) To arrive at group differences in memory performance, the authors performed median splitting of Day 3 trials by short and long reaction times during memory cueing on Day 2, as they took this as a putative measure of high/low levels of memory reactivation. Associative category hits on Day 3 showed a Group by Day 2 Reaction time (short, long) interaction, with post-hocs showing (according to the text) worse memory for short Day 2 RTs in the yohimbine group. These post-hocs should be corrected for multiple comparisons, as the result is not what would be predicted (see point 2). My primary issue here is that we are not given RT data for each group, nor is the median splitting procedure described in the methods. Was this across all groups, or within groups? Are short RTs in the yohimbine group any different from short RTs in the other two groups? Unfortunately, we are not given Day 2 picture category memory levels or reaction times for each group. This is relevant because (as given in Supplemental Table S1) memory performance (d´) for the Yohimbine group on Day 1 immediate testing is (roughly speaking) 20% lower than the other 2 groups (independently of whether the pairs will be presented again the following day). I appreciate that this is not significant in a group x performance ANOVA but how does this relate to later memory performance? What were the group-specific RTs on Day 1? So, before the reader goes into the fMRI results, there are questions regarding the supposed drug-induced changes in behavior. Indeed, in the discussion, there is repeated mention of subsequent memory impairment produced by yohimbine but the nature of the impairment is not clear.

This weakness was satisfactorily addressed in one revision round. As RT data are often not normally distributed, were they transformed prior to entry into linear models?

(2) The authors should be clearer as to what their original hypotheses were, and why they did the experiment. Despite being a complex literature, I would have thought the hypotheses would be reconsolidation impairment by cortisol and enhancement by yohimbine. Here it is relevant to point out that - only when the reader gets to the Methods section - there is mention of a paper published by this group in 2024. In this publication, the authors used the same study design but administered a stress manipulation after Day 2 cued recall, instead of a pharmacological one. They did not find a difference in associative hit rate between stress and control groups, but - similar to the current manuscript - reported that post-retrieval stress disrupts subsequent remembering (Day 3 performance) depending on neural memory reinstatement during reactivation (specifically driven by the hippocampus and its correlation with neocortical areas).

Instead of using these results, and other human studies, to motivate the current work, reference is made to a recent animal study: Line 169 "Building on recent findings in rodents (Khalaf et al. 2018), we hypothesized that the effects of post-retrieval noradrenergic and glucocorticoid activation would critically depend on the reinstatement of the neural event representation during retrieval". It is difficult to follow that a rodent study using contextual fear conditioning and examining single neuron activity to remote fear recall and extinction would be relevant enough to motivate a hypothesis for a human psychopharmacological study on emotionally neutral paired associates.

Minor comments<br /> - Related to Major issue 2. In the introduction, it would be helpful to be specific about the type of memory being probed in the different studies referenced (episodic vs conditioning). For the former, please make it clear whether stimuli to be remembered were emotional or neutral, and for which stimulus class drug effects were observed. This is particularly important given that in the first paragraph you describe memory reactivation in the context of traumatic memories via mention of PTSD. It would also be helpful to know to which species you refer. For example, in line 115, "timing of drug administration..." a rodent and a human study are cited.

This weakness was addressed in one revision round, resulting in an excellent introduction, highlighting the importance of studying post-retrieval effects for memory researchers and healthcare workers.

Reviewer #2 (Public review):

Summary:

The authors aimed to investigate how noradrenergic and glucocorticoid activity after retrieval influence subsequent memory recall with a 24-hour interval, by using a controlled three-day fMRI study involving pharmacological manipulation. They found that noradrenergic activity after retrieval selectively impairs subsequent memory recall, depending on hippocampal and cortical reactivation during retrieval.

Overall, there are several significant strengths for this well-written manuscript.

Reviewer #1 (Public review):

Summary:

Jin, Briggs and colleagues use light sheet imaging to reconstruct the islet three-dimensional Ca2+ network. The authors find that early/late responding (leader) cells are dynamic over time, and located at the islet periphery. By contrast, highly connected or hub cells are stable, and located toward the islet center. Suggesting that the two subpopulations are differentially regulated by fuel input, glucokinase activation only influences leader cell phenotype, whereas hubs remain stable.

Strengths:

The studies are novel in providing the first three-dimensional snapshot of the beta cell functional network, as well as determining the localization of some of the different subpopulations identified to date. The studies also provide some consensus as to the origin, stability and role of such subpopulations in islet function.

Weaknesses:

Experiments with metabolic enzyme activators do not take into account the influence of cell viability on the observed Ca2+ network data. Limitations of the imaging approach used need to be recognised and evaluated/discussed.

Comments on revisions:

The authors have addressed the majority of the points raised.

Reviewer #2 (Public review):

The manuscript by Erli Jin and Jennifer Briggs et al. utilizes light sheet microscopy to image islet beta cell calcium oscillations in 3D and determine where beta cell populations are located that begin and coordinate glucose-stimulated calcium oscillations. The light sheet technique allowed clear 3D mapping of beta cell calcium responses to glucose, glucokinase activation, and pyruvate kinase activation. The manuscript finds that synchronized beta-cells are found at the islet center, that leader beta cells showing the first calcium responses are located on the islet periphery, that glucokinase activation helped maintain beta cells that lead calcium responses, and that pyruvate kinase activation primarily increases islet calcium oscillation frequency. The study is well-designed, contains a significant amount of high quality data, and the conclusions are largely supported by the results.

Comments on revisions:

The manuscript by Erli Jin et al. has been improved with the revisions, which have addressed my previous concerns. The manuscript significantly improves the mechanistic underpinnings of islet calcium oscillations and resulting pulsatile insulin secretion.

Reviewer #3 (Public review):

Summary:

Jin, Briggs et al. made use of light-sheet 3D imaging and data analysis to assess the collective network activity in isolated mouse islets. The major advantage of using whole islet imaging, despite compromising on a speed of acquisition, is that it provides a complete description of the network, while 2D networks are only an approximation of the islet network. In static-incubation conditions, excluding the effects of perfusion, they assessed two subpopulations of beta cells and their spatial consistency and metabolic dependence.

Strengths:

The authors confirmed that coordinated Ca2+ oscillations are important for glycemic control. In addition, they definitively disproved the role of individual privileged cells, which were suggested to lead or coordinate Ca²⁺ oscillations. They provided evidence for differential regional stability, confirming the previously described stochastic nature of the beta cells that act as strongly connected hubs as well as beta cells in initiating regions (doi.org/10.1103/PhysRevLett.127.168101). This has not been a surprise to the reviewer.

The fact that islet cores contain beta cells that are more active and more coordinated has also been readily observed in high-frequency 2D recordings (e.g. DOI: 10.2337/db22-0952), suggesting that the high-speed capture of fast activity can partially compensate for incomplete topological information.

They also found an increased metabolic sensitivity of mantle regions of an islet with subpopulation of beta cells with a high probability of leading the islet activity and which can be entrained by fuel input. They discuss a potential role of alpha/delta cell interaction, however relative lack of beta cells in the islet border region could also be a factor contributing to less connectivity and higher excitability.

The Methods section contains a useful series of direct instructions on how to approach fast 3D imaging with currently available hardware and software.

The Discussion is clear and includes most of the issues regarding the interpretation of the presented results.

Taken together it is a strong technical paper to demonstrate the stochasticity regarding the functions subpopulations of beta cells in the islets may have and how less well-resolved approaches (both missing spatial resolution as well as missing temporal resolution) led us to jump to unjustified conclusions regarding the fixed roles of individual beta cells within an islet.

Weaknesses:

There are a few relevant issues that need to be addressed.

(1) The study is not internally consistent regarding the Results section. In the text the authors discuss changes in membrane potential (not been measured in this study), while in the figures they exclusively describe Ca2+ oscillations (which were measured). Examples are on lines 149, 150, 153, 154, 263... It is recommended that the silent and active phase in the Results section describe processes actually measured in this study as shown 6A.

(2) There are in fact no radially oriented networks in the core of an islet (l. 130, Fig. 4) apart from the fact that every hub has somewhat radially oriented edges. For radiality to have some general meaning, the normalized distance from the geometric center would need to be lower than 0.4. The networks are centrally located, which does not change the major conclusions of the study.

(3) The study would profit from acknowledging that Ca2+ influx is not a sole mechanism to drive insulin secretion and that KATP channels are not the sole target sensitive to changes in the cytosolic (global or local) ADP and ATP concentration or that there is an absolute concentration-dependence of these ligands on KATP channels. The relatively small conductance changes that have been found associated to active and silent phases (closing and opening of the KATP channels as interpreted by the authors, respectively, doi: 10.1152/ajpendo.00046.2013) and should be due to metabolic factors, could be also associated to desensitization of KATP channels to ATP due to the increase in cytosolic Ca2+ changes after intracellular Ca2+ flux (DOI: 10.1210/endo.143.2.8625) as they have been found to operate also at time scales, significantly faster (DOI: 10.2337/db22-0952) than reported before (refs. 21,22). Metabolic changes influence intracellular Ca2+ flux as well.

(4) There is no explanation for why KL divergence is so different between the pre-test regional consistency of the islets used to test the vehicle compared to those where GKa and PKa have been tested.

Reviewer #1 (Public review):

SARS-CoV-2 encodes a macrodomain (Mac1) within the nsp3 protein that removes ADP-ribose groups from proteins. However, its role during infection is not well understood. Evidence suggests that Mac1 antagonizes the host interferon response by counteracting the wave of ADP ribosylation that occurs during infection. Indeed, several PARPs are interferon-stimulated genes. While multiple targets have been proposed, the mechanistic links between ADP ribosylation and a robust antiviral response remain unclear.

Genetic inactivation of Mac1 abrogates viral replication in vivo, suggesting that small-molecule inhibitors of Mac1 could be developed into antivirals to treat COVID-19 and other emerging coronaviruses. The authors report a potent and selective small molecule inhibitor targeting Mac1 (AVI-4206) that demonstrates efficacy in human airway organoids and animal models of SARS-CoV-2 infection. While these results are compelling and provide proof of concept for the therapeutic targeting of Mac1, I am particularly intrigued by the potential of this compound as a probe to elucidate the mechanistic connections between infection-induced ADP ribosylation and the host antiviral response.

The precise function of Mac1 remains unclear. Given its presence in multiple viruses, it likely acts on a fundamental host immune pathway(s). AVI-4206, while promising as a lead compound for the development of antivirals targeting coronaviruses, could also be a valuable tool for uncovering the function of the Mac1 domain. This may lead to fundamental insights into the host immune response to viral infection.

Reviewer #2 (Public review):

Summary:

The authors describe the development of a novel inhibitor (AVI-4206) for the first macrodomains of the nsp3 protein of SARS-CoV-2 (Mac1). This involves both medical chemical synthesis, structural work as well as biochemical characterisation. Subsequently, the authors present their findings of the efficacy of the inhibitor both on cell culture, as well as animal models of SARS-CoV-2 infection. They find that despite high affinity for Mac1 and the known replicatory defects of catalytically inactive Mac1 only moderate beneficial effects can be observed in their chosen models.

Strengths:

The authors employ a variety of different assay to study the affinity, selectivity and potency of the novel inhibitor and thus the in vitro data are very compelling.<br /> Similarly, the authors use several cell culture and in vivo models to strengthen their findings.

Weaknesses:

(a) The selection of Targ1 and MacroD2 as off-target human macrodomains is poor as several studies have shown that the first macrodomains of PARP9 and PARP14 are much closer related to coronaviral macrodomains and both macrodomains are implicated in antiviral defence and immunity.

(b) The authors utilize only replication efficiency and general infection markers as read out for their Mac1 inhibitor. It would be good if they could show impact on the ADP-ribosylation of a known Mac1 target such as PARP14.

Reviewer #3 (Public review):

Summary:

The authors were trying to validate SARS-CoV-2 Mac1 as a drug discovery target and by extension other viral macrodomains.

Strengths:

The medicinal chemistry and structure based optimization is exemplary. Macrodomains and ADPribosyl hydrolases have a reputation for being undruggable, yet the authors managed to optimize hits from a fragment screen using structure based approaches and fragment linking to make a 20nM inhibitor as a tool compound to validate the target.<br /> In addition, the in vivo work is also a strength. The ability to reduce the viral count at a rate comparable to nirmatrelvir is impressive. Tracking the cytokine expression levels also supports much of the genetic data and mechanism of action for macrodomains.

Weaknesses:

The main compound AVI-4206, while being very potent and selective is not appreciably orally bioavailable. The fact that they have to use high doses of the compound IP to see in vivo effects may lead to questions regarding off target effects.

The cellular models are not as predictive of antiviral activity as one would expect. However, the authors had enough chutzpah to test the compound in vivo knowing that cellular models might not be an accurate representation of a living system with a fully functional immune system all of which is most likely needed in an antiviral response to test the importance of Mac1 as a target.

Reviewer #1 (Public review):

Summary:

In this paper, the authors develop a biologically plausible recurrent neural network model to explain how the hippocampus generates and uses barcode-like activity to support episodic memory. They address key questions raised by recent experimental findings: how barcodes are generated, how they interact with memory content (such as place and seed-related activity), and how the hippocampus balances memory specificity with flexible recall. The authors demonstrate that chaotic dynamics in a recurrent neural network can produce barcodes that reduce memory interference, complement place tuning, and enable context-dependent memory retrieval, while aligning their model with observed hippocampal activity during caching and retrieval in chickadees.

Strengths:

(1) The manuscript is well-written and structured.<br /> (2) The paper provides a detailed and biologically plausible mechanism for generating and utilizing barcode activity through chaotic dynamics in a recurrent neural network. This mechanism effectively explains how barcodes reduce memory interference, complement place tuning, and enable flexible, context-dependent recall.<br /> (3) The authors successfully reproduce key experimental findings on hippocampal barcode activity from chickadee studies, including the distinct correlations observed during caching, retrieval, and visits.<br /> (4) Overall, the study addresses a somewhat puzzling question about how memory indices and content signals coexist and interact in the same hippocampal population. By proposing a unified model, it provides significant conceptual clarity.

Weaknesses:

The recurrent neural network model incorporates assumptions and mechanisms, such as the modulation of recurrent input strength, whose biological underpinnings remain unclear. The authors acknowledge some of these limitations thoughtfully, offering plausible mechanisms and discussing their implications in depth.

One thread of questions that authors may want to further explore is related to the chaotic nature of activity that generates barcodes when recurrence is strong. Chaos inherently implies sensitivity to initial conditions and noise, which raises questions about its reliability as a mechanism for producing robust and repeatable barcode signals. How sensitive are the results to noise in both the dynamics and the input signals? Does this sensitivity affect the stability of the generated barcodes and place fields, potentially disrupting their functional roles? Moreover, does the implemented plasticity mitigate some of this chaos, or might it amplify it under certain conditions? Clarifying these aspects could strengthen the argument for the robustness of the proposed mechanism.

It may also be worth exploring the robustness of the results to certain modeling assumptions. For instance, the choice to run the network for a fixed amount of time and then use the activity at the end for plasticity could be relaxed.

Reviewer #2 (Public review):

Summary:

Striking experimental results by Chettih et al 2024 have identified high-dimensional, sparse patterns of activity in the chickadee hippocampus when birds store or retrieve food at a given site. These barcode-like patterns were interpreted as "indexes" allowing the birds to retrieve from memory the locations of stored food.<br /> The present manuscript proposes a recurrent network model that generates such barcode activity and uses it to form attractor-like memories that bind information about location and food. The manuscript then examines the computational role of barcode activity in the model by simulating two behavioral tasks, and by comparing the model with an alternate model in which barcode activity is ablated.

Strengths of the study:

- Proposes a potential neural implementation for the indexing theory of episodic memory<br /> - Provides a mechanistic model of striking experimental findings: barcode-like, sparse patterns of activity when birds store a grain at a specific location<br /> - A particularly interesting aspect of the model is that it proposes a mechanism for binding discrete events to a continuous spatial map, and demonstrates the computational advantages of this mechanism

Weaknesses:

- The relation between the model and experimentally recorded activity needs some clarification<br /> - The relation with indexing theory could be made more clear<br /> - The importance of different modeling ingredients and dynamical mechanisms could be made more clear<br /> - The paper would be strengthened by focusing on the most essential aspects

Reviewer #1 (Public review):

(1a) Summary:

The author studied metabolic networks for central metabolism, focusing on how system trajectories returned to their steady state. To quantify the response, systematic perturbation was performed in simulation and the maximal destabilization away from steady state (compared with initial perturbation distance) was characterized. The author analyzed the perturbation response and found that sparse network and networks with more cofactors are more "stable", in the sense that the perturbed trajectories have smaller deviation along the path back to the steady state.

(1b) Strengths and major contributions:

The author compared three metabolic models and performed systematic perturbation analysis in simulation. This is the first work characterized how perturbed trajectories deviate from equilibrium in large biochemical systems and illustrated interesting findings about the difference between sparse biological systems and randomly simulated reaction networks.

(1c) Discussion and impact for the field:

Metabolic perturbation is an important topic in cell biology and has important clinical implication in pharmacodynamics. The computational analysis in this study provides an initiative for future quantitative analysis on metabolism and homeostasis.

Comments on revised version:

The revised version of this manuscript made some clarifications, while I think the analysis of response coefficients is still numerical and model-specific, being unclear under dynamical systems of views.

Reviewer #2 (Public review):

The authors have conducted a valuable comparative analysis of perturbation responses in three nonlinear kinetic models of E. coli central carbon metabolism found in the literature. They aimed to uncover commonalities and emergent properties in the perturbation responses of bacterial metabolism. They discovered that perturbations in the initial concentrations of specific metabolites, such as adenylate cofactors and pyruvate, significantly affect the maximal deviation of the responses from steady-state values. Furthermore, they explored whether the network connectivity (sparse versus dense connections) influences these perturbation responses. The manuscript is reasonably well written.

