Reviewer #1 (Public review):

Koren et al. derive and analyse a spiking network model optimised to represent external signals using the minimum number of spikes. Unlike most prior work using a similar setup, the network includes separate populations of excitatory and inhibitory neurons. The authors show that the optimised connectivity has a like-to-like structure, which leads to the experimentally observed phenomenon of feature competition. The authors also examine how various (hyper)parameters-such as adaptation timescale, the excitatory-to-inhibitory cell ratio, regularization strength, and background current-affect the model. These findings add biological realism to a specific implementation of efficient coding. They show that efficient coding explains, or at least is consistent with, multiple experimentally observed properties of excitatory and inhibitory neurons.

As discussed in the first round of reviews, the model's ability to replicate biological observations such as the 4:1 ratio of excitatory vs. inhibitory neurons hinges on somewhat arbitrary hyperparameter choices. Although this may limit the model's explanatory power, the authors have made significant efforts to explore how these parameters influence their model. It is an empirical question whether the uncovered relationships between, e.g., metabolic cost and the fraction of excitatory neurons are biologically relevant.

The revised manuscript is also more transparent about the model's limitations, such as the lack of excitatory-excitatory connectivity.

Reviewer #2 (Public review):

Summary:

In this work, the authors present a biologically plausible, efficient E-I spiking network model and study various aspects of the model and its relation to experimental observations. This includes a derivation of the network into two (E-I) populations, the study of single-neuron perturbations and lateral-inhibition, the study of the effects of adaptation and metabolic cost, and considerations of optimal parameters. From this, they conclude that their work puts forth a plausible implementation of efficient coding that matches several experimental findings, including feature-specific inhibition, tight instantaneous balance, a 4 to 1 ratio of excitatory to inhibitory neurons, and a 3 to 1 ratio of I-I to E-I connectivity strength.

Strengths:

While many network implementations of efficient coding have been developed, such normative models are often abstract and lacking sufficient detail to compare directly to experiments. The intention of this work to produce a more plausible and efficient spiking model and compare it with experimental data is important and necessary in order to test these models. In rigorously deriving the model with real physical units, this work maps efficient spiking networks onto other more classical biophysical spiking neuron models. It also attempts to compare the model to recent single-neuron perturbation experiments, as well as some long-standing puzzles about neural circuits, such as the presence of separate excitatory and inhibitory neurons, the ratio of excitatory to inhibitory neurons, and E/I balance. One of the primary goals of this paper, to determine if these are merely biological constraints or come from some normative efficient coding objective, is also important. Lastly, though several of the observations have been reported and studied before, this work arguably studies them in more depth, which could be useful for comparing more directly to experiments.

Weaknesses:

This work is the latest among a line of research papers studying the properties of efficient spiking networks. Many of the characteristics and findings here have been discussed before, thereby limiting the new insights that this work can provide. Thus, the conclusions of this work should be considered and understood in the context of those previous works, as the authors state. Furthermore, the number of assumptions and free parameters in the model, though necessary to bring the model closer to biophysical reality, make it more difficult to understand and to draw clear conclusions from. As the authors state, many of the optimality claims depend on these free parameters, such as the dimensionality of the input signal (M=3), the relative weighting of encoding error and metabolic cost, and several others. This raises the possibility that it is not the case that the set of biophysical properties measured in the brain are accounted for by efficient coding, but rather that theories of efficient coding are flexible enough to be consistent with this regime. With this in mind, some of the conclusions made in the text may be overstated and should be considered in this light.

Conclusions, Impact, and additional context:

Notions of optimality are important for normative theories, but they are often studied in simple models with as few free parameters as possible. Biophysically detailed and mechanistic models, on the other hand, will often have many free parameters by their very nature, thereby muddying the connection to optimality. This tradeoff is an important concern in neuroscientific models. Previous efficient spiking models have often been criticized for their lack of biophysically-plausible characteristics, such as large synaptic weights, dense connectivity, and instantaneous communication. This work is an important contribution in showing that such networks can be modified to be much closer to biophysical reality without losing their essential properties. Though the model presented does suffer from complexity issues which raise questions about its connections to "optimal" efficient coding, the extensive study of various parameter dependencies offers a good characterization of the model and puts its conclusions in context.

Reviewer #3 (Public review):

Summary:

In their paper the authors tackle three things at once in a theoretical model: how can spiking neural networks perform efficient coding, how can such networks limit the energy use at the same time, and how can this be done in a more biologically realistic way than previous work.

They start by working from a long-running theory on how networks operating in a precisely balanced state can perform efficient coding. First, they assume split networks of excitatory (E) and inhibitory (I) neurons. The E neurons have the task to represent some lower dimensional input signal, and the I neurons have the task to represent the signal represented by the E neurons. Additionally, the E and I populations should minimize an energy cost represented by the sum of all spikes. All this results in two loss functions for the E and I populations, and the networks are then derived by assuming E and I neurons should only spike if this improves their respective loss. This results in networks of spiking neurons that live in a balanced state, and can accurately represent the network inputs.

They then investigate in depth different aspects of the resulting networks, such as responses to perturbations, the effect of following Dale's law, spiking statistics, the excitation (E)/inhibition (I) balance, optimal E/I cell ratios, and others. Overall, they expand on previous work by taking a more biological angle on the theory and show the networks can operate in a biologically realistic regime.

Strengths:

* The authors take a much more biological angle on the efficient spiking networks theory than previous work, which is an essential contribution to the field<br /> * They make a very extensive investigation of many aspects of the network in this context, and do so thoroughly<br /> * They put sensible constraints on their networks, while still maintaining the good properties these networks should have

Weaknesses:

* One of the core goals of the paper is to make a more biophysically realistic network than previous work using similar optimization principles. One of the important things they consider is a split into E and I neurons. While this works fine, and they consider the coding consequences of this, it is not clear from an optimization perspective why the split into E and I neurons and following Dale's law would be beneficial. This would be out of scope for the current paper however.<br /> * The theoretical advances in the paper are not all novel by themselves, as most of them (in particular the split into E and I neurons and the use of biophysical constants) had been achieved in previous models. However, the authors discuss these links thoroughly and do more in-depth follow-up experiments with the resulting model.

Assessment and context:

Overall, although much of the underlying theory is not necessarily new, the work provides an important addition to the field. The authors succeeded well in their goal of making the networks more biologically realistic, and incorporate aspects of energy efficiency. For computational neuroscientists this paper is a good example of how to build models that link well to experimental knowledge and constraints, while still being computationally and mathematically tractable. For experimental readers the model provides a clearer link of efficient coding spiking networks to known experimental constraints and provides a few predictions.

Reviewer #1 (Public review):

Summary:

This very short paper shows a greater likelihood of C->U substitutions at sites predicted to be unpaired in the SARS-CoV-2 RNA genome, using previously published observational data on mutation frequencies in SARS-CoV-2 (Bloom and Neher, 2023).