Comments on revised version:

The authors have addressed my concerns to a large extent. However, a few minor issues remain, as listed below:

(1) The authors identified key metabolites affecting responses to perturbations in two ways: (i) by fixing a metabolite's value and (ii) by performing a sensitivity analysis. It would be helpful for the modeling community to understand better the differences and similarities in the obtained results. Do both methods identify substrate-level regulators? Is freezing a metabolite's dynamics dramatically changing the metabolic response (and if yes, which ones are so different in the two cases)? Does the scope of the network affect these differences and similarities?

(2) Regarding the issues the authors encountered when performing the sensitivity analysis, they can be approached in two ways. First, the authors can check the methods for computing conserved moieties nicely explained by Sauro's group (doi:10.1093/bioinformatics/bti800) and compute them for large-scale networks (but beware of metabolites that belong to several conserved pools). Otherwise, the conserved pools of metabolites can be considered as variables in the sensitivity analysis-grouping multiple parameters is a common approach in sensitivity analysis.

Joint Public Review:

Automatically identifying single cell types in heterogeneous mixed cell populations hold great promise to characterize mixed cell populations and to discover new rules of spatial organization and cell-cell communication. Although the current manuscript focuses on the application of quality control of iPSC cultures, the same approach can be extended to a wealth of other applications including in depth study of the spatial context. The simple and high-content assay democratizes use and enables adoption by other labs.

The authors also propose a new nucleocentric phenotyping pipeline, where a convolutional neural network is trained on the nucleus and some margins around it. This nucleocentric approach improves classification performance at high densities because nuclear segmentation is less prone to errors in dense cultures.

The manuscript is supported by comprehensive experimental and computational validations that raises the bar beyond the current state of the art in the field of high-content phenotyping and makes this manuscript especially compelling. These include (i) Explicitly assessing replication biases (batch effects); (ii) Direct comparison of feature-based (a la cell profiling) versus deep-learning-based classification (which is not trivial/obvious for the application of cell profiling); (iii) Systematic assessment of the contribution of each fluorescent channel; (iv) Evaluation of cell-density dependency; (v) explicit examination of mistakes in classification; (vi) Evaluating the performance of different spatial contexts around the cell / nucleus; (vii) generalization of models trained on cultures containing a single cell type (mono-cultures) to mixed co-cultures; (viii) application to multiple classification tasks.

Reviewer #1 (Public review):

Summary:

The authors of this study set out to find RNA binding proteins in the CNS in cell-type specific sequencing data and discover that the cardiomyopathy-associated protein RBM20 is selectively expressed in olfactory bulb glutamatergic neurons and PV+ GABAergic neurons. They make an HA-tagged RBM20 allele to perform CLIP-seq to identify RBM20 binding sites and find direct targets of RBM20 in olfactory bulb glutmatergic neurons. In these neurons, RBM20 binds intronic regions. RBM20 has previously been implicated in splicing, but when they selectively knockout RBM20 in glutamatergic neurons they do not see changes in splicing, but they do see changes in RNA abundance, especially of long genes with many introns, which are enriched for synapse-associated functions. These data show that RBM20 has important functions in gene regulation in neurons, which was previously unknown, and they suggest it acts through a mechanism distinct from what has been studied before in cardiomyocytes.

Strengths:

The study finds expression of the cardiomyopathy-associated RNA binding protein RBM20 in specific neurons in the brain, opening new windows into its potential functions there.

The study uses CLIP-seq to identify RBM20 binding RNAs in olfactory bulb neurons.

Conditional knockout of RBM20 in glutamatergic or PV neurons allows the authors to detect mRNA expression that is regulated by RBM20.

The data include substantial controls and quality control information to support the rigor of the findings.

Weaknesses:

The authors do not fully identify the mechanism by which RBM20 acts to regulate RNA expression in neurons, though they do provide data suggesting that neuronal RBM20 does not regulate alternate splicing in neurons, which is an interesting contrast to its proposed mechanism of function in cardiomyocytes. Discovery of the RNA regulatory functions of RBM20 in neurons is left as a question for future studies.

The study does not identify functional consequences of the RNA changes in the conditional knockout cells, so this is also a question for the future.

Reviewer #2 (Public review):

Summary:

The group around Prof. Scheiffele has made seminal discoveries reg. alternative splicing that is reflected by a current ERC advanced grant and landmark papers in eLife (2015), Science (2016), and Nature Neuroscience (2019). Recently, the group investigated proteins that contain an RRM motif in the mouse cortex. One of them, termed RBM20, was originally thought to be muscle-specific and involved in alternative splicing in cardiomyocytes. However, upon close inspection, RBP20 is expressed in a particular set of interneurons (PV positive cells of the somatosensory cortex) in the cortex as well as in mitral cells of the olfactory bulb (OB). Importantly, they used CLIP to identify targets in the OB and heart. Next and quite importantly, they generated a knock-in mouse line with a His-biotin acceptor peptide and a HA epitope to perform specific biochemistry. Not surprisingly, this allowed them to specifically identify transcripts with long introns, however, most of the intronic binding sites were very distant to the splice sites. Closer GO term inspection revealed that RBM20 specifically regulates synapse-related transcripts. In order to get in vivo insight into its function in the brain, the authors generated both global as well as conditional KO mice. Surprisingly, there were no significant differences in in RBM20 ΔPV interneurons, however, 409 transcripts were deregulated in in OB glutamatergic neurons. Here, CLIP sites were mostly found to be very distant from differentially expressed exons. Furthermore, loss-of-function RBM20 primarily yields loss of transcripts, whereas upregulation appears to be indirect. Together, these results strongly suggest a role of RBM20 in the inclusion of cryptic exons thereby promoting target degradation.

Strengths:

The quality of the data and the figures is high, impressive and convincing. The reported results strongly suggest a role of RBM20 in the inclusion of cryptic exons thereby promoting target degradation.

Weaknesses:

I would not use the term weakness here.<br /> The description of the results is sometimes too dense and technical. As eLife does not have a size limit, there is no reason for the results section to be less than three pages. Especially the last paragraph of the results part (p4) does not do justice to the high importance of Fig. 5, which I consider of high importance and originality. Here are a few suggestions from a person that is not working on splicing, to improve the text part of this important manuscript.

(1) Introduction: too short, include a paragraph on splicing and cryptic exons<br /> (2) Results:<br /> - shortly describe the phenotypes of the mice mentioned<br /> - expand the section on Fig. 5 and cryptic exons especially<br /> (3) Discussion: too short, expand on the possible new role of RBM20 and target degradation, possibly by adding a scheme?

Reviewer #3 (Public review):

Summary:

The authors identified RBM20 expression in neural tissues using cell type-specific transcriptomic analysis. This discovery was further validated through in vitro and in vivo approaches, including RNA fluorescent in situ hybridization (FISH), open-source datasets, immunostaining, western blotting, and gene-edited RBM20 knockout (KO) mice. CLIP-seq and RiboTRAP data demonstrated that RBM20 regulates common targets in both neural and cardiac tissues, while also modulating tissue-specific targets. Furthermore, the study revealed that neuronal RBM20 governs long pre-mRNAs encoding synaptic proteins.

Strengths:

• Utilization of a large dataset combined with experimental evidence to identify and validate RBM20 expression in neural tissues.<br /> • Global and tissue-specific RBM20 KO mouse models provide robust support for RBM20 localization and expression.<br /> • Employing heart tissue as a control highlights the unique findings in neural tissues.

Weaknesses:

• Lack of physiological functional studies to explore RBM20's role in neural tissues.<br /> • Data quality requires improvement for stronger conclusions.<br /> • Western blot sample size should be increased for enhanced reliability.

Joint Public Reviews:

Summary:

The authors examine the eigenvalue spectrum of the covariance matrix of neural recordings in the whole-brain larval zebrafish during hunting and spontaneous behavior. They find that the spectrum is approximately power law, and, more importantly, exhibits scale-invariance under random subsampling of neurons. This property is not exhibited by conventional models of covariance spectra, motivating the introduction of the Euclidean random matrix model. The authors show that this tractable model captures the scale invariance they observe. They also examine the effects of subsampling based on anatomical location or functional relationships. Finally, they briefly discuss the benefit of neural codes which can be subsampled without significant loss of information.

Strengths:

With large-scale neural recordings becoming increasingly common, neuroscientists are faced with the question: how should we analyze them? To address that question, this paper proposes the Euclidean random matrix model, which embeds neurons randomly in an abstract feature space. This model is analytically tractable and matches two nontrivial features of the covariance matrix: approximate power law scaling, and invariance under subsampling. It thus introduces an important conceptual and technical advance for understanding large-scale simultaneously recorded neural activity.

Weaknesses:

The downside of using summary statistics is that they can be hard to interpret. Often the finding of scale invariance, and approximate power law behavior, points to something interesting. But here caution is in order: for instance, most critical phenomena in neural activity have been explained by relatively simple models that have very little to do with computation (Aitchison et al., PLoS CB 12:e1005110, 2016; Morrell et al., eLife 12, RP89337, 2014). Whether the same holds for the properties found here remains an open question.

Reviewer #1 (Public review):

This work regards the role of Aurora Kinase A (AurA) in trained immunity. The authors claim that AurA is essential to the induction of trained immunity. The paper starts with a series of experiments showing the effects of suppressing AurA on beta-glucan-trained immunity. This is followed by an account of how AurA inhibition changes the epigenetic and metabolic reprogramming that are characteristic of trained immunity. The authors then zoom in on specific metabolic and epigenetic processes (regulation of S-adenocylmethionine metabolism & histone methylation). Finally, an inhibitor of AurA is used to reduce beta-glucan's anti-tumour effects in a subcutaneous MC-38 model.

Strengths:

With the exception of my confusion around the methods used for relative gene expression measurements, the experimental methods are generally well-described. I appreciate the authors' broad approach to studying different key aspects of trained immunity (from comprehensive transcriptome/chromatin accessibility measurements to detailed mechanistic experiments). Approaching the hypothesis from many different angles inspires confidence in the results (although not completely - see weaknesses section). Furthermore, the large drug-screening panel is a valuable tool as these drugs are readily available for translational drug-repurposing research.

Weaknesses

(1) The manuscript contains factual inaccuracies such as:<br /> (a) Intro: the claim that trained cells display a shift from OXPHOS to glycolysis based on the paper by Cheng et al. in 2014; this was later shown to be dependent on the dose of stimulation and actually both glycolysis and OXPHOS are generally upregulated in trained cells (pmid 32320649)<br /> (b) Discussion: Trained immunity was first described as such in 2011, not decades ago.

(2) The authors approach their hypothesis from different angles, which inspires a degree of confidence in the results. However, the statistical methods and reporting are underwhelming.<br /> (a) Graphs depict mean +/- SEM, whereas mean +/- SD is almost always more informative.<br /> (b) The use of 1-tailed tests is dubious in this scenario. Furthermore, in many experiments/figures the case could be made that the comparisons should be considered paired (the responses of cells from the same animal are inherently not independent due to their shared genetic background and, up until cell isolation, the same host factors like serum composition/microbiome/systemic inflammation etc).<br /> (c) It could be explained a little more clearly how multiple testing correction was done and why specific tests were chosen in each instance.<br /> (d) Most experiments are done with n = 3, some experiments are done with n = 5. This is not a lot. While I don't think power analyses should be required for simple in vitro experiments, I would be wary of drawing conclusions based on n = 3. It is also not indicated if the data points were acquired in independent experiments. ATAC-seq/RNA-seq was, judging by the figures, done on only 2 mice per group. No power calculations were done for the in vivo tumor model.<br /> (e) Furthermore, the data spread in many experiments (particularly BMDM experiments) is extremely small. I wonder if these are true biological replicates, meaning each point represents BMDMs from a different animal? (disclaimer: I work with human materials where the spread is of course always much larger than in animal experiments, so I might be misjudging this.).

(3) Maybe the authors are reserving this for a separate paper, but it would be fantastic if the authors would report the outcomes of the entire drug screening instead of only a selected few. The field would benefit from this as it would save needless repeat experiments. The list of drugs contains several known inhibitors of training (e.g. mTOR inhibitors) so there must have been more 'hits' than the reported 8 Aurora inhibitors.

(4) Relating to the drug screen and subsequent experiments: it is unclear to me in supplementary figure 1B which concentrations belong to secondary screens #1/#2 - the methods mention 5 µM for the primary screen and "0.2 and 1 µM" for secondary screens, is it in this order or in order of descending concentration?<br /> (a) It is unclear if the drug screen was performed with technical replicates or not - the supplementary figure 1B suggests no replicates and quite a large spread (in some cases lower concentration works better?)

(5) The methods for (presumably) qPCR for measuring gene expression in Figure 1C are missing. Which reference gene was used and is this a suitably stable gene?

(6) From the complete unedited blot image of Figure 1D it appears that the p-Aurora and total Aurora are not from the same gel (discordant number of lanes and positioning). This could be alright if there are no/only slight technical errors, but I find it misleading as it is presented as if the actin (loading control to account for aforementioned technical errors!) counts for the entire figure.

(7) Figure 2: This figure highlights results that are by far not the strongest ones - I think the 'top hits' deserve some more glory. A small explanation on why the highlighted results were selected would have been fitting.

(8) Figure 3 incl supplement: the carbon tracing experiments show more glucose-carbon going into TCA cycle (suggesting upregulated oxidative metabolism), but no mito stress test was performed on the seahorse.

(9) Inconsistent use of an 'alisertib-alone' control in addition to 'medium', 'b-glucan', 'b-glucan + alisertib'. This control would be of great added value in many cases, in my opinion.

(10) Figure 4A: looking at the unedited blot images, the blot for H3K36me3 appears in its original orientation, whereas other images appear horizontally mirrored. Please note, I don't think there is any malicious intent but this is quite sloppy and the authors should explain why/how this happened (are they different gels and the loading sequence was reversed?)

(11) For many figures, for example prominently figure 5, the text describes 'beta-glucan training' whereas the figures actually depict acute stimulation with beta-glucan. While this is partially a semantic issue (technically, the stimulation is 'the training-phase' of the experiment), this could confuse the reader.

(12) Figure 6: Cytokines, especially IL-6 and IL-1β, can be excreted by tumour cells and have pro-tumoral functions. This is not likely in the context of the other results in this case, but since there is flow cytometry data from the tumour material it would have been nice to see also intracellular cytokine staining to pinpoint the source of these cytokines.

Reviewer #2 (Public review):

Summary:

This manuscript investigates the inhibition of Aurora A and its impact on β-glucan-induced trained immunity via the FOXO3/GNMT pathway. The study demonstrates that inhibition of Aurora A leads to overconsumption of SAM, which subsequently impairs the epigenetic reprogramming of H3K4me3 and H3K36me3, effectively abolishing the training effect.

Strengths:

The authors identify the role of Aurora A through small molecule screening and validation using a variety of molecular and biochemical approaches. Overall, the findings are interesting and shed light on the previously underexplored role of Aurora A in the induction of β-glucan-driven epigenetic change.

Weaknesses:

Given the established role of histone methylations, such as H3K4me3, in trained immunity, it is not surprising that depletion of the methyl donor SAM impairs the training response. Nonetheless, this study provides solid evidence supporting the role of Aurora A in β-glucan-induced trained immunity in murine macrophages. The part of in vivo trained immunity antitumor effect is insufficient to support the final claim as using Alisertib could inhibits Aurora A other cell types other than myeloid cells.

Reviewer #1 (Public Review):

HLA genes have long been known to harbor trans-species polymorphism (TSP). This manuscript aimed to use state-of-the-art analyses and updated genotyping data to rigorously test for the presence of TSP in HLA genes, quantify the timescales associated with HLA TSP, and relate HLA disease associations to evolutionary rates. To do this, the authors chose HLA alleles across great apes, old world monkeys, and new world monkeys on which to perform phylogenetic analyses, alongside non-parametric tests that compare patterns of synonymous diversity. Finally, HLA genetic associations with the disease were correlated with evolutionary rate.

Strengths:

The manuscript is well written and neatly organized, the figures are clear, and there are many supplementary analyses that will make this paper a great resource for MHC phylogenetics at allelic resolution.

Deployment of modern methodology such as BEAST2 can also test if the hypothesis of TSP is supported while accounting for uncertainties in tree topology and evolutionary rates, necessary additions to analyses of the MHC.

Weaknesses:

Because TSP has already been convincingly demonstrated to occur in the MHC, the primary benefit of the current study is to ensure these previous observations are still supported by the wealth of genetic data that is now available and modern phylogenetic approaches. However, the benefit of using the robust BEAST2 method comes with the weakness of not using all available data. Focusing on single gene trees with only a small subset of alleles may bias results, and inclusion/exclusion criteria should be better defined.

One major point that is somewhat overlooked is the presence of multiple copy numbers for the MHC genes through classic birth and death evolution. For example, MHC-B in new world monkeys is duplicated many times (up to 10; PMID: 23715823). This duplication is naturally accompanied by gene loss and pseudogene formation. All of these things muddy the waters considerably yet are not addressed here. A good example is MHC-A, where it has been very difficult to apportion orthologs, even amongst closely related species, due to alternative or incomplete duplication/loss across the species, or region configuration polymorphism (e.g. PMID: 26371256). An example is chimpanzee Patr-AL which shares similarities with human HLA-A*02 lineage, but is a separate locus, could this show up as TSP under the current analysis?

Similarly, an alternative hypothesis for TSP is convergent gene conversion mutations: intergenic gene conversion has been repeatedly observed in HLA genes and the possibility of it occurring with the same two genes becomes more realistic over 45 million years. If the same two MHC genes recombined in humans and in an NWM, each on their own lineages, this would appear as TSP and would cause an overlap of pairwise synonymous divergence between human-human and human-NWM allele comparisons. This might be especially possible in MHC-DR and MHC-DQ genes presented in Figure 2 since both humans and NWM have multiple MHC-DRB and DQB genes (unless e.g. were genes besides HLA/MHC-DRB1 such as DRB3,4,5 included in the DRB phylogenies?). While BEAST2 may be a good way of robustly modeling and identifying TSP, and I understand these analyses cannot support many more sequences, the authors should consider adding an analysis that rules out gene conversion as an explanation for their results (especially the often repeated claim of 45 million year TSP). For example, can the authors use BLAST to ensure that the alleles that underlie 45 million years of TSP do not share close similarities to other HLA genes present in their respective human and NWM genomes? This seems like it could be fairly quickly performed for all genes, and even if it argued against TSP, it would be an interesting finding.

Finally, the authors have limited themselves to a small subset of HLA/MHC alleles and do not provide sufficient information in the methods to understand how these were chosen nor sufficient discussion surrounding how inclusion/exclusion criteria could bias results. For example, the authors say the alleles were chosen at 2-digit (i.e. 1 field) resolution, but in the phylogenies of Fig. 2, I see variable numbers of alleles chosen for each 2-digit allele family - what metric was used to decide on these alleles?

"We also collected associations between amino acids and TCR phenotypes". It is not clear either what was analyzed, or the results for this part of the analysis. This is a topic of much debate and none of the previous work has been discussed (PMID: 18304006, PMID: 29636542 as primers for this contentious subject)

MHC class I also interact with NK cell receptors, including polymorphic KIR. Through their interactions during infection control and reproduction, the two complexes co-evolve across primates, contributing to the maintenance of MHC diversity. Interaction with KIR likely has a greater impact on HLA polymorphism than interactions with TCR, yet this is not factored into any of the models, or indeed mentioned in the text.

One additional reason inclusion of the KIR binding is important relates to the point above about gene conversion, where it is established that gene conversion reproducibly swaps KIR-binding motifs among MHC class I alleles and genes. HLA-A*23, *24, and *25, *32, for example, are characterized by the acquisition of the 'Bw4' motif from HLA-B (PMID: 26284483), likely followed by positive natural selection. For exon 2 (which encodes the motif), these alleles turn up in a clade distinct from other human HLA-A (Fig 2-S1). What is the impact of the Bw4 motif on this phylogeny? Could this shuffling of motifs be interpreted as indirect TSP?

The analysis that shows the most rapidly evolving sites occur in the peptide binding domain brings little new to the field. This has been established by the Hughes and Nei (cited) and Parham, Lawlor, etc of 1988 (e.g. PMID: 3375250), and replicated multiple times across human populations and many other species.<br /> Likewise, the disease association part. It is nice to have a summary of the known associations, but there are others out there and this one is far from thorough. Here, 50% of the information about infectious diseases appears to be taken from one reference, leaving out some major bodies of work; for example identifying specific peptide binding residues or peptides that associate with HIV (PMID: 22896606) or malaria control (PMID: 1280333). It is also missing some major concepts -such as the DRB1 'shared epitope' of peptide binding residues that predispose to Rheumatoid Arthritis and protects from Parkinson's disease (35 years of work from PMID: 2446635 through PMID: 30910980). The nasopharyngeal carcinoma and EBV story (e.g. PMID: 23209447). Another huge gap here is the pregnancy syndromes -associations of specific HLA C and NK cell receptor allotypes with preeclampsia for example. There are thousands of HLA associations not considered in this section, and to do them justice would likely require an enormous amount of work.<br /> Thus - neither the idea that HLA/MHC polymorphism is focused on peptide binding nor that this binding drives resistance to infection and associations with the disease are new concepts. The previous work in these areas is inadequately acknowledged.

The paper is written in a very approachable language, which is nice to read and friendly to non-experts, but perhaps a little too much so in places. I find that the paper follows a very non-traditional format with respect to for example the results section, which seems a mixture of Introduction/methods/figure legends/discussion with no real solid result description.

Reviewer #2 (Public Review):

Fortier and Pritchard investigated the breadth and depth of trans-species polymorphism (TSP) within six primate classical (antigen-presenting) major histocompatibility complex (MHC) genes (three MHC class I and three MHC class II). The MHC is of wide interest because of its unique evolutionary patterns within the genomes of jawed vertebrates and for its extensive and consistent associations with disease phenotypes. The findings of the paper are:<br /> 1) Trans-species polymorphism (TSP) within major histocompatibility complex (MHC) genes, whereby some alleles are more similar between rather than within species, occurs between humans and non-human primates despite rapid allelic turnover.<br /> 2) Highly polymorphic/rapidly evolving sites are mostly involved in peptide binding.<br /> 3) The identified, rapidly-evolving sites are associated with disease.

However, because these general findings have been previously demonstrated to varying extents by numerous other studies, these are not the strength of this paper. The strength and importance of this paper are in its utilization of a large evolutionary range of species and genes and its methodological approach and the extent of analyses undertaken to characterize the depth and extent of the TSP among primates. The major contribution of this paper is showing that TSP in the MHC is widespread among diverse primate taxa, and, depending on the particular MHC gene, TSP can be detected between humans and non-human primates as distantly diverged from the human lineage as new world monkeys of the Americas, ~45 million years ago. The paper, overall, made good methodological choices to account for the fascinating but challenging nature of the MHC, which includes its extensive allelic polymorphism (much of which is only characterized for the peptide-binding domain, encoded by exons 2 and 3), the difficulty in assessing phylogenetic relationships (particularly due to recombination and/or interallelic gene conversion), and differentiating convergence from conservation. There is no single analysis that can perfectly account for all these factors. This paper used two methods to test for TSP, Bayesian evolutionary analysis and synonymous nucleotide distances (dS), each with their respective strengths and limitations articulated. TSP, to varying degrees, is supported by both analyses. The paper further identifies rapidly evolving positions within the MHC molecules (predominantly located in the MHC peptide-binding domain), quantitatively shows that they are more likely to be in proximity to the bound peptide within the peptide binding domain, and shows, via a literature review of HLA fine-mapping studies, that those positions are associated with both infectious and autoimmune disease.

The conclusions of the paper, therefore, are supported and appropriate with the most important caveats noted, but the paper would benefit from:<br /> 1) Addressing how copy number variation of MHC class I genes among primate species might have affected their analyses and results (only single representative genes of the class II MHC, which also exhibit copy number variation, were used for this study).<br /> 2) Considering the differences between class I and class II MHC roles in immune function and how those might relate to the observed patterns.

Reviewer #1 (Public review):

Summary:

The manuscript discusses the role of phosphorylated ubiquitin (pUb) by PINK1 kinase in neurodegenerative diseases. It reveals that elevated levels of pUb are observed in aged human brains and those affected by Parkinson's disease (PD), as well as in Alzheimer's disease (AD), aging, and ischemic injury. The study shows that increased pUb impairs proteasomal degradation, leading to protein aggregation and neurodegeneration. The authors also demonstrate that PINK1 knockout can mitigate protein aggregation in aging and ischemic mouse brains, as well as in cells treated with a proteasome inhibitor. While this study provided some interesting data, several important points should be addressed before being further considered.

Strengths:

(1) Reveals a novel pathological mechanism of neurodegeneration mediated by pUb, providing a new perspective on understanding neurodegenerative diseases.<br /> (2) The study covers not only a single disease model but also various neurodegenerative diseases such as Alzheimer's disease, aging, and ischemic injury, enhancing the breadth and applicability of the research findings.

Weaknesses:

(1) PINK1 has been reported as a kinase capable of phosphorylating Ubiquitin, hence the expected outcome of increased p-Ub levels upon PINK1 overexpression. Figures 5E-F do not demonstrate a significant increase in Ub levels upon overexpression of PINK1 alone, whereas the evident increase in Ub expression upon overexpression of S65A is apparent. Therefore, the notion that increased Ub phosphorylation leads to protein aggregation in mouse hippocampal neurons is not yet convincingly supported.<br /> (2) The specificity of PINK1 and p-Ub antibodies requires further validation, as a series of literature indicate that the expression of the PINK1 protein is relatively low and difficult to detect under physiological conditions.<br /> (3) In Figure 6, relying solely on Western blot staining and golgi staining under high magnification is insufficient to prove the impact of PINK1 overexpression on neuronal integrity and cognitive function. The authors should supplement their findings with immunostaining results for MAP2 or NeuN to demonstrate whether neuronal cells are affected.<br /> (4) The authors should provide more detailed figure captions to facilitate the understanding of the results depicted in the figures.<br /> (5) While the study proposes that pUb promotes neurodegeneration by affecting proteasomal function, the specific molecular mechanisms and signaling pathways remain to be elucidated.

Reviewer #2 (Public review):

Summary:

The manuscript makes the claim that pUb is elevated in a number of degenerative conditions including Alzheimer's Disease and cerebral ischaemia. Some of this is based on antibody staining which is poorly controlled and difficult to accept at this point. They confirm previous results that a cytosolic form of PINK1 accumulates following proteasome inhibition and that this can be active. Accumulation of pUb is proposed to interfere with proteostasis through inhibition of the proteasome. Much of the data relies on over-expression and there is little support for this reflecting physiological mechanisms.

Weaknesses:

The manuscript is poorly written. I appreciate this may be difficult in a non-native tongue, but felt that many of the problems are organisational. Less data of higher quality, better controls and incision would be preferable. Overall the referencing of past work is lamentable.<br /> Methods are also very poor and difficult to follow.

Until technical issues are addressed I think this would represent an unreliable contribution to the field.

Reviewer #3 (Public review):

Summary:

This study aims to explore the role of phosphorylated ubiquitin (pUb) in proteostasis and its impact on neurodegeneration. By employing a combination of molecular, cellular, and in vivo approaches, the authors demonstrate that elevated pUb levels contribute to both protective and neurotoxic effects, depending on the context. The research integrates proteasomal inhibition, mitochondrial dysfunction, and protein aggregation, providing new insights into the pathology of neurodegenerative diseases.

Strengths:

- The integration of proteomics, molecular biology, and animal models provides comprehensive insights.<br /> - The use of phospho-null and phospho-mimetic ubiquitin mutants elegantly demonstrates the dual effects of pUb.<br /> - Data on behavioral changes and cognitive impairments establish a clear link between cellular mechanisms and functional outcomes.

Weaknesses:

- While the study discusses the reciprocal relationship between proteasomal inhibition and pUb elevation, causality remains partially inferred.<br /> - The role of alternative pathways, such as autophagy, in compensating for proteasomal dysfunction is underexplored.<br /> - The immunofluorescence images in Figure 1A-D lack clarity and transparency. It is not clear whether the images represent human brain tissue, mouse brain tissue, or cultured cells. Additionally, the DAPI staining is not well-defined, making it difficult to discern cell nuclei or staging. To address these issues, lower-magnification images that clearly show the brain region should be provided, along with improved DAPI staining for better visualization. Furthermore, the Results section and Figure legends should explicitly indicate which brain region is being presented. These concerns raise questions about the reliability of the reported pUb levels in AD, which is a critical aspect of the study's findings.<br /> - Figure 4B should also indicate which brain region is being presented.

Reviewer #1 (Public review):

Previous experimental studies demonstrated that membrane association drives avidity for several potent broadly HIV-neutralizing antibodies and its loss dramatically reduces neutralization. In this study, the authors present a tour de force analysis of molecular dynamics (MD) simulations that demonstrate how several HIV-neutralizing membrane-proximal external region (MPER)-targeting antibodies associate with a model lipid bilayer.

First, the authors compared how three MPER antibodies, 4E10, PGZL1, and 10E8, associated with model membranes, constructed with two lipid compositions similar to native viral membranes. They found that the related antibodies 4E10 and PGZL1 strongly associate with a phospholipid near heavy chain loop 1, consistent with prior crystallographic studies. They also discovered that a previously unappreciated framework region between loops 2-3 in the 4E10/PGZL1 heavy chain contributes to membrane association. Simulations of 10E8, an antibody from a different lineage, revealed several differences from published X-ray structures. Namely, a phosphatidylcholine binding site was offset and includes significant interaction with a nearby framework region. The revised manuscript demonstrates that these lipid interactions are robust to alterations in membrane composition and rigidity. However, it does not address the reverse-that phospholipids known experimentally not to associate with these antibodies (if any such lipids exist) also fail to interact in MD simulations.

Next, the authors simulate another MPER-targeting antibody, LN01, with a model HIV membrane either containing or missing an MPER antigen fragment within. Of note, LN01 inserts more deeply into the membrane when the MPER antigen is present, supporting an energy balance between the lowest energy conformations of LN01, MPER, and the complex. These simulations recapitulate lipid binding interactions solved in published crystallographic studies but also lead to the discovery of a novel lipid binding site the authors term the "Loading Site", which could guide future experiments with this antibody.

The authors next established course-grained (CG) MD simulations of the various antibodies with model membranes to study membrane embedding. These simulations facilitated greater sampling of different initial antibody geometries relative to membrane. These CG simulations , which cannot resolve atomistic interactions, are nonetheless compelling because negative controls (ab 13h11, BSA) that should not associate with membrane indeed sample significantly less membrane.

Distinct geometries derived from CG simulations were then used to initialize all-atom MD simulations to study insertion in finer detail (e.g., phospholipid association), which largely recapitulate their earlier results, albeit with more unbiased sampling. The multiscale model of an initial CG study with broad geometric sampling, followed by all-atom MD, provides a generalized framework for such simulations.

Finally, the authors construct velocity pulling simulations to estimate the energetics of antibody membrane embedding. Using the multiscale modelling workflow to achieve greater geometric sampling, they demonstrate that their model reliably predicts lower association energetics for known mutations in 4E10 that disrupt lipid binding. However, the model does have limitations: namely, its ability to predict more subtle changes along a lineage-intermediate mutations that reduce lipid binding are indistinguishable from mutations that completely ablate lipid association. Thus, while large/binary differences in lipid affinity might be predictable, the use of this method as a generative model are likely more limited.

The MD simulations conducted throughout are rigorous and the analysis are extensive, creative, and biologically inspired. Overall, these analyses provide an important mechanistic characterization of how broadly neutralizing antibodies associate with lipids proximal to membrane-associated epitopes to drive neutralization.

Reviewer #2 (Public review):

In this study, Maillie et al. have carried out a set of multiscale molecular dynamics simulations to investigate the interactions between the viral membrane and four broadly neutralizing antibodies that target the membrane proximal exposed region (MPER) of the HIV-1 envelope trimer. The simulation recapitulated in several cases the binding sites of lipid head groups that were observed experimentally by X-ray crystallography, as well as some new binding sites. These binding sites were further validated using a structural bioinformatics approach. Finally, steered molecular dynamics was used to measure the binding strength between the membrane and variants of the 4E10 and PGZL1 antibodies.

The use of multiscale MD simulations allows for a detailed exploration of the system at different time and length scales. The combination of MD simulations and structural bioinformatics provides a comprehensive approach to validate the identified binding sites. Finally, the steered MD simulations offer quantitative insights into the binding strength between the membrane and bnAbs.

While the simulations and analyses provide qualitative insights into the binding interactions, they do not offer a quantitative assessment of energetics. The coarse-grained simulations exhibit artifacts and thus require careful analysis.

This study contributes to a deeper understanding of the molecular mechanisms underlying bnAb recognition of the HIV-1 envelope. The insights gained from this work could inform the design of more potent and broadly neutralizing antibodies.

Reviewer #1 (Public review):

In this work, the authors examine the mechanism of action of MOTS-c and its impact on monocyte-derived macrophages. In the first part of the study, they show that MOTS-c acts as a host defense peptide with direct antibacterial activity. In the second part of the study, the authors aim to demonstrate that MOTS-c influences monocyte differentiation into macrophages via transcriptional regulation.

Major strengths. Methods used to study the bactericidal activity of MOTS-c are appropriate and the results convincing.

Major weaknesses. Methods used to study the impact on monocyte differentiation are inappropriate and the conclusions not fully supported by the data shown. A major issue is the use of the THP-1 cell line, a transformed monocytic line which does not mimic physiological monocyte biology. In particular, THP-1 differentiation is induced by PMA, which is a completely artificial system and conclusions from this approach cannot be generalized to monocyte differentiation. The authors would need to perform this series of experiments using freshly isolated monocytes, either from mouse or human. The read-out used for macrophage differentiation (adherence to plastic) is also not very robust, and the authors would need to analyze other parameters such as cell surface markers. It is also not clear whether MOTS-c could act in a cell-intrinsic fashion, as the authors have exposed cells to exogenous MOTS-c in all their experiments. The authors have also analyzed the transcriptomic changes induced by MOTS-c exposure in macrophages derived from young or old mice. While the results are potentially interesting, the differences observed seem independent from MOTS-c and mainly related to age, therefore the conclusions from this figure are not clear. The physiological relevance of this study is also unclear.

Reviewer #1 (Public review):

Summary:

This paper examines patterns of diversity and divergence in two closely related sub-species of Zea mays. While the data are interesting and the authors have tried to exclude multiple confounding factors, many patterns cannot clearly be ascribed to one cause or another.

Strengths:

The paper presents interesting data from sets of sympatric populations of the two sub-species, maize and teosinte. This sampling offers unique insights into the diversity and divergence between the two, as well as the geographic structure of each. Many analyses and simulations to check analyses have been carried out.