General comments:

A preference for unpaired bases as target for APOBEC-induced mutations has been demonstrated previously in functional studies so the finding is not entirely surprising. This of course assumes that A3A or other APOBEC is actually the cause of the majority of C->U changes observed in SARS-CoV-2 sequences.

I'm not sure why the authors did not use the published mutation frequency data to investigate other potential influences on editing frequencies, such as 5' and 3' base contexts. The analysis did not contribute any insights into the potential mechanisms underlying the greater frequency of C->U (or G->U) substitutions in the SARS-CoV-2 genome.

Comments on revisions:

The revisions have addressed my main comments in my review.

Reviewer #2 (Public review):

Hensel investigated the implications of SARS-CoV-2 RNA secondary structure in synonymous and nonsynonymous mutation frequency. The analysis integrated estimates of mutational fitness generated by Bloom and Neher (from publicly available patient sequences) and a population-averaged model of RNA base-pairing from Lan et al (from DMS mutational profiling with sequencing, DMS-MaPseq)

The results show that base-pairing limits the frequency of some synonymous substitutions (including the most common C→T), but not all: G→A and A→G substitutions seem unaffected by base-pairing.

The author then addressed nonsynonymous C→T substitutions at basepaired positions. While there is still a generally higher estimated mutational fitness at unpaired positions, they propose a coarse adjustment to disentangle base-pairing from inherent mutational fitness at a given position. This adjustment reveals that nonsynonymous substitutions at base-paired positions, which define major variants, have higher mutational fitness.

Overall, this manuscript highlights the importance of considering RNA secondary structure in viral evolution studies.

The conclusions of this work are generally well supported by the data presented. Particularly, the author acknowledges most limitations of the analyses and addresses them. Even though no new sequencing results were generated, the author used available data generated from the analysis of roughly seven million sequenced patient samples. Finally, the author discusses ways to improve the current available models.

There are a number of limitations of this work that should be highlighted, specifically in regard to the secondary structure data used in this paper. The Lan et al. dataset was generated using a multiplicity of infection (MOI) of 0.05, 24 hours post-infection (h.p.i.). At such a low MOI and late timepoint, viral replication is not synchronous and sequencing artifacts might be generated by cell debris and viral RNA degradation, therefore impacting the population-averaged results. In addition, the nonsynonymous base-paired positions in Figure 2 have relatively high population-averaged DMS reactivity, which suggests those positions are dynamic. Therefore, the proposed adjustment could result in an incorrect estimation of their inherent mutational fitness.

Additionally, like all such RNA probing experiments within cells, it remains difficult to deconvolve DMS/SHAPE low reactivity with RNA accessibility (e.g. from protein binding).

This work presents clear methods and an easy-to-access bioinformatic pipeline, which can be applied to other RNA viruses. Of note, it can be readily implemented in existing datasets. Finally, this study raises novel mechanistic questions on how mutational fitness is not correlated to secondary structure in the same way for every substitution.

Overall, this work highlights the importance of studying mutational fitness beyond an immune evasion perspective. On the other hand, it also adds to the viral intrinsic constraints to immune evasion.

Comments on revisions:

Following revision by the author, our concerns have been addressed. The additional analysis strengthens the conclusions & the revisions to the text have improved the manuscript for a general audience.

Reviewer #1 (Public review):

Summary:

This study focuses on metabolic changes in the paraventricular hypothalamic (PVH) region of the brain during acute periods of cold exposure. The authors point out that in comparison to the extensive literature on the effects of cold exposure in peripheral tissues, we know relatively little about its effects on the brain. They specifically focus on the hypothalamus, and identify the PVH as having changes in Atgl and Hsl gene expression changes during cold exposure. They then go on to show accumulation of lipid droplets, increased Fos expression, and increased lipid peroxidation during cold exposure. Further, they show that neuronal activation is required for the formation of lipid droplets and lipid peroxidation.

Strengths:

A strength of the study is trying to better understand how metabolism in the brain is a dynamic process, much like how it has been viewed in other organs. The authors also use a creative approach to measuring in vivo lipid peroxidation via delivery of BD-C11 sensor through a cannula to the region in conjunction with fiber photometry to measure fluorescence changes deep in the brain.

Comments on revised version:

The authors have attempted to address concerns brought to their attention in the initial review. They have performed one or two additional experiments to address concerns (e.g. adding fiber photometry of PVH neurons and trying to manipulate lipid peroxidation) though many of the concerns from the original review stand. The authors have also revised the text to limit the extent of their claims and to improve clarity, which is appreciated.

Reviewer #1 (Public review):

Summary:

IPF is a disease lacking regressive therapies which has a poor prognosis, and so new therapies are needed. This ambitious phase 1 study builds on the authors 2024 experience in Sci Tran Med with positive results with autologous transplantation of P63 progenitor cells in patients with COPD. The current study suggests P63+ progenitor cell therapy is safe in patients with ILD. The authors attribute this to acquisition of cells from a healthy upper lobe site, removed from the lung fibrosis. There are currently no cell based therapies for ILD and in this regard the study is novel with important potential for clinical impact if validated in Phase 2 and 3 clinical trials.

Strengths:

This study addresses the need for an effective therapy for interstitial lung disease. It offers good evidence the cell used for therapy are safe. In so doing it addresses a concern that some P63+ progenitor cells may be proinflammatory and harmful, as has been raised in the literature (articles which suggested some P63+ cells can promote honeycombing fibrosis; ref 26 &35). The authors attribute the safety they observed (without proof) to the high HOPX expression of administered cells (a marker found in normal Type 1 AECs. The totality of the RNASeq suggests the cloned cells are not fibrogenic. They also offer exploratory data suggesting a relationship between clone roundness and PFT parameters (and a negative association of patient age and clone roundness).

Weaknesses:

The authors can conclude they can isolate, clone, expand and administer P63+ progenitor cells safely; but with the small sample size and lack of placebo group no efficacy should be implied.

Comments on revisions:

The paper is meritorious as I noted initially

However, the authors did not directly address several of my concerns-i.e. their responses to the initial review were polite but did not translate into much change in the manuscript.

(1) Do these progenitor cells exert their beneficial effects by a paracrine mechanism vs transforming into lung AECs? Based on work in the field of bronchopulmonary dysplasia I suspect the benefits are mediated by a paracrine mecahnism and arguably media from these cells should be tested as an alternative to administering the cells themselves. In any case, for the revision a Discussion of the possibility of differentiation vs paracrine mechanisms, citing relevant literature, would be expected. I suggest that you add such a paragraph to a limitation section.

(2) Please address that potential implications of the fact that 5 patients had essentially normal DLCO/VA values. Saying that the "criterion for entry was DLCO" does not take away from the fact that DLCO/VA is a valid measure of lung diffusion capacity. In the absence of placebo an enrollment of mildly diseased patients would favor positive results (including stability in study endpoint parameters even without treatment). Thus, I suggest again that the limitations section should be more forthright in this regard.