Weaknesses:

The strength of conclusions that can be drawn from the analyses was low, partly because there are many strange patterns. The authors have done a good job of adding caveats, but clearly, these species do not meet many assumptions of our methods

Reviewer #1 (Public review):

Summary:

In this manuscript, Shao et al. investigate the contribution of different cortical areas to working memory maintenance and control processes, an important topic involving different ideas about how the human brain represents and uses information when no longer available to sensory systems. In two fMRI experiments, they demonstrate that human frontal cortex (area sPCS) represents stimulus (orientation) information both during typical maintenance, but even more so when a categorical response demand is present. That is, when participants have to apply an added level of decision control to the WM stimulus, sPCS areas encode stimulus information more than conditions without this added demand. These effects are then expanded upon using multi-area neural network models, recapitulating the empirical gradient of memory vs control effects from visual to parietal and frontal cortices. Multiple experiments and analysis frameworks provide support for the authors' conclusions, and control experiments and analysis are provided to help interpret and isolate the frontal cortex effect of interest. While some alternative explanations/theories may explain the roles of frontal cortex in this study and experiments, important additional analyses have been added that help ensure a strong level of support for these results and interpretations.

Strengths:

- The authors use an interesting and clever task design across two fMRI experiments that is able to parse out contributions of WM maintenance alone along with categorical, rule-based decisions. Importantly, the second experiment only uses one fixed rule, providing both an internal replication of Experiment 1's effects and extending them to a different situation when rule switching effects are not involved across mini-blocks.

- The reported analyses using both inverted encoding models (IEM) and decoders (SVM) demonstrate the stimulus reconstruction effects across different methods, which may be sensitive to different aspects of the relationship between patterns of brain activity and the experimental stimuli.

- Linking the multivariate activity patterns to memory behavior is critical in thinking about the potential differential roles of cortical areas in sub-serving successful working memory. Figure 3's nicely shows a similar interaction to that of Figure 2 in the role of sPCS in the categorization vs. maintenance tasks. This is an important contribution to the field when we consider how a distributed set of interacting cortical areas supports successful working memory behavior.

- The cross-decoding analysis in Figure 4 is a clever and interesting way to parse out how stimulus and rule/category information may be intertwined, which would have been one of the foremost potential questions or analyses requested by careful readers.

- Additional ROI analyses in more anterior regions of the PFC help to contextualize the main effects of interest in the sPCS (and no effect in the inferior frontal areas, which are also retinotopic, adds specificity). And, more explanation for how motor areas or preparation are likely not involved strengthens the takeaways of the study (M1 control analysis).

Weaknesses:

- An explicit, quantitative link between the RNN and fMRI data is perhaps a last point that would integrate the RNN conclusion and analyses in line with the human imaging data.

- As Rev 2 mentions, multiple types of information codes may be present, and the response letter Figure 5 using representational similarity (RSA) gets at this question. It would strengthen the work to, at minimum, include this analysis as an extended or supplemental figure.

To sum up the results, a possible, brief schematic of each cortical area analyzed and its contribution to information coding in WM and successful subsequent behavior may help readers take away important conclusions of the cortical circuitry involved.

Reviewer #2 (Public review):

Summary:

The author provide evidence that helps resolve long-standing questions about the differential involvement of frontal and posterior cortex in working memory. They show that whereas early visual cortex shows stronger decoding of memory content in a memorization task vs a more complex categorization task, frontal cortex shows stronger decoding during categorization tasks than memorization tasks. They find that task-optimized RNNs trained to reproduce the memorized orientations show some similarities in neural decoding to people. Together, this paper presents interesting evidence for differential responsibilities of brain areas in working memory.

Strengths:

This paper was overall strong. It had a well-designed task, best-practice decoding methods, and careful control analyses. The neural network modeling adds additional insight into the potential computational roles of different regions.

Weaknesses:

Few. While more could be perhaps done to understand the RNN-fMRI correspondence, the paper contributes a compelling set of empirical findings and interpretations that can inform future research.

Das EU-Parlament hat die vorgesehenen strengeren ökologischen Vorschriften für Agrarsubventionen verändert. So ist der Erhalt von Subventionen nicht mehr daran geknüpft, dass 4% der bebaubaren Fläche brach liegen. .https://taz.de/EU-und-Ampel-geben-Bauernprotesten-nach/!6004784/

Reviewer #1 (Public review):

Summary:

This paper proposes a new model of perceptual habituation and tests it over two experiments with both infants and adults. The model combines a neural network for visual processing with a Bayesian rational model for attention (i.e., looking time) allocation. This Bayesian framework allows the authors to measure elegantly diverse factors that might drive attention, such as expected information gain, current information gain, and surprise. The model is then fitted to infant and adult participants' data over two experiments, which systematically vary the amount of habituation trials (Experiment 1) and the type of dishabituation stimulus (familiarity, pose, number, identity, and animacy). Results show that a model based on (expected) information gain performs better than a model based on surprise. Additionally, while novelty preference is observed when exposure to familiar stimuli is elevated, no familiarity preference is observed when exposure to familiar stimuli is low or intermediate, which is in contrast with past work.

Strengths:

There are three key strengths of this work:

(1) It integrates a neural network model with a Bayesian rational learner, thus bridging the gap between two fields that have often been disconnected. This is rarely seen in the cognitive science field, but the advantages are very clear from this paper: It is possible to have computational models that not only process visual information, but also actively explore the environment based on overarching attentional processes.

(2) By varying parametrically the amount of stimulus exposure and by testing the effects of multiple novel stimulus types, this work allowed the authors to put classical theories of habituation to the test on much finer scales than previous research has done.

(3) The Bayesian model allows the authors to test what specific aspects are different in infants and adults, showing that infants display greater values for the noise parameter.

Weaknesses:

Although a familiarity preference is not found, it is possible that this is related to the nature of the stimuli and the amount of learning that they offer. While infants here are exposed to the same perceptual stimulus repeatedly, infants can also be familiarised to more complex stimuli or scenarios. Classical statistical learning studies for example expose infants to specific pseudo-words during habituation/familiarisation, and then test their preference for familiar vs novel streams of pseudo-words. The amount of learning progress in these probabilistic learning studies is greater than in perceptual studies, and familiarity preferences may thus be more likely to emerge there. For these reasons, I think it is important to frame this as a model of perceptual habituation. This would also fit well with the neural net that was used, which is processing visual stimuli rather than probabilistic structures. If statements in the discussion are limited to perceptual paradigms, they would make the arguments more compelling.

Reviewer #2 (Public review):

Summary:

This paper extends a Bayesian perception/action model of habituation behavior (RANCH) to infant-looking behavior. The authors test the model predictions against data from several groups of infants and adults tested in habituation paradigms that vary the number of familiarisation stimuli and the nature of the test stimuli. Model sampling was taken as a proxy for looking times. The predictions of the model generally resemble the empirical data collected, though there are some potentially important differences.

Strengths:

This study addresses an important question, given the fundamental nature of habituation to learning and memory. Previous explanations of infant habituation have typically not been in the form of formal models, making falsification difficult. This Bayesian model is relatively simple but also incorporates a CNN to which the actual stimulus image can be presented, which enables principled predictions about image similarity to be derived.

The paper contains data from a relatively large number of adults and infants, allowing parameter differences across age to be probed.

The data suggests that the noise prior parameter is higher in infants, suggesting one mechanism through which infant and adult habituation is different, though of course, this depends on whether there is sufficient empirical evidence that other explanations can be ruled out, which isn't clear in the manuscript currently.

Weaknesses:

There are no formal tests of the predictions of RANCH against other leading hypotheses or models of habituation. This makes it difficult to evaluate the degree to which RANCH provides an alternative account that makes distinct predictions from other accounts. I appreciate that because other theoretical descriptions haven't been instantiated in formal models this might be difficult, but some way of formalising them to enable comparison would be useful.

The justification for using the RMSEA fitting approach could also be stronger - why is this the best way to compare the predictions of the formal model to the empirical data? Are there others? As always, the main issue with formal models is determining the degree to which they just match surface features of empirical data versus providing mechanistic insights, so some discussion of the level of fit necessary for strong inference would be useful.

The difference in model predictions for identity vs number relative to the empirical data seems important but isn't given sufficient weight in terms of evaluating whether the model is or is not providing a good explanation of infant behavior. What would falsification look like in this context?

For the novel image similarity analysis, it is difficult to determine whether any differences are due to differences in the way the CNN encodes images vs in the habituation model itself - there are perhaps too many free parameters to pinpoint the nature of any disparities. Would there be another way to test the model without the CNN introducing additional unknowns?

Related to that, the model contains lots of parts - the CNN, the EIG approach, and the parameters, all of which may or may not match how the infant's brain operates. EIG is systematically compared to two other algorithms, with KL working similarly - does this then imply we can't tell the difference between an explanation based on those two mechanisms? Are there situations in which they would make distinct predictions where they could be pulled apart? Also in this section, there doesn't appear to be any formal testing of the fits, so it is hard to determine whether this is a meaningful difference. However, other parts of the model don't seem to be systematically varied, so it isn't always clear what the precise question addressed in the manuscript is (e.g. is it about the algorithm controlling learning? or just that this model in general when fitted in a certain way resembles the empirical data?)

Reviewer #1 (Public review):

In the manuscript "Identification of neurodevelopmental organization of the cell populations of Juvenile Huntington's disease using dorso-ventral HD organoids and HD mouse embryos," the authors establish a fused dorso-ventral system that mimics cortex-striatum interactions within a single organoid and use this system to investigate neurodevelopmental impairments caused by HD. Specifically, they describe certain phenotypes in 60-day HD organoids and the brains of humanized mouse embryos, utilizing both wet-lab and single-cell sequencing techniques. The authors also develop dorsal/ventral and ventral/dorsal mosaic control/HD organoids, showing a capacity to rescue some HD phenotypes.

The manuscript could be a valuable contribution to the field, however it has relevant drawbacks, the most significant being a lack of clarity regarding the replicates used for each genotype in the sequencing analyses. The lack of information on replicates raises the possibility that only a single replicate was analyzed for each organoid and brain sample. This approach may lead to concerns regarding the reproducibility of the findings, and it may be necessary for the authors to generate additional data to strengthen their conclusions. In addition, the analysis of the HD samples was conducted by pooling distinct cell populations from different brain regions (CTX, HIP, ChP for the dorsal brain, and STR, HYP, TH for the ventral brain). It is unclear why scRNA seq was used on pooled brain regions, which could obscure region-specific insights.

Another issue pertains to their proposed outcome: "Finally, we found that TTR protein, a choroid plexus marker, is elevated in the adult HD mouse serum, indicating that TTR may be a promising marker for detecting HD". This statement appears to lack statistical support, which makes this set of data potentially misleading and inconclusive.

The authors are encouraged to provide evidence of biological replicates, remove outcomes that lack statistical support, and address a series of points as detailed elsewhere.

Reviewer #2 (Public review):

The article titled "Identification of neurodevelopmental organization of the cell populations of juvenile Huntington's disease using dorso-ventral HD organoids and HD mouse embryos" analyses an in vitro human brain organoid model containig dorsal and ventral telencephalum structures derived from human iPSC from Huntington's disease patients or control subjects.

The authors describe differences in the pattern of expression of genes related to proliferation and neuronal maturation, with a slower pattern of differentiation present in HD cells. Moreover, the authors described a higher differentiation capacity of HD cells to generate choroid plexus identity following dorsal telencephalon prime protocol differentiation when compared to control cells. Whereas the claims related to Choroid plexus identity are intriguing, most of the claims made through the manuscript are not sustained by quantitative data or consistent results in the different conditions analysed, or many experiments seem to be missing to reach final conclusions.

In addition, the quality of the organoids used for experiments does not seem to have been assessed or satisfactorily presented in the figures of this paper. Many important details related to the experimental execution are missing in the current version of this manuscript.

Reviewer #1 (Public review):

Shin et al. conduct extensive electrophysiological and behavioral experiments to study the mechanisms of short-term synaptic plasticity at excitatory synapses in layer 2/3 of the rat medial prefrontal cortex. The authors interestingly find that short-term facilitation is driven by progressive overfilling of the readily releasable pool, and that this process is mediated by phospholipase C/diacylglycerol signaling and synaptotagmin-7 (Syt7). Specifically, knockdown of Syt7 not only abolishes the refilling rate of vesicles with high fusion probability, but it also impairs the acquisition of trace fear memory.

Overall, the authors offer novel insight to the field of synaptic plasticity through well-designed experiments that incorporate a range of techniques.

Reviewer #2 (Public review):

Summary:

Shin et al aim to identify in a very extensive piece of work a mechanism that contributes to dynamic regulation of synaptic output in the rat cortex at the second time scale. This mechanism is related to a new powerful model is well versed to test if the pool of SV ready for fusion is dynamically scaled to adjust supply demand aspects. The methods applied are state-of-the-art and both address quantitative aspects with high signal to noise. In addition, the authors examine both excitatory output onto glutamatergic and GABAergic neurons, which provides important information on how general the observed signals are in neural networks, The results are compellingly clear and show that pool regulation may be predominantly responsible. Their results suggests that a regulation of release probability, the alternative contender for regulation, is unlikely to be involved in the observed short term plasticity behavior (but see below). Besides providing a clear analysis pof the underlying physiology, they test two molecular contenders for the observed mechanism by showing that loss of Synaptotagmin7 function and the role of the Ca dependent phospholipase activity seems critical for the short term plasticity behavior. The authors go on to test the in vivo role of the mechanism by modulating Syt7 function and examining working memory tasks as well as overall changes in network activity using immediate early gene activity. Finally, they model their data, providing strong support for their interpretation of TS pool occupancy regulation.

Strengths:

This is a very thorough study, addressing the research question from many different angles and the experimental execution is superb. The impact of the work is high, as it applies recent models of short term plasticity behavior to in vivo circuits further providing insights how synapses provide dynamic control to enable working memory related behavior through nonpermanent changes in synaptic output.

Weaknesses:

While this work is carefully examined and the results are presented and discussed in a detailed manner, the reviewer is still not fully convinced that regulation of release provability is not a putative contributor to the observed behavior. No additional work is needed but in the moment I am not convinced that changes in release probability are not in play. One solution may be to extend the discussion of changes in rules probability as an alternative.

Fig 3 I am confused about the interpretation of the Mean Variance analysis outcome. Since the data points follow the curve during induction of short term plasticity, aren't these suggesting that release probability and not the pool size increases? Related, to measure the absolute release probability and failure rate using the optogenetic stimulation technique is not trivial as the experimental paradigm bias the experiment to a given output strength, and therefore a change in release probability cannot be excluded.

Fig4B interprets the phorbol ester stimulation to be the result of pool overfilling, however, phorbol ester stimulation has also been shown to increase release probability without changing the size of the readily releasable pool. The high frequency of stimulation may occlude an increased paired pulse depression in presence of OAG, which others have interpreted in mammalian synapses as an increase in release probability.

The literature on Syt7 function is still quite controversial. An observation in the literature that loss of Syt7 function in the fly synapse leads to an increase of release probability. Thus the observed changes in short term plasticity characteristics in the Syt7 KD experiments may contain a release probability component. Can the authors really exclude this possibility? Figure 5 shows for the Syt7 KD group a very prominent depression of the EPSC/IPSC with the second stimulus, particularly for the short interpulse intervals, usually a strong sign of increased release probability, as lack of pool refilling can unlikely explain the strong drop in synaptic output.

Reviewer #3 (Public review):

Summary:

The report by Shin, Lee, Kim, and Lee entitled "Progressive overfilling of readily releasable pool underlies short-term facilitation at recurrent excitatory synapses in layer 2/3 of the rat prefrontal cortex" describes electrophysiological experiments of short-term synaptic plasticity during repetitive presynaptic stimulation at synapses between layer 2/3 pyramidal neurons and nearby target neurons. Manipulations include pharmacological inhibition of PLC and actin polymerization, activation of DAG receptors, and shRNA knockdown of Syt7. The results are interpreted as support for the hypothesis that synaptic vesicle release sites are vacant most of the time at resting synapses (i.e., p_occ is low) and that facilitation (and augmentation) components of short-term enhancement are caused by an increase in occupancy, presumably because of acceleration of the transition from not-occupied to occupied. The report additionally describes behavioural experiments where trace fear conditioning is degraded by knocking down syt7 in the same synapses.

Strengths:

The strength of the study is in the new information about short-term plasticity at local synapses in layer 2/3, and the major disruption of a memory task after eliminating short-term enhancement at only 15% of excitatory synapses in a single layer of a small brain region. The local synapses in layer 2/3 were previously difficult to study, but the authors have overcome a number of challenges by combining channel rhodopsins with in vitro electroporation, which is an impressive technical advance.

Weaknesses:

The question of whether or not short-term enhancement causes an increase in p_occ (i.e., "readily releasable pool overfilling") is important because it cuts to the heart of the ongoing debate about how to model short term synaptic plasticity in general. However, my opinion is that, in their current form, the results do not constitute strong support for an increase in p_occ, even though this is presented as the main conclusion. Instead, there are at least two alternative explanations for the results that both seem more likely. Neither alternative is acknowledged in the present version of the report.

The evidence presented to support overfilling is essentially two-fold. The first is strong paired pulse depression of synaptic strength when the interval between action potentials is 20 or 25 ms, but not when the interval is 50 ms. Subsequent stimuli at frequencies between 5 and 40 Hz then drive enhancement. The second is the observation that a slow component of recovery from depression after trains of action potentials is unveiled after eliminating enhancement by knocking down syt7. Of the two, the second is predicted by essentially all models where enhancement mechanisms operate independently of release site depletion - i.e., transient increases in p_occ, p_v, or even N - so isn't the sort of support that would distinguish the hypothesis from alternatives (Garcia-Perez and Wesseling, 2008, https://doi.org/10.1152/jn.01348.2007).

Regarding the paired pulse depression: The authors ascribe this to depletion of a homogeneous population of release sites, all with similar p_v. However, the details fit better with the alternative hypothesis that the depression is instead caused by quickly reversing inactivation of Ca2+ channels near release sites, as proposed by Dobrunz and Stevens to explain a similar phenomenon at a different type of synapse (1997, PNAS,<br /> https://doi.org/10.1073/pnas.94.26.14843). The details that fit better with Ca2+ channel inactivation include the combination of the sigmoid time course of the recovery from depression (plotted backwards in Fig1G,I) and observations that EGTA (Fig2B) increases the paired-pulse depression seen after 25 ms intervals. That is, the authors ascribe the sigmoid recovery to a delay in the activation of the facilitation mechanism, but the increased paired pulse depression after loading EGTA indicates, instead, that the facilitation mechanism has already caused p_r to double within the first 25 ms (relative to the value if the facilitation mechanism was not active). Meanwhile, Ca2+ channel inactivation would be expected to cause a sigmoidal recovery of synaptic strength because of the sigmoidal relationship between Ca2+-influx and exocytosis (Dodge and Rahamimoff, 1967, https://doi.org/10.1113/jphysiol.1967.sp008367).

The Ca2+-channel inactivation hypothesis could probably be ruled in or out with experiments analogous to the 1997 Dobrunz study, except after lowering extracellular Ca2+ to the point where synaptic transmission failures are frequent. However, a possible complication might be a large increase in facilitation in low Ca2+ (Fig2B of Stevens and Wesseling, 1999, https://doi.org/10.1016/s0896-6273(00)80685-6).

On the other hand, even if the paired pulse depression is caused by depletion of release sites rather than Ca2+-channel inactivation, there does not seem to be any support for the critical assumption that all of the release sites have similar p_v. And indeed, there seems to be substantial emerging evidence from other studies for multiple types of release sites with 5 to 20-fold differences in p_v at a wide variety of synapse types (Maschi and Klyachko, eLife, 2020, https://doi.org/10.7554/elife.55210; Rodriguez Gotor et al, eLife, 2024, https://doi.org/10.7554/elife.88212 and refs. therein). If so, the paired pulse depression could be caused by depletion of release sites with high p_v, whereas the facilitation could occur at sites with much lower p_v that are still occupied. It might be possible to address this by eliminating assumptions about the distribution of p_v across release sites from the variance-mean analysis, but this seems difficult; simply showing how a few selected distributions wouldn't work - such as in standard multiple probability fluctuation analyses - wouldn't add much.

In any case, the large increase - often 10-fold or more - in enhancement seen after lowering Ca2+ below 0.25 mM at a broad range of synapses and neuro-muscular junctions noted above is a potent reason to be cautious about the LS/TS model. There is morphological evidence that the transitions from a loose to tight docking state (LS to TS) occur, and even that the timing is accelerated by activity. However, 10-fold enhancement would imply that at least 90 % of vesicles start off in the LS state, and this has not been reported. In addition, my understanding is that the reverse transition (TS to LS) is thought to occur within 10s of ms of the action potential, which is 10-fold too fast to account for the reversal of facilitation seen at the same synapses (Kusick et al, 2020, https://doi.org/10.1038/s41593-020-00716-1).

Individual points:

(1) An additional problem with the overfilling hypothesis is that syt7 knockdown increases the estimate of p_occ extracted from the variance-mean analysis, which would imply a faster transition from unoccupied to occupied, and would consequently predict faster recovery from depression. However, recovery from depression seen in experiments was slower, not faster. Meanwhile, the apparent decrease in the estimate of N extracted from the mean-variance analysis is not anticipated by the authors' model, but fits well with alternatives where p_v varies extensively among release sites because release sites with low p_v would essentially be silent in the absence of facilitation.

(2) Figure S4A: I like the TTX part of this control, but the 4-AP part needs a positive control to be meaningful (e.g., absence of TTX).

(3) Line 251: At least some of the previous studies that concluded these drugs affect vesicle dynamics used logic that was based on some of the same assumptions that are problematic for the present study, so the reasoning is a bit circular.

(4) Line 329 and Line 461: A similar problem with circularity for interpreting earlier syt7 studies.

Reviewer #1 (Public review):

Summary:

In this study, the authors explore a novel mechanism linking aging to chromosome mis-segregation and aneuploidy in yeast cells. They reveal that, in old yeast mother cells, chromosome loss occurs through asymmetric partitioning of chromosomes to daughter cells, a process coupled with the inheritance of an old Spindle Pole Body. Remarkably, the authors identify that remodeling of the nuclear pore complex (NPC), specifically the displacement of its nuclear basket, triggers these asymmetric segregation events. This disruption also leads to the leakage of unspliced pre-mRNAs into the cytoplasm, highlighting a breakdown in RNA quality control. Through genetic manipulation, the study demonstrates that removing introns from key chromosome segregation genes is sufficient to prevent chromosome loss in aged cells. Moreover, promoting pre-mRNA leakage in young cells mimics the chromosome mis-segregation observed in old cells, providing further evidence for the critical role of nuclear envelope integrity and RNA processing in aging-related genome instability.

Strengths:

The findings presented are not only intriguing but also well-supported by robust experimental data, highlighting a previously unrecognized connection between nuclear envelope integrity, RNA processing, and genome stability in aging cells, deepening our understanding of the molecular basis of chromosome loss in aging.

Weaknesses:

Further analysis of yeast aging data from microfluidic experiments will provide important information about the dynamic features and prevalence of the key aging phenotypes, e.g. pre-mRNA leakage and chromosome loss, reported in this work. In addition, a discussion would be needed to clarify the relationship between "chromosome loss" in this study and "genomic missegregation" reported previously in yeast aging.

Reviewer #2 (Public review):

Summary:

The authors make the interesting discovery of increased chromosome non-dysjunction in aging yeast mother cells. The phenotype is quite striking and well supported with solid experimental evidence. This is quite significant to a haploid cell (as used here) - loss of an essential chromosome leads to death soon thereafter. The authors then work to tie this phenotype to other age-associated phenotypes that have been previously characterized: accumulation of extrachromosomal rDNA circles that then correlate with compromised nuclear pore export functions, which correlates with "leaky" pores that permit unspliced mRNA messages to be inappropriately exported to the cytoplasm. They then infer that three intron containing mRNAs that encode portions in resolving sister chromatid separation during mitosis, are unspliced in this age-associated defect and thus lead to the non-dysjunction problem.

Strengths: The discovery of age-associated chromosome non-dysjunction is an interesting discovery, and it is demonstrated in a convincing fashion with "classic" microscopy-based single cell fluorescent chromosome assays that are appropriate and seem robust. The correlation of this phenotype with other age-associated phenotypes - specifically extrachromosomal rDNA circles and nuclear pore dysfunction - is supported by in vivo genetic manipulations that have been well-characterized in the past.

In addition, the application of the single cell mRNA splicing defect reporter showed very convincingly that general mRNA splicing is compromised in aged cells. Such a pleiotropic event certainly has big implications.

Weaknesses:

The biggest weakness is "connecting all the dots" of causality and linking the splicing defect to chromosome disjunction. I commend the authors for making a valiant effort in this regard, but there are many caveats to this interpretation. While the "triple intron" removal suppressed the non-dysjunction defect in aged cells, this could simply be a kinetic fix, where a slowdown in the relevant aspects of mitosis, could give the cell time to resolve the syntelic attachment of the chromatids. To this point, I note that the intronless version of GLC7, which affects the most dramatic suppression of the three genes, is reported by one of the authors to have a slow growth rate (Parenteau et al, 2008 - https://doi.org/10.1091/mbc.e07-12-1254).

Lastly, the Herculean effort to perform FISH of the introns in the cytoplasm is quite literally at the statistical limit of this assay. The data were not as robust as the other assays employed through this study. The data show either "no" signal for the young cells or a signal of 0, 1,or 2 FISH foci in the aged cells. In a Poisson distribution, which this follows, it is improbable to distinguish between these differences.

Reviewer #3 (Public review):

Summary:

Mirkovic et al explore the cause underlying development of aneuploidy during aging. This paper provides a compelling insight into the basis of chromosome missegregation in aged cells, tying this phenomenon to the established Nuclear Pore Complex architecture remodeling that occurs with aging across a large span of diverse organisms. The authors first establish that aged mother cells exhibit aberrant error correction during mitosis. As extrachromosomal rDNA circles (ERCs) are known to increase with age and lead to NPC dysfunction that can result in leakage of unspliced pre-mRNAs, Mirkovic et al search for intron-containing genes in yeast that may be underlying chromosome missegregation, identifying three genes in the aurora B-dependent error correction pathway: MCM21, NBL1, and GLC7. Interestingly, intron-less mutants in these genes suppress chromosome loss in aged cells, with a significant impact observed when all three introns were deleted (3x∆i). The 3x∆i mutant also suppresses the increased chromosome loss resulting from nuclear basket destabilization in a mlp1∆ mutant. The authors then directly test if aged cells do exhibit aberrant mRNA export, using RNA FISH to identify that old cells indeed leak intron-containing pre-mRNA into the cytoplasm, as well as a reporter assay to demonstrate translation of leaked pre-mRNA, and that this is suppressed in cells producing less ERCs. Mutants causing increased pre-mRNA leakage are sufficient to induce chromosome missegregation, which is suppressed by the 3x∆i.

Strengths:

The finding that deleting the introns of 3 genes in the Aurora B pathway can suppress age-related chromosome missegregation is highly compelling. Additionally, the rationale behind the various experiments in this paper is well-reasoned and clearly explained.

Weaknesses:

In some cases, controls for experiments were not presented or were depicted in other figures. High variability was seen in chromosome loss data, leading to large error bars. The text could have been more polished.

Reviewer #1 (Public review):

Summary:

The manuscript uses state-of-the-art analysis technology to document the spatio-temporal dynamics of brain activity during the processing of threats. The authors offer convincing evidence that complex spatio-temporal aspects of brain dynamics are essential to describe brain operations during threat processing.

Strengths:

Rigorous complex analyses well suited to the data.

Weaknesses:

Lack of a simple take-home message about discovery of a new brain operation.

Reviewer #2 (Public review):

Summary:

This paper by Misra and Pessoa uses switching linear dynamical systems (SLDS) to investigate the neural network dynamics underlying threat processing at varying levels of proximity. Using an existing dataset from a threat-of-shock paradigm in which threat proximity is manipulated in a continuous fashion, the authors first show that they can identify states that each has their own linear dynamical system and are consistently associated with distinct phases of the threat-of-shock task (e.g., "peri-shock", "not near", etc). They then show how activity maps associated with these states are in agreement with existing literature on neural mechanisms of threat processing, and how activity in underlying brain regions alters around state transitions. The central novelty of the paper lies in its analyses of how intrinsic and extrinsic factors contribute to within-state trajectories and between-state transitions. A final set of analyses shows how the findings generalize to another (related) threat paradigm.

Strengths:

The analyses for this study are conducted at a very high level of mathematical and theoretical sophistication. The paper is very well written and effectively communicates complex concepts from dynamical systems. I am enthusiastic about this paper, but I think the authors have not yet exploited the full potential of their analyses in making this work meaningful toward increasing our neuroscientific understanding of threat processing, as explained below.

Weaknesses:

(1) I appreciate the sophistication of the analyses applied and/or developed by the authors. These methods have many potential use cases for investigating the network dynamics underlying various cognitive and affective processes. However, I am somewhat disappointed by the level of inferences made by the authors based on these analyses at the level of systems neuroscience. As an illustration consider the following citations from the abstract: "The results revealed that threat processing benefits from being viewed in terms of dynamic multivariate patterns whose trajectories are a combination of intrinsic and extrinsic factors that jointly determine how the brain temporally evolves during dynamic threat" and "We propose that viewing threat processing through the lens of dynamical systems offers important avenues to uncover properties of the dynamics of threat that are not unveiled with standard experimental designs and analyses". I can agree to the claim that we may be able to better describe the intrinsic and extrinsic dynamics of threat processing using this method, but what is now the contribution that this makes toward understanding these processes?

(2) How sure can we be that it is possible to separate extrinsically and intrinsically driven dynamics?

Reviewer #1 (Public review):

Summary:

The topic of nanobody-based PET imaging is important and holds great potential for real-world applications since nanobodies have many advantages over full sized immunoglobulins and small molecules.

Strengths:

The submitted manuscript contains quite a bit of interesting data from a collaborative team of well-respected researchers. The authors are to be congratulated for presenting results that may not have turned out the way they had hoped, and doing so in a transparent fashion.

Weaknesses:

However, the manuscript could be considered to be a collection of exploratory findings rather than a complete and mature scientific exposition. Most of the sample sizes were 3 per group, which is fine for exploratory work, but insufficient to draw strong statistically robust conclusions for definitive results.

Reviewer #2 (Public review):

Summary:

This is a strong and well-described study showing for the first time the use and publicly available resources to use a specific PET tracer to track proliferating transplanted cells in vivo, in a full murine immunecompetent environment.

In this study the authors described a previously developed set of VHH-based PET tracers to track transplants (cancer cells, embryo's) in a murine immune-competent environment.

Strengths:

Unique set of PET tracer and mouse strain to track transplanted cells in vivo without genetic modification of the transplanted cells. This is a unique asset, and a first-in-kind.

Weaknesses:

-some methodological aspects and controls are missing

-no clinical relevance?

Reviewer #1 (Public review):

Summary:

The paper is well-organized, with clearly defined sections. The systematic review methodology is thorough, with clear eligibility criteria, search strategy, and data collection methods. The risk of bias assessment is also detailed and useful for evaluating the strength of evidence. The involvement of a patient panel is noticeable and positive, ensuring the research addresses real-world concerns and aligning scientific inquiry with patient perspectives. The statistical approach used for analyzing seems appropriate.

The authors are encouraged to take into account the following points:

As the authors have acknowledged, there is a high risk of bias across all included studies, particularly in randomization, selective outcome reporting, and incomplete data, which could be highlighted more explicitly in the paper's discussion section, particularly the potential implications for the generalizability of the results. The authors can also suggest mitigation strategies for future studies (e.g., better randomization, blinding, reporting standards, etc.). None of the studies include female animals, and the use of young adult animals (instead of aged models) limits the applicability of the findings to the human stroke population, where stroke incidence is higher in older adults and perhaps the gender issue must be included to reflect the translational aspects. The authors can add to the paper's discussion section that perhaps future preclinical studies should include both sexes and aged animals to align better with the clinical population and improve the translation of findings. Another point is the comorbidity. Comorbidities such as diabetes and hypertension are prevalent in stroke patients. How can these be considered in preclinical designs? The authors should emphasize the importance of future research incorporating such comorbid models to enhance clinical relevance.

None of the studies had independent replication of their findings, which is a key limitation, especially for a field with high translational expectations. This should be highlighted as a critical next step for validating the efficacy of CCR5 antagonists.

The studies accessed limited cognitive outcomes (only one reported a cognitive outcome). Given the importance of cognitive recovery post-stroke, this is a gap to highlight in the discussion. Future studies should include more diverse and comprehensive behavioral assessments, including cognitive and emotional domains, to fully evaluate the therapeutic potential.

The timing of CCR5 administration across studies varies widely (from pre-stroke to several days post-stroke) complicating the interpretation and comparison of results. The authors are encouraged to add that future preclinical studies could focus on narrowing the therapeutic window to more clinically relevant time points.<br /> The paper identifies some alignment with clinical trials, but there are several gaps, too, particularly in the types of behavioral tests used in preclinical studies versus those in clinical trials. If this systematic review and meta-analysis aim to formulate a set of recommendations for future studies, it is important that the authors also propose specific preclinical behavioral tasks that could better align with clinical measures used in trials, like functional assessments related to human stroke outcomes.

The discussion needs some revisions. It could benefit from an expanded explanation of CCR5's mechanistic role in neuroplasticity and stroke recovery. For instance, linking CCR5 antagonism more closely with molecular pathways related to synaptic repair and remyelination would enhance the quality of the discussion and understanding of the drugs' potential.

While the tool is used to assess the risk of bias, it might be helpful to integrate a broader framework for evaluating the quality of included studies. This could include sample size justifications, statistical power analysis, or the use of pre-registration in animal studies. These elements can also introduce bias or minimize those if in place.

Please also highlight confounding factors that might have influenced the results in the included studies, such as variation in stroke models, dosing regimens, or behavioral assessment methods.

There is some discussion of the meta-analysis' limitations due to the few studies, but this point could be more thoroughly addressed. Please consider including a more critical discussion of the limitations of pooling data from heterogeneous study designs, stroke models, and outcome measures. What can this lead to? Is it reliable to do so, or does it lack scientific rigor? The authors are encouraged to formulate a balanced discussion adding, positive and negative aspects.<br /> The conclusion should more explicitly acknowledge that while CCR5 antagonists show potential, the findings are still preliminary due to the limitations in the preclinical studies (high bias risk, lack of diverse animal models). Overall, the conclusion can end with a call for rigorous, well-controlled, and replicated studies with improved alignment to clinical populations and trials to show that the conclusion remains inconclusive, considering what has been analyzed here.

Reviewer #2 (Public review):

Summary:

This is an interesting, timely, and high-quality study on the potential neuroprotective capabilities of C-C chemokine receptor type 5 (CCR5) antagonists in ischemic stroke. The focus is on preclinical investigations.