(3) The authors acknowledge the lack of a placebo group but in a study of mild IPF, I worry that without a placebo group the only robust findings are those related to technique of transplantation and the safety of cell therapy. The paper still reads as if there is a clinical benefit...I would advise you further soften this (while understanding the desire to emphasize a hopeful observation). The price for not having a placebo group must be avoidance of claims of efficacy. The improvements in DLCO and CT in several cases speaks for the need for the planned phase 2 trial, which if positive will be the time to claim efficacy signals.

Reviewer #1 (Public review):

Summary:

In this manuscript, authors have investigated the effects of JNK inhibition on sucrose-induced metabolic dysfunction in rats. They used multi-tissue network analysis to study the effects of the JNK inhibitor JNK-IN-5A on metabolic dysfunction associated with excessive sucrose consumption. Their results show that JNK inhibition reduces triglyceride accumulation and inflammation in the liver and adipose tissues while promoting metabolic adaptations in skeletal muscle. The study provides new insights into how JNK inhibition can potentially treat metabolic dysfunction-associated fatty liver disease (MAFLD) by modulating inter-tissue communication and metabolic processes.

Strengths:

The study has several notable strengths:

Comprehensive Multi-Tissue Analysis: The research provides a thorough multi-tissue evaluation, examining the effects of JNK inhibition across key metabolically active tissues, including the liver, visceral white adipose tissue, skeletal muscle, and brain. This comprehensive approach offers valuable insights into the systemic effects of JNK inhibition and its potential in treating MAFLD.

Robust Use of Systems Biology: The study employs advanced systems biology techniques, including transcriptomic analysis and genome-scale metabolic modeling, to uncover the molecular mechanisms underlying JNK inhibition. This integrative approach strengthens the evidence supporting the role of JNK inhibitors in modulating metabolic pathways linked to MAFLD.

Potential Therapeutic Insights: By demonstrating the effects of JNK inhibition on both hepatic and extrahepatic tissues, the study offers promising therapeutic insights into how JNK inhibitors could be used to mitigate metabolic dysfunction associated with excessive sucrose consumption, a key contributor to MAFLD.

Behavioral and Metabolic Correlation: The inclusion of behavioral tests alongside metabolic assessments provides a more holistic view of the treatment's effects, allowing for a better understanding of the broader physiological implications of JNK inhibition.

Weaknesses:

The authors have adequately addressed all my concerns, and the revisions have significantly improved the manuscript's clarity and impact.

Reviewer #2 (Public review):

Excessive sucrose is a possible initial factor for the development of metabolic dysfunction-associated fatty liver disease (MAFLD). To investigate the possibility that intervention with JNK inhibitor could lead to the treatment of metabolic dysfunction caused by excessive sucrose intake, the authors performed multi-organ transcriptomics analysis (liver, visceral fat (vWAT), skeletal muscle, and brain) in a rat model of MAFLD induced by sucrose overtake (+ JNK inhibitor treatment).

The major strengths and weakness of this study are as follows.

Strengths:

・It has been previously reported that inhibition of JNK signalling can contribute to the prevention of hepatic steatosis (HS) and related metabolic syndrome in other models, but the role of JNK signalling in the metabolic disruption caused by excessive intake of sucrose, a possible initial factor for the development of MAFLD, has not been well understood, and the authors have addressed this point.<br /> ・This study is also important because pharmacological therapy for MAFLD has not yet been established.<br /> ・By obtaining transcriptomic data in multiple organs and comprehensively analyzing the data using gene co-expression network (GCN) analysis and genome-scale metabolic models (GEM), the authors showed the multi-organ interaction in not only in the pathology of MAFLD caused by excessive sucrose intake but also in the treatment effects by JNK-IN-5A.<br /> ・Since JNK signalling has diverse physiological functions in many organs, the authors effectively assessed possible side effects with a view to the clinical application of JNK-IN-5A.

Weaknesses:

・The metabolic process activities were evaluated using RNA-seq results in Figure 7, but direct data such as metabolite measurements are lacking.<br /> ・There is a lack of consistency in the data between JNK-IN-5A_D1 and _D2, and there is no sufficient data-based explanation for why the effects observed in D1 were inconsistent in the D2 samples.<br /> ・Although it is valuable that the authors were able to suggest the possibility of JNK inhibitor as a therapeutic strategy for MAFLD, the evaluation of the therapeutic effect was limited to evaluation of plasma TG, LDH, and gene expression changes. As there was no evaluation of liver tissue images, it is unclear what changes were brought about in the liver by the excessive sucrose intake and the treatment with JNK-IN-5A.

As mentioned in the Weakness section, biological data is insufficient, such as the lack of metabolite measurements and a histological evaluation of the liver. However, overall, the authors successfully provided the valuable insights that the JNK inhibitor has a cross-organ therapeutic effect on their MAFLD model induced by sucrose overtake. Their insist is supported by convincing data, comprehensively analysing the transcriptomic data obtained from multiple organs using GCN (gene co-expression network) analysis and GEM (genome-scale metabolic modelling).

Their comprehensive transcriptomic analysis in multiple organs, including the brain, has demonstrated that the effects of drugs are more widespread than just on specific tissues thought to be the main target, indicating the importance of focusing on tissue interactions when we assess the effects of drugs. Also, the data set in this study will be useful for comparative evaluation with transcriptomics data for other MALFD models.

Reviewer #1 (Public review):

Summary:

This paper describes a new in vitro model for DRG neurons that recapitulates several key differences between the peripheral and central branches of DRG axons in vivo. These differences include morphology (with one branch being thinner than the other), and regenerative capacity (with the peripheral branch displaying higher regenerative capacity). The authors analyze the abundance of various microtubule associated protein (MAPs) in each branch, as well as the microtubule dynamics in each branch and find significant differences between branches. Importantly, they found that a well-known conditioning paradigm (prior lesion of the peripheral branch improves the regenerative capacity of the central branch) is not only reproduced in this system, but also leads to loss of the asymmetry of MAPs between branches. Zooming in on one MAP that shows differential abundance between the axons, they find that the severing enzyme Spastin is required for the asymmetry in microtubule dynamics and in regenerative capacity following a conditioning lesion

Strengths:

The establishment of an experimental system that recapitulates DRG axon asymmetry in vitro is an important step that is likely to be useful for other studies. In addition, identifying key molecular signatures that differ between central and peripheral branches, and determining how they are lost following a conditioning lesion adds to our understanding of why peripheral axons have a better regenerative capacity. Last, the authors use of an in vivo model system to support some of their in vitro findings is a strength of this work.

Weaknesses:

One weakness of the manuscript is that to a large degree, one of its main conclusions (MAP symmetry underlies differences in regenerative capacity) relies mainly on a correlation, without firmly establishing a causal link. However, this is weakness is relatively minor because (1) it is partially addressed with the Spastin KO and (2) there isn't a trivial way to show a causal relationship in this case. (3) It is addressed in the Discussion section.

Reviewer #2 (Public review):

Summary:

The authors set out to develop a tissue culture method in which to study the different regenerative abilities of the central and peripheral branch of sensory axons. Neurons developed a small and large branch, which have different regenerative abilities, different transport rates and different microtubule properties. The study provides convincing evidence that the two axonal branches differ in a way to corresponds to in vivo. The different regenerative abilities of the two branches are an important observation, because until now it has not been clear whether this difference is intrinsic to the neuron and axons or due to differences in the environment surrounding the axons. The authors have then looked for molecular explanations of the differences between the branches. They find different transport rates and different microtubule dynamics. The different microtubule dynamics are explained by differing levels of spastin, an enzyme that severs microtubules encouraging dynamics.

Strengths:

The differences between the two branches are clearly shown, together with differences in transport, microtubule dynamics and regeneration. The in vitro model is novel and could be widely used. The methods used are robust and generally accepted.

Weaknesses:

The revised version of the paper has addressed the weaknesses that were identified.

Reviewer #3 (Public review):

Summary:

In this manuscript, Costa and colleagues investigate how asymmetry in dorsal root ganglion (DRG) neurons is established. The authors developed an in vitro system that mimics the pseudo-unipolar morphology and asymmetry of DRG neurons during the regeneration of the peripheral and central branch axons. They suggest that central-like DRG axons exhibit a higher density of growing microtubules. By reducing the polymerization of microtubules in these central-like axons, they were able to eliminate the asymmetry in DRG neurons.

Strengths:

The authors point out a distinct microtubule-associated protein signature that differentiates between DRG neurons' central and peripheral axonal branches. Experimental results demonstrate that genetic deletion of spastin eliminated the differences in microtubule dynamics and axon regeneration between the central and peripheral branches.

Weaknesses:

While some of the data are compelling, experimental evidence does not fully support the main claims.

In its current form, the study is primarily descriptive and lacks convincing mechanistic insights. It misses important controls and further validation using 3D in vitro models.

The significance of studying microtubule polymerization to DRG asymmetry in vitro is questionable, especially considering the model's validity. Classifying the central and peripheral-like branches in cultured DRG neurons will require further in-depth characterization. Additional validation using adult DRG neuron cultures not aged in vitro will be required in future studies.

The comparison of asymmetry associated with a regenerative response between in vitro and in vivo paradigms has significant limitations due to the nature of the in vitro culture system. When cultured in isolation, DRG neurons fail to form functional connections with appropriate postsynaptic target neurons (the central branch) or to differentiate the peripheral domains associated with the innervation of target organs. Rather than growing neurons on a flat, hard surface like glass, more physiologically relevant substrates and/or culturing conditions should be considered. This approach could help eliminate potential artifacts caused by plating adult DRG neurons on a flat surface. Additionally, the authors should consider replicating their findings in a 3D culture model or using dorsal root ganglia explants, where both centrally and peripherally projecting axons are present.

Panels 5H-J require additional processing with astrocyte markers to accurately define the lesion borders. Furthermore, including a lower magnification would facilitate a direct comparison of the lesion site. The use of cholera toxin subunit B (CTB) to trace dorsal column sensory axons is prone to misinterpretation, as the tracer accumulates at the axon's tip. This limitation makes it extremely challenging to distinguish between regenerating and degenerating axons.

Reviewer #1 (Public Review):

The authors showed that autophagy-related genes are involved in plant immunity by regulating the protein level of the salicylic acid receptor, NPR1.

The experiments are carefully designed and the data is convincing. The authors did a good job of understanding the relationship between ATG6 and NRP1.

Comments on latest version:

The authors have sufficiently addressed all concerns raised, which further enhanced data presentation. No additional concerns were raised.

Reviewer #2 (Public Review):

The manuscript by Zhang et al. explores the effect of autophagy regulator ATG6 on NPR1-mediated immunity. The authors propose that ATG6 directly interacts with NPR1 in the nucleus to increase its stability and promote NPR1-dependent immune gene expression and pathogen resistance. This novel role of ATG6 is proposed to be independent of its role in autophagy in the cytoplasm. The authors demonstrate through biochemical analysis that ATG6 interacts with NPR1 in yeast and very weakly in vitro. They further demonstrate using overexpression transgenic plants that in the presence of ATG6-mcherry the stability of NPR1-GFP and its nuclear pool is increased.

Comments on latest version:

The initial apprehensions about statistical oversights and the use of an unclear nuclear marker were fixed. The implementation of the nls-mCherry for nuclear co-localization and additional statistical analyses was done well. However, the functional importance pertaining to cytoplasmic accumulation of the ARG6 protein should ideally be explored in more detail in future studies.

Updated sections:<br /> • Figure 1e: Added statistical analysis and updated with a nuclear marker.<br /> • Line Revisions: Terminology corrections for "infection" instead of "invasion".<br /> • NLS Analysis: Extended alignment and inclusion of conserved domains with predicted NLS (cut-off score: 2.6).

Reviewer #1 (Public review):

Summary:

This study shows that the pro-inflammatory S1P signaling regulates the responses of muller glial cells to damage. The authors describe the expression of S1P signaling components. Using agonist and antagonist of the pathways they also investigate their effect on the de-differentiation and proliferation of Muller glial cells in damaged retina of postnatal chicks. They show that S1PR1 is highly expressed in resting MG and non-neurogenic MGPCs. This receptor suppresses the proliferation and neuronal activity promotes MGPC cell cycle re-entry and enhanced the number of regenerated amacrine-like cells after retinal damage. The formation of MGPCs in damaged retinas is impaired in the absence of microglial cells. This study further shows that ablation of microglial cells from the retina increases the expression of S1P-related genes in MG, whereas inhibition of S1PR1 and SPHK1 partially rescues the formation of MGPCs in damaged retinas depleted of microglia. The studies also show that expression of S1P-related genes is conserved in fish and human retinas.

Strengths:

This is well-conducted study, with convincing images and statistically relevant data

Weaknesses:

In a previous study, the authors have shown that S1P is upstream of NF-κB signaling (Palazzo et al. 2020; 2022, 2023). Although S1P and NF-κB signaling have overlapping effects, the authors here provide evidence for S1P specific effects, adding some new information to the field.