Strengths:

The results are timely and interesting. An outstanding feature is that stroke patient representatives have directly participated in the work. Although this is often called for, it is hardly realized in research practice, so the work goes beyond established standards.

The included studies were assessed regarding the therapeutic impact and their adherence to current quality assurance guidelines such as STAIR and SRRR, another important feature of this work. While overall results were promising, there were some shortcomings regarding guideline adherence.

The paper is very well written and concise yet provides much highly useful information. It also has very good illustrations and extremely detailed and transparent supplements.

Weaknesses:

Although the paper is of very high quality, a couple of items that may require the authors' attention to increase the impact of this exciting work further. Specifically:

Major aspects:

(1) I hope I did not miss that (apologies if I did), but when exactly was the search conducted? Is it possible to screen the recent literature (maybe up to 12/2024) to see whether any additional studies were published?

(2) Please clearly define the difference between "study" and "experiment," as this is not entirely clear. Is an "experiment" a distinct investigation within a particular publication (=study) that can describe more than one such "experiment"? Thanks for clarifying.

(3) Is there an opportunity to conduct a correlation analysis between the quality of a study (for instance, after transforming the ROB assessment into a kind of score) and reported effect sizes for particular experiments or studies? This might be highly interesting.

Reviewer #1 (Public review):

Summary:

The authors aim to explore the effects of the electrogenic sodium-potassium pump (Na+/K+-ATPase) on the computational properties of highly active spiking neurons, using the weakly-electric fish electrocyte as a model system. Their work highlights how the pump's electrogenicity, while essential for maintaining ionic gradients, introduces challenges in neuronal firing stability and signal processing, especially in cells that fire at high rates. The study identifies compensatory mechanisms that cells might use to counteract these effects, and speculates on the role of voltage dependence in the pump's behavior, suggesting that Na+/K+-ATPase could be a factor in neuronal dysfunctions and diseases

Strengths:

(1) The study explores a less-examined aspect of neural dynamics-the effects of Na+/K+-ATPase electrogenicity. It offers a new perspective by highlighting the pump's role not only in ion homeostasis but also in its potential influence on neural computation.<br /> (2) The mathematical modeling used is a significant strength, providing a clear and controlled framework to explore the effects of the Na+/K+-ATPase on spiking cells. This approach allows for the systematic testing of different conditions and behaviors that might be difficult to observe directly in biological experiments.<br /> (3) The study proposes several interesting compensatory mechanisms, such as sodium leak channels and extracellular potassium buffering, which provide useful theoretical frameworks for understanding how neurons maintain firing rate control despite the pump's effects.

Weaknesses:

(1) While the modeling approach provides valuable insights, the lack of experimental data to validate the model's predictions weakens the overall conclusions.<br /> (2) The proposed compensatory mechanisms are discussed primarily in theoretical terms without providing quantitative estimates of their impact on the neuron's metabolic cost or other physiological parameters.

Reviewer #2 (Public review):

Summary:

The paper 'The electrogenicity of the Na+/K+-ATPase poses challenges for computation in highly active spiking cells' by Weerdmeester, Schleimer, and Schreiber uses computational models to present the biological constraints under which electrocytes-specialized highly active cells that facilitate electro-sensing in weakly electric fish-may operate. The authors suggest potential solutions these cells could employ to circumvent these constraints.

Electrocytes are highly active or spiking (greater than 300Hz) for sustained periods (for minutes to hours), and such activity is possible due to an influx of sodium and efflux of potassium ions into these cells for each spike. This ion imbalance must be restored after each spike, which in electrocytes, as with many other biological cells, is facilitated by the Na-K pumps at the expense of biological energy, i.e., ATP molecules. For each ATP molecule the pump uses, three positively charged sodium ions from the intracellular space are exchanged for two positively charged potassium ions from the extracellular volume. This creates a net efflux of positive ions into the extracellular space, resulting in hyperpolarized potentials for the cell over time. This does not pose an issue in most cells since the firing rate is much slower, and other compensatory mechanisms and other pumps can effectively restore the ion imbalances. In electrocytes of weakly electric fish, however, that operate under very different circumstances, the firing rate is exceptionally high. On top of this, these cells are also involved in critical communication and survival behaviors, emphasizing their reliable functioning.

In a computation model, the authors test four increasingly complex solutions to the problem of counteracting the hyperpolarized states that occur due to continuous NaK pump action to sustain baseline activity. First, they propose a solution for a well-matched Na leak channel that operates in conjunction with the NaK pump, counteracting the hyperpolarizing states naturally. Additionally, their model shows that when such an orchestrated Na leak current is not included, quick changes in the firing rates could have unexpected side effects. Secondly, they study the implication of this cell in the context of chirps - a means of communication between individual fishes. Here, an upstream pacemaking neuron entrains the electrocyte to spike, which ceases to produce a so-called chirp - a brief pause in the sustained activity of the electrocytes. In their model, the authors show that it is necessary to include the extracellular potassium buffer to have a reliable chirp signal. Thirdly, they tested another means of communication in which there was a sudden increase in the firing rate of the electrocyte followed by a decay to the baseline. For reliable occurrence of this, they emphasize that a strong synaptic connection between the pacemaker neuron and the electrocyte is warranted. Finally, since these cells are energy-intensive, they hypothesize that electrocytes may have energy-efficient action potentials, for which their NaK pumps may be sensitive to the membrane voltages and perform course correction rapidly.

Strengths:

The authors extend an existing electrocyte model (Joos et al., 2018) based on the classical Hodgkin and Huxley conductance-based models of Na and K currents to include the dynamics of the NaK pump. The authors estimate the pump's properties based on reasonable assumptions related to the leak potential. Their proposed solutions are valid and may be employed by weakly electric fish. The authors explore theoretical solutions that compound and suggest that all these solutions must be simultaneously active for the survival and behavior of the fish. This work provides a good starting point for exploring and testing in in vivo experiments which of these proposed solutions the fish use and their relative importance.

Weaknesses:

The modeling work makes assumptions and simplifications that should be listed explicitly. For example, it assumes only potassium ions constitute the leak current, which may not be true as other ions (chloride and calcium) may also cross the cell membrane. This implies<br /> that the leak channels' reversal potential may differ from that of potassium. Additionally, the spikes are composed of sodium and potassium currents only and no other ion type (no calcium). Further, these ion channels are static and do not undergo any post-translational modifications. For instance, a sodium-dependent potassium pump could fine-tune the potassium leak currents and modulate the spike amplitude (Markham et al., 2013).

This model considers only NaK pumps. In many cell types, several other ion pumps/exchangers/symporters are simultaneously present and actively participate in restoring the ion gradients. It may be true that only NaK pumps are expressed in the weakly electric fish Eigenmannia virescens. This limits the generalizability of the results to other cell types. While this does not invalidate the results of the present study, biological processes may find many other solutions to address the non-electroneutral nature of the NaK pump. For example, each spike could include a small calcium ion influx that could be buffered or extracted via a sodium-calcium exchanger.

Finally, including testable hypotheses for these computational models would strengthen this work.

Reviewer #1 (Public review):

Summary:

This work made a lot of efforts to explore the multifaceted roles of the inferior colliculus (IC) in auditory processing, extending beyond traditional sensory encoding. The authors recorded neuronal activity from the IC at single unit level when monkeys were passively exposed or actively engaged in behavioral task. They concluded that 1）IC neurons showed sustained firing patterns related to sound duration, indicating their roles in temporal perception, 2) IC neuronal firing rates increased as sound sequences progress, reflecting modulation by behavioral context rather than reward anticipation, 3) IC neurons encode reward prediction error and their capability of adjusting responses based on reward predictability, 4) IC neural activity correlates with decision-making. In summary, this study tried to provide a new perspective on IC functions by exploring its roles in sensory prediction and reward processing, what are not traditionally associated with this structure.

Strengths:

The major strength of this work is that the authors performed electrophysiological recordings from the IC of behaving monkeys. Compared with the auditory cortex and thalamus, the IC in monkeys has not been adequately explored.

Comments on revised version:

The authors have adequately addressed all my concerns.

Reviewer #2 (Public review):

Summary:

The inferior colliculus (IC) has been explored for its possible functions in behavioral tasks and has been suggested to play more important roles rather than simple sensory transmission. The authors show us two major findings based on their experiments. The first one is climbing effect, which means that neurons' activities continue to increase along time course. The second one is reward effect, which refers to sudden increase of IC neurons' activities when the rewarding is given. Climbing effect is a surprising finding, but reward effect has not been explored clearly here.

Strengths:

Complex cognitive behaviors can be regarded as simple ideals of generating output based on information input, which depends on all kinds of input from sensory systems. The auditory system has hierarchic structures no less complex than those areas in charge of complex functions. Meanwhile, IC receives projections from higher areas, such as the auditory cortex, which implies IC is involved in complex behaviors. Experiments in behavioral monkeys are always time-consuming work with hardship, and this will offer more approximate knowledge of how the human brain works.

Weaknesses:

These findings are more about correlation but not causality of IC function in behaviors.

About 'reward effect', it is still unknown if the true nature of reward effect is the simple response to the sound elicited by the electromagnetic valve of rewarding system. The authors claimed the testing space is sound-proofed and believed this is enough to support their opinion. Since the electromagnetic valve was connected to the water tube, and the water tube was attached to a monkey-chair or even in monkey's mouth, the click sound may transmit to the monkey independently on air. There are simple ways to test what happens. One is to add a few trials without reward and see what happens, or to vary the latency between sound sequence and reward.

Only one of the major findings is convincing, this definitely reduces the credibility of the authors' statements.

Reviewer #1 (Public review):

In this manuscript, the authors recorded cerebellar unipolar brush cells (UBCs) in acute brain slices. They confirmed that mossy fiber (MF) inputs generate a continuum of UBC responses. Using systematic and physiological trains of MF electrical stimulation, they demonstrated that MF inputs either increased or decreased UBC firing rates (UBC ON vs. OFF) or induced complex, long-lasting modulation of their discharges. The MF influence on UBC firing was directly associated with a specific combination of metabotropic glutamate receptors, mGluR2/3 (inhibitory) and mGluR1 (excitatory). Ultimately, the amount and ratio of these two receptors controlled the time course of the effect, yielding specific temporal transformations such as phase shifts. The experiments are well-executed and properly analyzed.

Strengths:

(1) A wide range of MF stimulation based on activity patterns observed in vivo was explored, including burst duration and frequency dependency, which could serve as a valuable foundation for explicit modeling of temporal transformations in the granule cell layer.<br /> (2) The pharmacological blockade of mGluR2/3, mGluR1, AMPA, and NMDA receptors helped identify the specific roles of these glutamate receptors.<br /> (3) The experiments convincingly demonstrate the key role of mGluR1 receptors in temporal information processing by UBCs.

Weaknesses:

(1) This study is a follow up of previous work (Guo et al., Nat. Commun., 2021).<br /> (2) The MF activity used to mimic natural stimulation was previously collected from primates, whereas the recordings were conducted in mice.

Comments on revisions:

The authors included a discussion about inhibition, but I still disagree with their claim that it was not possible to study the MF-UBC connection with inhibition unblocked. This group has already conducted experiments on Golgi cell inhibition in slices.

Reviewer #2 (Public review):

This study addresses the question of how UBCs transform synaptic input patterns into spiking output patterns and how different glutamate receptors contribute to their transformations. The first figure utilizes recorded patterns of mossy fiber firing during eye movements in the flocculus of rhesus monkeys obtained from another laboratory. In the first figure, these patterns are used to stimulate mossy fibers in the mouse cerebellum during extracellular recordings of UBCs in acute mouse brain slices. The remaining experiments stimulate mossy fiber inputs at different rates or burst durations, which is described as 'mossy-fiber like', although they are quite simpler than those recorded in vivo. As expected from previous work, AMPA mediates the fast responses, and mGluR1 and mGluR2/3 mediate the majority of longer-duration and delayed responses. The manuscript is well organized and the discussion contextualizes the results effectively.

Comments on revisions:

The authors have adequately addressed my concerns.

Reviewer #1 (Public review):

Summary:

In the submitted manuscript, Solomon et al carefully detail shifts in tissue-specific myeloid populations associated with trained immunity using intraperitoneal BCG injection as a model for induction. They define the kinetics of shifts in myeloid populations within the spleen and the transcriptional response associated with IP BCG exposure. In lineage tracing experiments, they demonstrate that tissue-resident macrophages, red-pulp macrophages (RPM) that are rapidly depleted after BCG exposure, are replenished from recruited monocytes and expansion of tissue-resident cells; they use transcriptional profiling to characterize those cells. In contrast to previous descriptions of BCG-driven immune training, they do not find BCG in the bone marrow in their model, suggesting that there is not direct training of myeloid precursor populations in the bone marrow. They then link the observed trained immunity phenotype (restriction of heterologous infection with ST) with early activation of STAT1 through IFN-γ.

Strengths:

The work includes careful detaining of shifts and origins of myeloid populations within tissue associated with trained immunity and is a meaningful advance for the field.

Caveats:<br /> Given that the authors demonstrate that BCG persists in the spleen, it is possible that some level of BCG persistence in the spleen is a necessary contributor (together with signaling through STAT1) to the observed tissue-specific T1 phenotype.

Whether ongoing signaling through the axes are required for ongoing protection is not specifically addressed in this work. There is recent work by other groups that partially addresses these caveats, and it would be helpful context to reference those papers.

Reviewer #2 (Public review):

Summary:

In this study, Solomon and colleagues demonstrate that trained immunity induced by BCG can reprogram myeloid cells within localised tissue, which can sustain prolonged protective effects. The authors further demonstrate an activation of STAT1-dependent pathways.

Strengths:

The main strength of this paper is the in-depth investigation of cell populations affected by BCG training, and how their transcriptome changes at different time points post-training. Through use of flow cytometry and sequencing methods, the authors identify a new cell population derived from classical monocytes. They also show that long-term trained immunity protection in the spleen is dependent on resident cells. Through sequencing, drug and recombinant inhibition of IFNg pathways, the authors reveal STAT1-dependent responses are required for changes in the myeloid population upon training, and recruitment of trained monocytes.

Weaknesses:

A significant amount of work has already been performed for this study. No significant weaknesses were found.

Comments on revisions:

I thank the authors for carefully considering all reviewer comments. I have no further recommendations for the authors.

Reviewer #1 (Public review):

This manuscript by Kleinman & Foster investigates the dependence of hippocampal replay on VTA activity. They recorded neural activity from the dorsal CA1 region of the hippocampus while chemogenetically silencing VTA dopamine neurons as rats completed laps on a linear track with reward delivery at each end. Reward amount changed across task epochs within a session on one end of the track. The authors report that VTA activity is necessary for an increase in sharp-wave rate to remain localized to the feeder that undergoes a change in reward magnitude, an effect that was especially pronounced in a novel environment. They follow up on this result with a second experiment in which reward magnitude varies unpredictably at one end of the linear track and report that changes in sharp-wave rate at the variable location reflect both the amount of reward rats just received there, in addition to a smaller modulation that is reminiscent of reward prediction error coding, in which the previous reward rats received at the variable location affects the magnitude of the subsequent change in sharp-wave rate that occurs on the present visit.

This work is technically innovative, combining neural recordings with chemogenetic inactivation. The question of how VTA activity affects replay in the hippocampus is interesting and important given that much of the work implicating hippocampal replay in memory consolidation and planning comes from reward-motivated behavioral tasks.

Comments on revisions:

Overall, I think the authors have done everything they could to address reviewer concerns, short of collecting more data. The more consistent statistical approach makes the paper easier to read and follow. It's helpful to have more details/rationale for the variability in CNO dose and timing. I think some of the results are still not fully convincing, especially the reward volatility experiment (which the authors also note requires additional validation). Given the small number of rats, the small effect sizes, and the complexity of the experimental manipulations, I still have concerns about whether these effects would hold with larger groups sizes.

Reviewer #2 (Public review):

(1) Summary<br /> Kleinman and Foster's study investigates the role of dopamine signaling in the ventral tegmental area (VTA) on hippocampal replay and sharp-wave ripples (SWR) in rats exposed to changes in reward magnitude and environmental novelty. The authors utilize chemogenetic silencing techniques to modulate dopamine neuron activity in the VTA while conducting simultaneous electrophysiological recordings from the hippocampal CA1 region. Their findings suggest that VTA dopamine signaling is critical for modulating hippocampal replay in response to changes in reward context and novelty, with specific disruptions observed in replay dynamics when VTA is inhibited, particularly in novel environments.

(2) Strengths<br /> The research addresses a significant gap in our understanding of the neurobiological underpinnings of memory and spatial learning, highlighting the importance of dopamine-mediated processes. The methodological approach is robust, combining chemogenetic silencing with precise electrophysiological measurements, which allows for a detailed examination of the neural circuits involved. The study provides important insights into how hippocampal replay and SWR are influenced by reward prediction errors, as well as the role of dopamine in these processes. Specifically, the authors note that VTA silencing unexpectedly did not prevent increases in ripple activities where reward was increased, but induced significant aberrant increases in environments where reward levels were unchanged, highlighting a novel dependency of hippocampal replay on dopamine and a VTA-independent reward prediction error signal in familiar environments. These findings are critical for understanding the consolidation of episodic memory and the neural basis of learning.

(3) Weaknesses<br /> Despite the strengths in methodology and conceptual framework, the study has several weaknesses that could affect the interpretation of the results. There is a need for more rigorous histological validation to confirm the extent and specificity of viral expression (from all animals ideally), which is crucial for ensuring the accuracy of the findings. Variability in the dosing and timing of chemogenetic interventions could also lead to inconsistencies in the data, suggesting a need for more standardized experimental protocols.