Reviewer #2 (Public review):

Summary:

Sphingosine-1-phosphate (S1P) metabolic and signaling genes are expressed highly in retinal Müller glia (MG) cells. This study tested how S1P signaling regulates glial phenotype, dedifferentiation of, reprogramming into proliferating MG-derived progenitor cells (MGPCs), and neuronal differentiation of the progeny of MGPCs using in vivo chick retina. Major techniques used are Sc-RNASeq and immunohistochemistry to determine the gene expression and proliferation of MG cells that co-label with signaling antibodies or mRNA FISH following treating the in vivo eyes with various S1P signaling antagonists, agonists, and signal modulators. The major conclusions drawn are supported by the results presented. However, the methodology they have used to modulate the S1P pathway using various chemical drugs raises questions about the outcomes and whether those are the real effects of S1P receptor modulation or S1P synthesis inhibition.

Strengths:

- Use of elaborated single-cell RNAseq expression data.<br /> - Use of FISH for S1P receptors and kinase as a good quality antibody is not available.<br /> - Use of EdU assay in combination with IHC<br /> - Comparison with human and Zebrafish Sc-RNA data

Weaknesses:

The methodology is not very clean. A number of drugs (inhibitors/ antagonists/agonists signal modulators) are used to modulate S1P expression or signaling in the retina without evidence that these drugs are reaching the target cells. No alternative evaluation if the drugs, in fact, are effective. The drug solubility in the vehicle and in the vitreous is not provided, and how did they decide on using a single dose of each drug to have the optimal expected effect on the S1P pathway?

In the revision, the authors provided justification for the use of single doses of the modulators and how they could pass the retinal barrier and affect the MG gene expression and receptor functioning.

Reviewer #1 (Public review):

Summary:

The authors employed a combinatorial CRISPR-Cas9 knockout screen to uncover synthetically lethal kinase genes that could play a role in drug resistance to kinase inhibitors in triple-negative breast cancer. The study successfully reveals FYN as a mediator of resistance to depletion and inhibition of various tyrosine kinases, notably EGFR, IGF-1R, and ABL, in triple-negative breast cancer cells and xenografts. Mechanistically, they demonstrate that KDM4 contributes to the upregulation of FYN and thereby is an important mediator of the drug resistance. All together, these findings suggest FYN and KDM4A as potential targets for combination therapy with kinase inhibitors in triple-negative breast cancer. Moreover, the study may also have important implications for other cancer types and other inhibitors, as the authors suggest that FYN could be a general feature of drug-tolerant persister cells.

Strengths:

(1) The authors used a large combination matrix of druggable tyrosine kinase gene knockouts, enabling studying of co-dependence of kinase genes. This approach mitigates off-target effects typically associated with kinase inhibitors, enhancing the precision of the findings.

(2) The authors demonstrate the importance of FYN in drug resistance in multiple ways. They demonstrate synergistic interactions using both knockouts and inhibitors, while also revealing its transcriptional upregulation upon treatment, strengthening the conclusion that FYN plays a role in the resistance.

(3) The study extends its impact by demonstrating the potent in vivo efficacy of certain combination treatments, underscoring the clinical relevance of the identified strategies.

Weaknesses:

(1) The combination of FYN knockout with other gene knockouts exhibits only very modest synergy. The high standard deviation observed for FYN knockout in Figure S2A weakens the robustness of these findings. As combination treatments involving inhibitors did demonstrate stronger synergistic effects, the data still support the role of FYN in regulating sensitivity to the described drugs.

(2) While the study identifies KDM4A as a key contributor to FYN upregulation, it does not fully explore the upstream mechanisms regulating KDM4A or the downstream pathways through which FYN upregulation confers drug resistance. These unaddressed questions limit the mechanistic understanding that can be obtained from this study.

(3) FYN has been implicated in drug resistance in previous studies, and other mechanisms for its upregulation and downstream effects have already been described. While this study adds value to the existing literature in the context of breast cancer, it does not present entirely novel findings regarding FYN's role in drug resistance.

Reviewer #1 (Public review):

Summary:

The authors constructed a novel HSV-based therapeutic vaccine to cure SIV in a primate model. The novel HSV vector is deleted for ICP34.5. Evidence is given that this protein blocks HIV reactivation by interference with the NFkappaB pathway. The deleted construct supposedly would reactivate SIV from latency. The SIV genes carried by the vector ought to elicit a strong immune response. Together the HSV vector would elicit a shock and kill effect. This is tested in a primate model.

Strengths and weaknesses:

(1) Deleting ICP34.5 from the HSV construct has a very strong effect on HIV reactivation. The mechanism underlying increased activation by deleting ICP34.5 is only partially explored. Overexpression of ICP34.5 has a much smaller effect (reduction in reactivation) than deletion of ICP34.5 (strong activation); this is acknowledged by the authors that no full mechanistic explanation can be given at this moment.

(2) No toxicity data are given for deleting ICP34.5. How specific is the effect for HIV reactivation? A RNA seq analysis is required to show the effect on cellular genes.

A RNA seq analysis was done in the revised manuscript comparing the effect of HSV-1 and deleted vector in J-LAT cells (Fig S5). More than 2000 genes are upregulated after transduction with the modified vector in comparison with the WT vector. Hence, the specificity of upregulation of SIV genes is questioned. Authors do NOT comment on these findings. In my view it questions the utility of this approach.

(3) The primate groups are too small and the results to variable to make averages. In Fig 5, the group with ART and saline has two slow rebounders. It is not correct to average those with the single quick rebounder. Here the interpretation is NOT supported by the data.

Although authors provided some promising SIV DNA data, no additional animals were added. Groups of 3 animals are too small to make any conclusion, especially since the huge variability in response. The average numbers out of 3 are still presented in the paper, which is not proper science.

No data are given of the effect of the deletion in primates. Now the deleted construct is compared with an empty vector containing no SIV genes. Authors provide new data in Fig S2 on the comparison of WT and modified vector in cells from PLWH, but data are not that convincing. A significant difference in reactivation is seen for LTR in only 2/4 donors and in Gag in 3/4 donors. (Additional question what is meaning of LTR mRNA, do authors relate to genomic RNA??)

Discussion

HSV vectors are mainly used in cancer treatment partially due to induced inflammation. Whether these are suitable to cure PLWH without major symptoms is a bit questionable to me and should at least be argued for.

The RNA seq data add on to this worry and should at least be discussed.

Reviewer #2 (Public review):

Summary:

In this article Wen et. al., describe the development of a 'proof-of-concept' bi-functional vector based out of HSV-deltaICP-34.5's ability to purge latent HIV-1 and SIV genomes from cells. They show that co-infection of latent J-lat T-cell lines with a HSV-deltaICP-34.5 vector can reactivate HIV-1 from a latent state. Over- or stable expression of ICP 34.5 ORF in these cells can arrest latent HIV-1 genomes from transcription, even in the presence of latency reversal agents. ICP34.5 can co-IP with- and de-phosphorylate IKKa/b to block its interaction with NF-k/B transcription factor. Additionally, ICP34.5 can interact with HSF1 which was identified by mass-spec. Thus, the authors propose that the latency reversal effect of HSV-deltaICP-34.5 in co-infected JLat cells is due to modulatory effects on the IKKa/b-NF-kB and PP1-HSF-1 pathway.