Comments on revisions:

I commend the authors for their work in addressing my and the other reviewers' comments. I think these changes have improved the paper, and no further changes are absolutely necessary.

Reviewer #3 (Public review):

Summary:

The authors of this work are trying to understand the role dopaminergic terminals coming from VTA have on hippocampal mechanisms of memory consolidation, with emphasis on the replay of hippocampal patterns of activity during periods of consummatory behavior in reward locations. Previous work suggested that replay of relevant spatial trajectories supports reward localization and influences behavior.

The authors then tried to separate two conditions that were known to cause an increase in replay activity - spatial novelty encoding and variation of reward magnitude - and evaluate how these changed when VTA dopamine neurons were inactivated by a chemogenetic tool. They found that the rate of reverse replay (trajectory going away from the goal location) is increased with reward only in novel, but not in familiar environments. Overall this suggests that the VTA dopamine signal is critical during learning of novel locations, but not during explorations of already familiar environments.

Strengths:

The inactivation of VTA projections during goal-oriented behavior and in-vivo analysis of patterns of hippocampal activity during both novelty and reward variability. This work adds to the body of evidence that reverse replay constitutes an important mechanism in learning spatial goal locations. Furthermore, this work also points to the role of VTA in reward prediction error with consequences for spatial navigation and consolidation of spatial memories.

The authors addressed very carefully all the points raised during the revision and I am very pleased with the revised manuscript.

Reviewer #1 (Public review):

The paper proposes an interesting perspective on the spatio-temporal relationship between FC in fMRI and electrophysiology. The study found that while similar networks configurations are found in both modalities, there is a tendency for the networks to spatially converge more commonly at synchronous than asynchronous timepoints. However, my confidence in the findings and their interpretation is undermined by an incomplete justification for the expected outcomes for each of the proposed scenarios.

Main Concern

Fig 1 makes sense to me conceptually, including the schematics of the trajectories, i.e.:

- Scenario1. Temporally convergent, same trajectories through connectome state space<br /> - Scenario2. Temporally divergent, different trajectories through connectome state space

However, based on my understanding (and apologies if I am mistaken), I am concerned that these scenarios do not necessarily translate into the schematic CRP plots shown in fig 2C, or the statements in the main text, i.e.:

- For scenario1, "epochs of cross-modal spatial similarity should occur more frequently at on-diagonal (synchronous) than off-diagonal (asynchronous) entries, resulting in an on-/off-diagonal ratio larger than unity"<br /> - For scenario2, "epochs of spatial similarity could occur equally likely at on-diagonal and off-diagonal entries (ratio≈1)"

Where do the authors get these statements and the schematics in fig2C from? They do not seem to be fully justified via previous literature, theory, or simulations?

In particular, I am not convinced based on the evidence currently in the paper, that the ratio of off- to on-diagonal entries (and under what assumptions) is a definitive way to discriminate between scenarios 1 and 2.

For example, what about the case where the same network configuration reoccurs in both modalities at multiple time points. It seems to me that you would get a CRP with entries occurring equally on the on-diagonal as on the off-diagonal, regardless of whether the dynamics are matched between the two modalities or not (i.e. regardless of scenario 1 or 2 being true).

This thought experiment example might have a flaw in it, and the authors might ultimately be correct, but nonetheless a systematic justification needs to be provided for using the ratio of off- to on-diagonal entries to discriminate between scenario 1 and 2 (and under what assumptions it is valid).

In the absence of theory, the authors could use surrogate data for scenario 1 and 2. For example:

a. For scenario 1, run the CRP using a single modality. E.g. feed in the EEG into the analysis as both modality 1 AND modality 2. This should provide at least one example of CRP under scenario 1 (although it does not ensure that all CRPs under this scenario will look like this, it is at least a useful sanity check).<br /> b. For scenario 2, run the CRP using a single modality plus a shuffled version. E.g. feed in the EEG into the analysis as both modality 1 AND a temporally shuffled version of the EEG as modality 2. The temporal shuffling of the EEG could be done by simple splitting the data into blocks of say ~10s and then shuffling them into a new order. This should provide a version of the CRP under scenario 2 (although it does not ensure that all CRPs under this scenario will look like this, it is at least a useful sanity check)

The authors have provided CRP plots for option a. It shows a CRP, as expected, consistent with scenario 1. This is a useful sanity check. However, as mentioned above, it does not ensure that all CRPs under this scenario will look like this.

However, the authors have not shown a CRP as per option b. As such, there is an incomplete justification for the expected outcomes of the scenarios.

Note that another option, which has not been carried out, is to use full simulations, with clearly specified assumptions, for scenario1 and 2. One way of doing this is to use a simplified (state-space) setup where you randomly simulate N spatially fixed networks that are independently switching on and off over time (i.e. "activation" is 0 or 1). Note that this would result in a N-dimensional connectome state space.

Using this, you can simulate and compute the CRPs for the two scenarios:

a. Scenario 1: where the simulated activation timecourses are set to be the same between both modalities<br /> b. Scenario 2: where the simulated activation timecourses are simulated separately for each of the modalities

Minor Concern

Leakage correction. The paper states: "To mitigate this issue, we provide results from source-localized data both with and without leakage correction (supplementary and main text, respectively)." It is great that the authors provide both. However, given that FC in EEG is almost totally dominated by spatial leakage (see Hipp paper), the main results/figures for the scalp EEG should be done using spatial leakage corrected EEG data.

Reviewer #2 (Public review):

Summary:

The study investigates the brain's functional connectivity (FC) dynamics across different timescales using simultaneous recordings of intracranial EEG/source-localized EEG and fMRI. The primary research goal was to determine which of three convergence/divergence scenarios is the most likely to occur.

The results indicate that despite similar FC patterns found in different data modalities, the timepoints were not aligned, indicating spatial convergence but temporal divergence.

The researchers also found that FC patterns in different frequencies do not overlap significantly, emphasizing the multi-frequency nature of brain connectivity. Such asynchronous activity across frequency bands supports the idea of multiple connectivity states that operate independently and are organized into a multiplex system.

Strengths:

The data supporting the authors' claims are convincing and come from simultaneous recordings of fMRI and iEEG/EEG, which has been recently developed and adapted.

The analysis methods are solid and involved a novel approach to analyzing the co-occurrence of FC patterns across modalities (cross-modal recurrence plot, CRP) and robust statistics, including replication of the main results using multiple operationalizations of the functional connectome (e.g., amplitude, orthogonalized, and phase-based coupling).

In addition, the authors provided a detailed interpretation of the results, placing them in the context of recent advances and understanding of the relationships between functional connectivity and cognitive states.

The authors also did a control analysis and verified the effect of temporal window size or different functional connecvitity operationalizations. I also applaud their effort to make the analysis code open-sourced.

Reviewer #1 (Public review):

Summary:

The anatomical connectivity of the claustrum and the role of its output projections has, thus far, not been studied in detail. The aim of this study was to map the outputs of the endopiriform (EN) region of the claustrum complex, and understand their functional role. Here the authors have combined sophisticated intersectional viral tracing techniques, and ex vivo electrophysiology to map the neural circuitry of EN outputs to vCA1, and shown that optogenetic inhibition of the EN→vCA1 projection impairs both social and object recognition memory. Interestingly the authors find that the EN neurons target inhibitory interneurons providing a mechanism for feedforward inhibition of vCA1.

Strengths:

The strength of this study was the application of a multilevel analysis approach combining a number of state-of-the-art techniques to dissect the contribution of the EN→vCA1 to memory function.

In addition the authors conducted behavioural analysis of locomotor activity, anxiety and fear memory, and complemented the analysis of discrimination with more detailed description of the patterns of exploratory behaviour.

Reviewer #2 (Public review):

Summary:

Yamawaki et al., conducted a series of neuroanatomical tracing and whole cell recording experiments to elucidate and characterise a relatively unknown pathway between the endopiriform (EN) and CA1 of the ventral hippocampus (vCA1) and to assess its functional role in social and object recognition using fibre photometry and dual vector chemogenetics. The main findings were that the EN sends robust projections to the vCA1 that collateralise to the prefrontal cortex, lateral entorhinal cortex and piriform cortex, and these EN projection neurons terminate in the stratum lacunosum-moleculare (SLM) layer of distal vCA1, synapsing onto GABAergic neurons that span across the Pyramidal-Stratum Radiatum (SR) and SR-SML borders. It was also demonstrated that EN input disynaptically inhibits vCA1 pyramidal neurons. vCA1 projecting EN neurons receive afferent input from piriform cortex, and from within EN. Finally, fibre photometry experiments revealed that vCA1 projecting EN neurons are most active when mice explore novel objects or conspecifics, and pathway-specific chemogenetic inhibition led to an impairment in the ability to discriminate between novel vs. familiar objects and conspecifics.

This is an interesting mechanistic study that provides valuable insights into the function and connectivity patterns of afferent input from the endopiriform to the CA1 subfield of the ventral hippocampus. The authors propose that the EN input to the vCA1 interneurons provides a feedforward inhibition mechanism by which memory-based novelty detection could be promoted. The experiments are carefully conducted, and the methodological approaches used are sound. The conclusions of the paper are supported by the data presented.

Reviewer #1 (Public review):

Summary:

Liu and colleagues applied the hidden Markov model on fMRI to show three brain states underlying speech comprehension. Many interesting findings were presented: brain state dynamics were related to various speech and semantic properties, timely expression of brain states (rather than their occurrence probabilities) was correlated with better comprehension, and the estimated brain states were specific to speech comprehension but not at rest or when listening to non-comprehensible speech.

Strengths:

Recently, the HMM has been applied to many fMRI studies, including movie watching and rest. The authors cleverly used the HMM to test the external/linguistic/internal processing theory that was suggested in comprehension literature. I appreciated the way the authors theoretically grounded their hypotheses and reviewed relevant papers that used the HMM on other naturalistic datasets. The manuscript was well written, the analyses were sound, and the results had clear implications.

Reviewer #2 (Public review):

Liu et al. applied hidden Markov models (HMM) to fMRI data from 64 participants listening to audio stories. The authors identified three brain states, characterized by specific patterns of activity and connectivity, that the brain transitions between during story listening. Drawing on a theoretical framework proposed by Berwick et al. (TICS 2023), the authors interpret these states as corresponding to external sensory-motor processing (State 1), lexical processing (State 2), and internal mental representations (State 3). States 1 and 3 were more likely to transition to State 2 than between one another, suggesting that State 2 acts as a transition hub between states. Participants whose brain state trajectories closely matched those of an individual with high comprehension scores tended to have higher comprehension scores themselves, suggesting that optimal transitions between brain states facilitated narrative comprehension.

Overall, the conclusions of the paper are well-supported by the data. Several recent studies (e.g., Song, Shim, and Rosenberg, eLife, 2023) have found that the brain transitions between a small number of states; however, the functional role of these states remains under-explored. An important contribution of this paper is that it relates the expression of brain states to specific features of the stimulus in a manner that is consistent with theoretical predictions.

The correlation between narrative features and brain state expression was reliable, but relatively low (~0.03). As discussed in the manuscript, this could be due to measurement noise, as well as narrative features accounting for a small proportion of cognitive processes underlying the brain states.

A strength of the paper is that the authors repeated the HMM analyses across different tasks (Figure 5) and an independent dataset (Figure S3) and found that the data was consistently best fit by 3 brain states. Across tasks, however, the spatial regions associated with each state varied. For example, state 2 during narrative comprehension was similar to both states 2 and 3 during rest (Fig. 5A), suggesting that the organization of the three states was task dependent.

The three states identified in the manuscript correspond rather well to areas with short, medium, and long temporal timescales (see Hasson, Chen & Honey, TiCs, 2015). Given the relationship with behavior, where State 1 responds to acoustic properties, State 2 responds to word-level properties, and State 3 responds to clause-level properties, a "single-process" account where the states differ in terms of the temporal window for which one needs to integrate information over may offer a more parsimonious account than a multi-process account where the states correspond to distinct processes. This possibility is mentioned briefly in the introduction, but not developed further.

Reviewer #1 (Public review):

The authors in this paper investigate the nature of the activity in the rodent EPN during a simple freely moving cue-reward association task. Given that primate literature suggest movement coding whereas other primate and rodent studies suggest mainly reward outcome coding in the EPNs, it is important try to tease apart the two views. Through careful analysis of behavior kinematics, position, and the neural activity in the EPNs, the authors reveal an interesting and complex relationship between the EPN and mouse behavior.

Strengths:

(1) The authors use a novel freely moving task to study EPN activity, which displays rich movement trajectories and kinematics. Given that previous studies have mostly looked at reward coding during head fixed behavior, this study adds a valuable dataset to the literature.

(2) The neural analysis is rich and thorough. Both single neuron level and population level (i.e. PCA) analysis are employed to reveal what EPN encodes.

Discussion:<br /> EPN is one of the major output nuclei of the basal ganglia. What information is present within EPN is still unclear, and under investigation. The authors have used electrophysiology to determine the nature of information present within EPN that is likely to be valuable to the field. Future studies should try to address whether this information is specific to certain cell types within EPN or whether there is topography within EPN that reflects the kinematic information present within EPN. This will require more careful dissection of EPN activity based on anatomy. Future experiments should also consider tasks that isolate a single limb (i.e. joystick tasks) in order to better understand the kinematic encoding of forelimb movement. This, combined with recording in forelimb encoding region of EPN, should give us insights into the nature of kinematic control of EPN. Overall, this study will be useful to inspire future investigations in the function of EPN.

Reviewer #2 (Public review):

This paper examined how the activity of neurons in the entopeduncular nucleus (EPN) of mice relates to kinematics, value, and reward. The authors recorded neural activity during an auditory cued two-alternative choice task, allowing them to examine how neuronal firing relates to specific movements like licking or paw movements, as well as how contextual factors like task stage or proximity to a goal influence the coding of kinematic and spatiotemporal features. The data shows that the firing of individual neurons is linked to kinematic features such as lick or step cycles. However, the majority of neurons exhibited activity related to both movement types, suggesting that EPN neuronal activity does not merely reflect muscle-level representations. This contradicts what would be expected from traditional action selection or action specification models of the basal ganglia.

The authors also show that spatiotemporal variables account for more variability compared to kinematic features alone. Using demixed Principal Component Analysis, they reveal that at the population level, the three principal components explaining the most variance were related to specific temporal or spatial features of the task, such as ramping activity as mice approached reward ports, rather than trial outcome or specific actions. Notably, this activity was present in neurons whose firing was also modulated by kinematic features, demonstrating that individual EPN neurons integrate multiple features. A weakness is that what the spatiotemporal activity reflects is not well specified. The authors suggest some may relate to action value due to greater modulation when approaching a reward port, but acknowledge action value is not well parametrized or separated from variables like reward expectation.

A key goal was to determine whether activity related to expected value and reward delivery arose from a distinct population of EPN neurons or was also present in neurons modulated by kinematic and spatiotemporal features. In contrast to previous studies (Hong & Hikosaka 2008 and Stephenson-Jones et al., 2016), the current data reveals that individual neurons can exhibit modulation by both reward and kinematic parameters. Two potential differences may explain this discrepancy: First, the previous studies used head-fixed recordings, where it may have been easier to isolate movement versus reward-related responses. Second, those studies observed prominent phasic responses to the delivery or omission of expected rewards - responses that are present but not common in the current paper. This suggests a possibility that the VGlut2+ EPN neurons that project to the LHb were under/not sampled, antidromic or optogenetic tagging would have been needed to confirm the identity of the populations that were recorded. Alternatively, in the head-fixed recordings, kinematic/spatial coding may have gone undetected due to the forced immobility.

Overall, this paper offers needed insight into how the basal ganglia output encodes behavior. The EPN recordings from freely moving mice clearly demonstrate that individual neurons integrate reward, kinematic, and spatiotemporal features, challenging traditional models. However, the specific relationship between the spatiotemporal activity and factors like action value remains unclear.

Reviewer #1 (Public review):

Kreeger and colleagues have explored the balance of excitation and inhibition in the cochlear nucleus octopus cells of mice using morphological, electrophysiological and computational methods. On the surface, the conclusion, that synaptic inhibition is present, does not seem like a leap. However, the octopus cells have been in the past portrayed as lacking synaptic inhibition. This view was supported by the paucity of glycinergic fibers in the octopus cell area and the lack of apparent IPSPs. Here, Kreeger et al., used beautiful immunohistochemical and mouse genetic methods to quantify the inhibitory and excitatory boutons over the complete surface of individual octopus cells and further analyzed the proportions of the different subtypes of spiral ganglion cell inputs. I think the analysis of synaptic distribution and the origin of the excitatory inputs stands as one of the most complete descriptions of any neuron, leaving little doubt about the presence of glycinergic boutons.

Kreeger et al then examined inhibition physiologically. Recordings from these neurons are notoriously difficult to make because of the enormous leak currents that shunt membrane stimuli and currents, and complicate voltage clamp. The authors have tried to overcome these limitations using drugs to block leak conductances, and computational approaches based on realistic parameters. They conclude that dendritic inhibition can modify the size and kinetics of excitatory signals, and may play out in computations made on temporally dispersed stimuli as might be experienced during a ramp in sound frequency or complex natural sounds like vocalizations.