Next the authors cleverly construct a bifunctional HSV based vector with deleted ICP34.5 and 47 ORFs to purge latency and avoid immunological refluxes, and additionally expand the application of this construct as a vaccine by introducing SIV genes. They use this 'vaccine' in mouse models and show the expected SIV-immune responses. Experiments in rhesus macaques (RM), further elicit potential for their approach to reactivate SIV genomes and at the same time block their replication by antibodies. What was interesting in the SIV experiments is that the dual-functional vector vaccine containing sPD1- and SIV Gag/Env ORFs effectively delayed SIV rebound in RMs and in some cases almost neutralized viral DNA copy detection in serum. Very promising indeed, however there are some questions I wish the authors explored to answer, detailed below.

Overall, this is an elegant and timely work demonstrating the feasibility of reducing virus rebound in animals, and potentially expand to clinical studies. The work was well written, and sections were clearly discussed.

Strengths:

The work is well designed, rationale explained and written very clearly for lay readers.<br /> Claims are adequately supported by evidence and well designed experiments including controls.

Weaknesses:

(1) It looks like ICP0 is also involved in latency reversal effects. More follow-up work will be required to test if this is in fact true.

(2) It is difficult to estimate the depletion of the latent viral reservoir. The authors have tried to address this issue. A more convincing argument to this reviewer will be data to demonstrate that after the bi-functional vaccine, the animals show overall reduction in the number of circulating latent cells. The feasibility to obtain such a result is not clearly demonstrated.

(3) The authors state that the reduced virus rebound detected following bi-functional vaccine delivery is due to latent genomes becoming activated and steady-state neutralization of these viruses by antibody response. This needs to be demonstrated. Perhaps cell-culture experiments from specimen taken from animals might help address this issue. In lab cultures one could create environments without antibody responses, under these conditions one would expect higher level of viral loads being released in response to the vaccine in question.

Reviewer #1 (Public review):

Summary:

This work provides a new potential tool to manipulate Tregs function for therapeutic use. It focuses on the role of PGAM in Tregs differentiation and function. The authors, interrogating publicly available transcriptomic and proteomic data of human regulatory T cells and CD4 T cells, state that Tregs express higher levels of PGAM (at both message and protein levels) compared to CD4 T cells. They then inhibit PGAM by using a known inhibitor ECGC and show that this inhibition affects Tregs differentiation. This result was also observed when they used antisense oligonucleotides (ASOs) to knockdown PGAM1.

PGAM1 catalyzes the conversion of 3PG to 2PG in the glycolysis cascade. However, the authors focused their attention on the additional role of 3PG: acting as starting material for the de novo synthesis of serine.

They hypothesized that PGAM1 regulates Tregs differentiation by regulating the levels of 3PG that are available for de novo synthesis of serine, which has a negative impact on Tregs differentiation. Indeed, they tested whether the effect on Tregs differentiation observed by reducing PGAM1 levels was reverted by inhibiting the enzyme that catalyzes the synthesis of serine from 3PG.

The authors continued by testing whether both synthesized and exogenous serine affect Tregs differentiation and continued with in vivo experiments to examine the effects of dietary serine restriction on Tregs function.

In order to understand the mechanism by which serine impacts Tregs function, the authors assessed whether this depends on the contribution of serine to one-carbon metabolism and to DNA methylation.

The authors therefore propose that extracellular serine and serine whose synthesis is regulated by PGAM1 induce methylation of genes Tregs associated, downregulating their expression and overall impacting Tregs differentiation and suppressive functions.

Strengths:

The strength of this paper is the number of approaches taken by the authors to verify their hypothesis. Indeed, by using both pharmacological and genetic tools in in vitro and in vivo systems they identified a potential new metabolic regulation of Tregs differentiation and function.

Weaknesses:

Using publicly available transcriptomic and proteomic data of human T cells, the authors claim that both ex vivo and in vitro polarized Tregs express higher levels of PGAM1 protein compared to CD4 T cells (naïve or cultured under Th0 polarizing conditions). The experiments shown in this paper have all been carried out in murine Tregs. Publicly available resources for murine data (ImmGen -RNAseq and ImmPRes - Proteomics) however show that Tregs do not express higher PGAM1 (mRNA and protein) compared to CD4 T cells. It would be good to verify this in the system/condition used in the paper.

It would also be good to assess the levels of both PGAM1 mRNA and protein in Tregs PGAM1 knockdown compared to scramble using different methods e.g. qPCR and western blot. However, due to the high levels of cell death and differentiation variability, that would require cells to be sorted.

It is not specified anywhere in the paper whether cells were sorted for bulk experiments. Based on the variability of cell differentiation, it would be good if this was mentioned in the paper as it could help to interpret the data with a different perspective.

Reviewer #2 (Public review):

Summary:

The authors have tried to determine the regulatory role of Phosphoglycerate mutate (PGAM), an enzyme involved in converting 3-phosphoglycerate to 2-phosphoglycerate in glycolysis, in differentiation and suppressive function of regulatory CD4 T cells through de novo serine synthesis. This is done by contributing one carbon metabolism and eventually epigenetic regulation of Treg differentiation.

Strengths:

The authors have rigorously used inhibitors and antisense RNA to verify the contribution of these pathways in Treg differentiation in-vitro. This has also been verified in an in-vivo murine model of autoimmune colitis. This has further clinical implications in autoimmune disorders and cancer.

Weaknesses:

The authors have used inhibitors to study pathways involved in Treg differentiation. However, they have not studied the context of overexpression of PGAM, which was the actual reason to pursue this study.

Reviewer #1 (Public review):

This paper measures the positioning and diffusivity of RNaseE-mEos3.2 proteins in E. coli as a function of rifampicin treatment, compares RNaseE to other E. coli proteins, and measures the effect of changes in domain composition on this localization and motion. The straightforward study is thoroughly presented, including very good descriptions of the imaging parameters and the image analysis/modeling involved, which is good because the key impact of the work lies in presenting this clear methodology for determining the position and mobility of a series of proteins in living bacteria cells.

My key notes and concerns are listed below; the most important concerns are indicated with asterisks.

(1) The very start of the abstract mentions that the domain composition of RNase E varies among species, which leads the reader to believe that the modifications made to E. coli RNase E would be to swap in the domains from other species, but the experiment is actually to swap in domains from other E. coli proteins. The impact of this work would be increased by examining, for instance, RNase E domains from B. subtilis and C. crescentus as mentioned in the introduction.

(2) Furthermore, the introduction ends by suggesting that this work will modulate the localization, diffusion, and activity of RNase E for "various applications", but no applications are discussed in the discussion or conclusion. The impact of this work would be increased by actually indicating potential reasons why one would want to modulate the activity of RNase E.

(3) Lines 114 - 115: "The xNorm histogram of RNase E shows two peaks corresponding to each side edge of the membrane": "side edge" is not a helpful term. I suggest instead: "...corresponding to the membrane at each side of the cell"

(4) ***A key concern of this reviewer is that, since membrane-bound proteins diffuse more slowly than cytoplasmic proteins, some significant undercounting of the % of cytoplasmic proteins is expected due to decreased detectability of the faster-moving proteins. This would not be a problem for the LacZ imaging where essentially all proteins are cytoplasmic, but would significantly affect the reported MB% for the intermediate protein constructs. How is this undercounting considered and taken into account? One could, for instance, compare LacZ vs. LacY (or RNase E) copy numbers detected in fixed cells to those detected in living cells to estimate it.

(5) ***The rifampicin treatment study is not presented well. Firstly, it is found that LacY diffuses more rapidly upon rifampicin treatment. This change is attributed to changes in crowding at the membrane due to mRNA. Several other things change in cells after adding rif, including ATP levels, and these factors should be considered. More importantly, since the change in the diffusivity of RNaseE is similar to the change in diffusivity of LacY, then it seems that most of the change in RNaseE diffusion is NOT due to RNaseE-mRNA-ribosome binding, but rather due to whatever crowding/viscosity effects are experienced by LacY (along these lines: the error reported for D is SEM, but really should be a confidence interval, as in Figure 1, to give the reader a better sense of how different (or similar) 1.47 and 1.25 are).

(6) Lines 185-189: it is surprising to me that the CTD mutants both have the same change in D (5.5x and 5.3x) relative to their full-length counterparts since D for the membrane-bound WT protein should be much less sensitive to protein size than D for the cytoplasmic MTS mutant. Can the authors comment?

(7) Lines 190-194. Again, the confidence intervals and experimental uncertainties should be considered before drawing biological conclusions. It would seem that there is "no significant change" in the rhlB and pnp mutants, and I would avoid saying "especially for ∆pnp" when the same conclusion is true for both (one shouldn't say 1.04 is "very minute" and 1.08 is just kind of small - they are pretty much the same within experiments like this).

(8) ***Lines 221-223 " This is remarkable because their molecular masses (and thus size) are expected to be larger than that of MTS" should be reconsidered: diffusion in a membrane does not follow the Einstein law (indeed lines 223-225 agree with me and disagree with lines 221-223). (Also the discussion paragraph starting at line 375). Rather, it is generally limited by the interactions with the transmembrane segments with the membrane. So Figure 3D does not contain the right data for a comparison, and what is surprising to me is that MTS doesn't diffuse considerably faster than LacY2.

(9) ***The logical connection between the membrane-association discussion (which seems to ignore associations with other proteins in the cell) and the preceding +/- rifampicin discussion (which seeks to attribute very small changes to mRNA association) is confusing.

(10) Separately, the manuscript should be read through again for grammar and usage. For instance, the title should be: "Single-molecule imaging reveals the *roles* of *the* membrane-binding motif and *the* C-terminal domain of RNase E in its localization and diffusion in Escherichia coli". Also, some writing is unwieldy, for instance, "RNase E's D" would be easier to read if written as D_{RNaseE}. (underscore = subscript), and there is a lot of repetition in the sentence structures.

Reviewer #2 (Public review):

Summary:

Troyer and colleagues have studied the in vivo localisation and mobility of the E.coli RNaseE (a protein key for mRNA degradation in all bacteria) as well as the impact of two key protein segments (MTS and CTD) on RNase E cellular localisation and mobility. Such sequences are important to study since there is significant sequence diversity within bacteria, as well as a lack of clarity about their functional effects. Using single-molecule tracking in living bacteria, the authors confirmed that >90% of RNaseE localised on the membrane, and measured its diffusion coefficient. Via a series of mutants, they also showed that MTS leads to stronger membrane association and slower diffusion compared to a transmembrane motif (despite the latter being more embedded in the membrane), and that the CTD weakens membrane binding. The study also rationalised how the interplay of MTS and CTD modulate mRNA metabolism (and hence gene expression) in different cellular contexts.

Strengths:

The study uses powerful single-molecule tracking in living cells along with solid quantitative analysis, and provides direct measurements for the mobility and localisation of E.coli RNaseE, adding to information from complementary studies and other bacteria. The exploration of different membrane-binding motifs (both MTS and CTD) has novelty and provides insight on how sequence and membrane interactions can control function of protein-associated membranes and complexes. The methods and membrane-protein standards used contribute to the toolbox for molecular analysis in live bacteria.

Weaknesses:

The Results sections can be structured better to present the main hypotheses to be tested. For example, since it is well known that RNase E is membrane-localised (via its MTS), one expects its mobility to be mainly controlled by the interaction with the membrane (rather than with other molecules, such as polysomes and the degradosome). The results indeed support this expectation - however, the manuscript in its current form does not lay down the dominant hypothesis early on (see second Results chapter), and instead considers the rifampicin-addition results as "surprising"; it will be best to outline the most likely hypotheses, and then discuss the results in that light.

Similarly, the authors should first discuss the different modes of interaction for a peripheral anchor vs a transmembrane anchor, outline the state of knowledge and possibilities, and then discuss their result; in its current version, the ms considers the LacY2 and LacY6 faster diffusion compared to MTS "remarkable", but considering the very different mode of interaction, there is no clear expectation prior to the experiment. In the same section, it would be good to see how the MD simulations capture the motion of LacY6 and LacY12, since this will provide a set of results consistent with the experimental set.

The work will benefit from further exploration of the membrane-RNase E interactions; e.g., the effect of membrane composition is explored by just using two different growth media (which on its own is not a well-controlled setting), and no attempts to change the MTS itself were made. The manuscript will benefit from considering experiments that explore the diversity of RNaseE interactions in different species; for example, the authors may want to consider the possibility of using the membrane-localisation signals of functional homologs of RNaseE in different bacteria (e.g., B. subtilis). It would be good to look at the effect of CTD deletions in a similar context (i.e., in addition to the MTS substitution by LacY2 and LacY6).

The manuscript will benefit from further discussion of the unstructured nature of the CTD, especially since the RNase CTD is well known to form condensates in Caulobacter crescentus; it is unclear how the authors excluded any roles for RNaseE phase separation in the mobility of RNaseE in E.coli cells.

Some statements in the Discussion require support with example calculations or toning down substantially. Specifically, it is not clear how the authors conclude that RNaseE interacts with its substrate for a short time (and what this time may actually be); further, the speculation about the MTS "not being an efficient membrane-binding motif for diffusion" lacks adequate support as it stands.