Reviewer #2 (Public review):

Kreeger et.al provided mechanistic evidence for flexible coincidence detection of auditory nerve synaptic inputs by octopus cells in the mouse cochlear nucleus. The octopus cells are highly specialized neurons that, with appropriate stimuli, can fire repetitively at very high rates (> 800 Hz in vivo), yield responses dominated by the onset of sound for simple stimuli, and integrate auditory nerve inputs over a wide frequency span. Previously, it was thought that octopus cells received little inhibitory input, and their integration of auditory input depended principally on temporally precise coincidence detection of excitatory auditory nerve inputs, coupled with a low input resistance established by high levels of expression of certain potassium channels and hyperpolarization-activated channels.

This study provides convincing evidence that octopus cells do in fact receive glycinergic synaptic input that can influence the efficacy of excitatory dendritic synaptic activity. By coupling selected genetic mouse models to characterize synaptic inputs and enable optogenetic stimulation of subsets of afferents, fluorescent microscopy, detailed reconstructions of the location of inhibitory synapses on the soma and dendrites of octopus cells, slice physiology, and computational modeling, they have been able to clarify the presence of functional inhibition and elucidate some of the features of the inhibitory inputs to octopus cells at a biophysical level. They also show through modeling that inhibition is predicted to both provide shunting of synaptic currents and to change the peak timing of dendritic EPSPs as they travel to the soma. Both of these effects are potentially critically important in integration in these fast, coincidence-detecting neurons, and the magnitudes of the effects could have physiological significance. Overall, this work extends thinking about the functional sensory processing roles of octopus cells beyond the pre-existing hypotheses that are focussed primarily on the coincidence detection of excitatory inputs.

The authors have addressed all of my prior concerns, including improving several aspects of the presentation. The modeling is better described, which is critical because it provides a foundation to help interpret some of the physiology and to propose specific functions.

Reviewer #1 (Public review):

Summary:

The authors use an innovative behavior assay (chamber preference test) and standard calcium imaging experiments on cultured dorsal root ganglion (DRG) neurons to evaluate the consequences of global knockout of TRPV1 and TRPM2, and overexpression of TRPV1, on warmth detection. They find a profound effect of TRPM2 elimination in the behavioral assay, whereas the elimination of TRPV1 has the largest effect on the neuronal responses. These findings are very important, as there is substantial ongoing discussion in the field regarding the contribution of TRP channels to different aspects of thermosensation.

Strengths:

The chamber preference test is an important innovation compared to the standard two-plate test, as it depends on thermal information sampled from the entire skin, as opposed to only the plantar side of the paws. With this assay, and the detailed analysis, the authors provide strong supporting evidence for a role of TRPM2 in warmth avoidance. The conceptual framework using the Drift Diffusion Model provides a first glimpse of how this decision of a mouse to change between temperatures can be interpreted and may form the basis for further analysis of thermosensory behavior.

Weaknesses:

The authors juxtapose these behavioral data with calcium imaging data using isolated DRG neurons. As the authors acknowledge, it remains unclear whether the clear behavioral effect seen in the TRPM2 knockout animals is directly related to TRPM2 functioning as a warmth sensor in sensory neurons. The effects of the TRPM2 KO on the proportion of warmth sensing neurons are very subtle, and TRPM2 may also play a role in the behavioral assay through its expression in thermoregulatory processes in the brain. Future behavioral experiments on sensory-neuron specific TRPM2 knockout animals will be required to clarify this important point.

Reviewer #3 (Public review):

Summary and strengths:

In the manuscript, Abd El Hay et al investigate the role of thermally sensitive ion channels TRPM2 and TRPV1 in warm preference and their dynamic response features to thermal stimulation. They develop a novel thermal preference task, where both the floor and air temperature are controlled, and conclude that mice likely integrate floor with air temperature to form a thermal preference. They go on to use knockout mice and show that TRPM2-/- mice play a role in the avoidance of warmer temperatures. Using a new approach for culturing DRG neurons they show the involvement of both channels in warm responsiveness and dynamics. This is an interesting study with novel methods that generate important new information on the different roles of TRPV1 and TRPM2 on thermal behavior.

Comments on revisions:

Thanks to the authors for addressing all the points raised. They now include more details about the classifier, better place their work in context of the literature, corrected the FOVs, and explained the model a bit further. The new analysis in Figure 2 has thrown up some surprising results about cellular responses that seem to reduce the connection between the cellular and behavioral data and there are a few things to address because of this:

TRPM2 deficient responses: The differences in the proportion of TRPM2 deficient responders compared to WT are only observed at one amplitude (39C), and even at this amplitude the effect is subtle. Most surprisingly, TRPM2 deficient cells have an enhanced response to warm compared to WT mice to 33C, but the same response amplitude as WT at 36C and 39C. The authors discuss why this disconnect might be the case, but together with the lack of differences between WT and TRPM2 deficient mice in Fig 3, the data seem in good agreement with ref 7 that there is little effect of TRPM2 on DRG responses to warm in contrast to a larger effect of TRPV1. This doesn't take away from the fact there is a behavioral phenotype in the TRPM2 deficient mice, but the impact of TRPM2 on DRG cellular warm responses is weak and the authors should tone down or remove statements about the strength of TRPM2's impact throughout the manuscript, for example:<br /> "Trpv1 and Trpm2 knockouts have decreased proportions of WSNs."<br /> "this is the first cellular evidence for the involvement of TRPM2 on the response of DRG sensory neurons to warm-temperature stimuli"<br /> "we demonstrate that TRPV1 and TRPM2 channels contribute differently to temperature detection, supported by behavioural and cellular data"<br /> "TRPV1 and TRPM2 affect the abundance of WSNs, with TRPV1 mediating the rapid, dynamic response to warmth and TRPM2 affecting the population response of WSNs."<br /> "Lack of TRPV1 or TRPM2 led to a significant reduction in the proportion of WSNs, compared to wildtype cultures".

The new analysis also shows that the removal of TRPV1 leads to cellular responses with smaller responses at low stimulus levels but larger responses with longer latencies at higher stimulus levels. Authors should discuss this further and how it fits with the behavioral data.

Analysis clarification: authors state that TRPM2 deficient WSNs show "Their response to the second and third stimulus, however, are similar to wildtype WSNs, suggesting that tuning of the response magnitude to different warmth stimuli is degraded in Trpm2-/- animals." but is there a graded response in WT mice? It looks like there is in terms of the %responders but not in terms of response amplitude or AUC. Authors could show stats on the figure showing differences in response amplitude/AUC/responders% to different stimulus amplitudes within the WT group.

New discussion point: sex differences are "similar to what has been shown for an operant-based thermal choice assay (11,56)", but in their rebuttal, they mention that ref 11 did not report sex differences. 56 does. Check this.

The authors added in new text about the drift diffusion model in the results, however it's still not completely clear whether the "noise" is due to a perceptual deficit or some other underlying cause. Perhaps authors could discuss this further in the discussion.

Reviewer #2 (Public review):

Summary:

This manuscript reports analyses of fMRI data from infants and toddlers watching naturalistic movies. Visual areas in the infant brain show distinct functions, consistent with previous studies using resting state and awake task-based infant fMRI. The pattern of activity in visual regions contains some features predicted by the regions' retinotopic responses. The revised version of the manuscript provides additional validation of the methodology, and clarifies the claims. As a result, the data provide clear support for the claims.

Strengths:

The authors have collected a unique dataset: the same individual infants both watched naturalistic animations and a specific retinotopy task. Using these data position the authors show that activity evoked by movies, in infants' visual areas, is correlated with the regions' retinopic response. The revised manuscript validates this methodology, using adult data. The revised manuscript also shows that an infant's movie watching data is not sufficient or optimal to predict their visual areas' retinotopic responses; anatomical alignment with a group of previous participants provides more accurate prediction of a new participant's retinotopic response.

Weaknesses:

A key step in the analysis of the movie-watching data is the selection of independent components of the movie evoked response that resemble retinotopic spatial patterns. While the trained researcher was unlikely to be biased by this infant's own retinotopy, he/she was actively looking for ICs that resemble average patterns of retinotopic response. To show that these ICs didn't arise by chance (i.e. in noise), the authors proposed an additional analysis in the revised manuscript, by misaligning the functional and anatomical data for a subset of participants. This only partially confirms the reliability of the original components, since when the (new) coder tried to be conservative to avoid false components, he/she identified just over half of the 'true' components (13 vs 22 estimated over the group of 6 infants).

Reviewer #1 (Public review):

Summary:

In this study, the authors use thermal proteome profiling to capture changes in protein stability following a brief (30 min) treatment of cells with various mitochondrial stressors. This approach identified PEBP1 as a potentiator of Integrated Stress Response (ISR) induction by various mitochondrial stressors, although the specific dynamics vary by stressor. PEBP1 deletion attenuates DELE1-HRI-mediated activation of the ISR, independent of its known role in the RAF/MEK/ERK pathway. These effects can be bypassed by HRI overexpression and do not affect DELE1 processing. Interestingly, in cells, PEBP1 physically interacts with eIF2alpha, but not its phosphorylated form (eIF2alpha-P), leading the authors to suggest that PEBP1 functions as a scaffold to promote eIF2alpha phosphorylation by HRI.

Strengths:

The authors present a clear and well-structured study, beginning with an original and unbiased approach that effectively addresses a novel question. The investigation of PEBP1 as a specific regulator of the DELE1-HRI signaling axis is particularly compelling, supported by extensive data from both genetic and pharmacological manipulations. Including careful titrations, time-course experiments, and orthogonal approaches strengthens the robustness of their findings and bolsters their central claims.

Moreover, the authors skillfully integrate publicly available datasets with their original experiments, reinforcing their conclusions' generality and broader relevance. This comprehensive combination of methodologies underscores the reliability and significance of the study's contributions to our understanding of stress signaling.

Weaknesses:

While the study presents exciting findings, there are a few areas that could benefit from further exploration. The HRI-DELE1 pathway was only recently discovered, leaving many unanswered questions. The observation that PEBP1 interacts with eIF2alpha, but not with its phosphorylated form, suggests a novel mechanism for regulating the Integrated Stress Response (ISR). However, as they note themselves, the authors do not delve into the biochemical or molecular mechanisms through which PEBP1 promotes HRI signaling. Given the availability of antibodies against phosphorylated HRI, it would have been interesting to explore whether PEBP1 influences HRI phosphorylation. Furthermore, since the authors already have recombinant PEBP1 protein (as shown in Figure 1D), additional in vitro experiments such as in vitro immunoprecipitation, FRET, or surface plasmon resonance (SPR) could have confirmed the interaction with eIF2alpha. Future studies might investigate whether PEBP1 directly interacts with HRI, stimulates its auto-phosphorylation or kinase activity, or serves as a template for oligomerization, potentially supported by structural characterization of the complex and mutational validation.

Another point of weakness is the unclear significance of the 1.5-2x enhanced interaction with eIF2alpha upon PEBP1 phosphorylation, as there is little evidence to show that this increase has any downstream effects. The ATF4-luciferase reporter experiments, comparing WT and S153D overexpression, may have reached saturation with WT, making it difficult to detect further stimulation by S153D. Additionally, expression levels for WT and mutant forms are not provided, making it challenging to interpret the results. It would also be interesting to explore whether combined mitochondrial stress and PMA treatment further enhance the ISR.

Lastly, while the authors claim that oligomycin does not significantly alter the melting temperature of recombinant PEBP1 in vitro, the data in Figure S1D suggest a small shift. Without variance measures across replicates or background subtraction, this claim is less convincing. The inclusion of statistical analyses would strengthen the interpretation of these results.

Impact on the field:

The study's relevance is underscored by the fact that overactive ISR is linked to a broad range of neurodegenerative diseases and cognitive disorders, a field actively being explored for therapeutic interventions, with several drugs currently in clinical trials. Similarly, mitochondrial dysfunction plays a well-established role in brain health and other diseases. Identifying new targets within these pathways, like PEBP1, could provide alternative therapeutic strategies for treating such conditions. Therefore, gaining a deeper understanding of the mechanisms through which PEBP1 influences ISR regulation is highly pertinent and could have far-reaching implications for the development of future therapies.

Reviewer #2 (Public review):

Summary:

In this work, Cheng et al use the TPP/MS-CETSA strategy to discover new components for the mitochondria arm of the Integrated Stress Response. By using short exposures of several drugs that potentially induce mitochondrial stress, they find significant CETSA shifts for the scaffold protein PEBP1 both for antimycinA and oligomycin, making PEBP1 a candidate for mitochondrial-induced ISR signaling. After extensive follow-up work, they provide good support that PEBP1 is likely involved in ISR, and possibly act through an interaction with the key ISR effector node EIF2a.

Strengths:

The work adds an important understanding of ISR signaling where PEBP1 might also constitute a druggable node to attenuate cellular stress. Although CETSA has great potential for dissecting cellular pathways, there are few studies where this has been explored, particularly with such an extensive follow-up, also giving the work methodological implications. Together I therefore think this study could have a significant impact.

Weaknesses:

The TPP/MS-CETSA experiment is quite briefly described and might have a too relaxed cut-off. The assays confirming interactions between PEBP1 and EIF2a might not be fully conclusive.

Reviewer #3 (Public review):

Summary:

In this paper, Chang and Meliala et al. demonstrate that PEBP1 is a modulator of the ISR, specifically through the induction of mitochondrial stress. The authors utilize thermal proteome profiling (TPP) by which they identify PEPB1 as a thermally stabilized protein upon oligomycin treatment, indicating its role in mitochondrial stress. Moreover, RNA-sequencing analysis indicated that PEBP1 may be specifically modulating the mitochondrial stress-induced ISR, as PEBP1 knock-out reduces phosphorylation of eIF2α. They also show that PEBP1 function is independent of ER stress specifically tunicamycin treatment and loss of PEBP1 does affect mitochondrial ISR but in an OMA1, DELE1 independent manner. Thus, the authors hypothesized that PEBP1 interacts directly with eIF2α, functioning as a scaffolding protein. However, direct co-immunoprecipitation failed to demonstrate PEBP1 and eIF2α potential interaction. The authors then used a NanoBiT luminescence complementation assay to show the PEBP1-eIF2a interaction and its disruption by S51 phosphorylation.

Strengths:

Taken together, this work is novel, and the data presented suggests PEBP1 has a role as a modulator of the mitochondrial ISR, enhancing the signal to elicit the necessary response.

Weaknesses:

The one major issue of this work is the lack of a mechanism showing precisely how PEBP1 amplifies the mitochondrial integrated stress response. The work, as it is described, presents data suggesting PEBP1's role in the ISR but fails to present a more conclusive mechanism.

Reviewer #2 (Public review):

Summary:

In this paper, the authors investigated the admixture history of domestic cattle since they were introduced into Iberia, by studying genomic data from 24 ancient samples dated to ~2000-8000 years ago and comparing them to modern breeds. They aimed to (1) characterize genomic variation of skeletal remains and concordance (or discordance) with morphological features; (2) test for hybridization between wild aurochs and domestic cattle; (3) test for correlation between genetic ancestry and stable isotope levels (which are indicative of ecological niche); and (4) test for previously hypothesized higher aurochs ancestry in a modern breed of fighting bulls.

Strengths:

Overall, this study collects valuable new data and tests several important hypotheses regarding the evolutionary history and genomic variation of domestic cattle in Iberia, such as admixture between domestic and wild populations, and correlation between genome-wide aurochs ancestry and aggressiveness.

Weaknesses:

Most conclusions are well supported by the data presented, with the strengths and caveats of each analysis clearly explained. The presence of admixed individuals in prehistorical periods strongly support hybridization between wild and domestic populations, although the evidence for sex-biased introgression and ecological niche sharing is relatively weak. Lastly, the authors presented convincing evidence for relatively constant aurochs ancestry across all modern breeds, including the Lidia breed that has been bred for aggressiveness for centuries.

Major comments:

As the authors pointed out, a major limitation of this study is uncertainty in the "population identity" for most sampled individuals (i.e., whether an individual belonged to the domesticated or wild herd when they were alive). Based on chronology, morphology and genetic data, it is clear the Mesolithic samples from the Artusia and Mendandia sites are bona fide aurochs, but the "population identities" of individuals from the other two sites are much less certain. Indeed, archeological and morphological evidence from El Portalon supports the presence of both domestic animals and wild aurochs, which is echoed by the inter-individual heterogeneity in genetic ancestry. Despite the strong evidence of hybridization, it is unclear whether these admixed individuals were raised in the domestic population or lived in the wild population and hunted, limiting the authors' ability to draw conclusions regarding the direction of gene flow.

In general, detecting sex-bias admixture is an inherently challenging problem, especially given limited data. The differential ancestry proportions (estimated by f4 ratios) on autosomes and X chromosome are indicative of sex-biased hybridization and consistent with previous mtDNA results and other non-genetic data. However, as shown in Fig 3, the confidence intervals of X and autosomal estimates overlap for all but a couple of individuals, despite the overall trend of the point estimates. Moreover, even if there is significant difference, it only suggests existence of sex-bias but does not speak to the extent (unless further quantitative argument is made). Statements such as "it was mostly aurochs males who contributed wild ancestry to domestic herds" is too strong and may be interpreted as extreme bias. The authors did a good job noting the caveats of this analysis and down-toned the statement in the main text, but claims regarding sex-bias hybridization that use the phrase "mostly" in the abstract and discussion need to be further weakened.

The stable isotope analysis is very under-powered, due to issues of categorization of wild vs domestic Bos, as discussed by the authors. Although the considerable overlap in stable isotope values between domestic and wild groups is consistent with shared ecological niche, but the absence of evidence (ie significant difference between groups) is not evidence of absence. Two alternative, non-mutually exclusive scenarios are (1) prevalent errors in classification of wild vs domestic individuals; (2) different ecological niches share similar isotope profiles. Thus, the claim "suggesting that wild and domesticated groups often did not occupy different niches in Iberia" is still too strong.