Reviewer #3 (Public review):

Summary:

The manuscript by Troyer et al quantitatively measured the membrane localization and diffusion of RNase E, an essential ribonuclease for mRNA turnover as well as tRNA and rRNA processing in bacteria cells. Using single-molecule tracking in live E. coli cells, the authors investigated the impact of membrane targeting sequence (MTS) and the C-terminal domain (CTD) on the membrane localization and diffusion of RNase E under various perturbations. Finally, the authors tried to correlate the membrane localization of RNase E to its function on co- and post-transcriptional mRNA decay using lacZ mRNA as a model.

The major findings of the manuscripts include:

(1) WT RNase E is mostly membrane localized via MTS, confirming previous results. The diffusion of RNase E is increased upon removal of MTS or CTD, and more significantly increased upon removal of both regions.

(2) By tagging RNase E MTS and different lengths of LacY transmembrane domain (LacY2, LacY6, or LacY12) to mEos3.2, the results demonstrate that short LacY transmembrane sequence (LacY2 and LacY6) can increase the diffusion of mEos3.2 on the membrane compared to MTS, further supported by the molecular dynamics simulation. A similar trend was roughly observed in RNase E mutants with MTS switched to LacY transmembrane domains.

(3) The removal of RNase E MTS significantly increases the co-transcriptional degradation of lacZ mRNA, but has minimal effect on the post-transcriptional degradation of lacZ mRNA. Removal of CTD of RNase E overall decreases the mRNA decay rates, suggesting the synergistic effect of CTD on RNase E activity.

Strengths:

(1) The manuscript is clearly written with very detailed method descriptions and analysis parameters.

(2) The conclusions are mostly supported by the data and analysis.

(3) Some of the main conclusions are interesting and important for understanding the cellular behavior and function of RNase E.

Weaknesses:

(1) Some of the observations show inconsistent or context-dependent trends that make it hard to generalize certain conclusions. Those points are worth discussion at least. Examples include:

(a) The authors conclude that MTS segment exhibits reduced MB% when succinate is used as a carbon source compared to glycerol, whereas LacY2 segment maintains 100% membrane localization, suggesting that MTS can lose membrane affinity in the former growth condition (Ln 341-342). However, the opposite case was observed for the WT RNase E and RNase E-LacY2-CTD, in which RNase E-LacY2-CTD showed reduced MB% in the succinate-containing M9 media compared to the WT RNase E (Ln 264-267). This opposite trend was not discussed. In the absence of CTD, would the media-dependent membrane localization be similar to the membrane localization sequence or to the full-length RNase E?

(b) When using mEos3.2 reporter only, LacY2 and LacY6 both increase the diffusion of mEos3.2 compared to MTS. However, when inserting the LacY transmembrane sequence into RNase E or RNase E without CTD, only the LacY2 increases the diffusion of RNase E. This should also be discussed.

(2) The authors interpret that in some cases the increase in the diffusion coefficient is related to the increase in the cytoplasm localization portion, such as for the LacY2 inserted RNase E with CTD, which is rational. However, the authors can directly measure the diffusion coefficient of the membrane and cytoplasm portion of RNase E by classifying the trajectories based on their localizations first, rather than just the ensemble calculation.

(3) The error bars of the diffusion coefficient and MB% are all SEM from bootstrapping, which are very small. I am wondering how much of the difference is simply due to a batch effect. Were the data mixed from multiple biological replicates? The number of biological replicates should also be reported.

(4) Some figures lack p-values, such as Figures 4 and 5C-D. Also, adding p-values directly to the bar graphs will make it easier to read.

Reviewer #1 (Public review):

Summary:

This study uses single nucleus multi-omics to profile the transcriptome and chromatin accessibility of mouse XX and XY primordial germ cells (PGCs) at three time points spanning PGC sexual differentiation and entry of XX PGCs into meiosis (embryonic days 11.5-13.5). They find that PGCs can be clustered into sub-populations at each time point, with higher heterogeneity among XX PGCs and more switch-like developmental transitions evident in XY PGCs. In addition, they identify several transcription factors that appear to regulate sex-specific pathways as well as cell-cell communication pathways that may be involved in regulating XX vs XY PGC fate transitions. The findings are important and overall rigorous. The study could be further improved by better connection to the biological system, including putting the transcriptional heterogeneity of XX PGCs in the context of findings that meiotic entry is spatially asynchronous in the fetal ovary and further addressing the role of retinoic acid signaling. Overall, this study represents and advance in germ cell regulatory biology and will be a highly used resource in the field of germ cell development.

Strengths:

(1) The multi-omics data is mostly rigorously collected and carefully interpreted.

(2) The dataset is extremely valuable and helps to answer many long-standing questions in the field.

(3) In general, the conclusions are well anchored in the biology of the germ line in mammals.

Comments on revised version:

Most of my concerns have been addressed in the revised manuscript. I have one remaining concern but I believe this is important in order for the paper to be fully appreciated:

In Figures 2a, 2e, 3a, and 3e, the visualization scheme is very difficult to follow, and has not been updated or improved in the revised manuscript. It's very hard to see the colors corresponding to average expression for many genes because the circles are so small. The yellow color is hard to see and makes it hard to estimate the size of the circle. This issue is particularly egregious in Figure 2a for the data relating to ZKSCAN5, which is specifically highlighted in the text in lines 421-426. This data must be shown in a more convincing way in order to make the claims. An update to the visualization, including color scheme, is very strongly recommended; it is not difficult and would substantially improve the ability of these panels to communicate their message.

Reviewer #2 (Public review):

Summary:

This manuscript by Alexander et al describes a careful and rigorous application of multiomics to mouse primordial germ cells (PGCs) and their surrounding gonadal cells during the period of sex differentiation.

Strengths:

In thoughtfully designed figures, the authors identify both known and new candidate gene regulatory networks in differentiating XX and XY PGCs and sex-specific interactions of PGCs with supporting cells. In XY germ cells, novel findings include the predicted set of TFs regulating Bnc2, which is known to promote mitotic arrest, as well as the TFs POU6F1/2 and FOXK2 and their predicted targets that function in mitosis and signal transduction. In XX germ cells, the authors deconstruct the regulation of the premeiotic replication factor Stra8, which reveals TFs involved in meiosis, retinoic acid signaling, pluripotency and epigenetics among predictions; this finding, along with evidence supporting regulatory potential of retinoic acid receptors in meiotic gene expression is an important addition to the debate over the necessity of retinoic acid in XX meiotic initiation. In addition, a self-regulatory network of other TFs is hypothesized in XX differentiating PGCs, including TFAP2c, TCF5, ZFX, MGA and NR6A1, which is predicted to turn on meiotic and Wnt signaling targets. Finally, analysis of PGC-support cell interactions during sex differentiation reveals substantially more interactions in XX, via WNTs and BMPs, as well as some new signaling pathways that predominate in XY PGCs including ephrins, CADM1, Desert Hedgehog and matrix metalloproteases. This dataset will be an excellent resource for the community, motivating functional studies and serving as a discovery platform.

Weaknesses:

While the authors performed all of their comparisons between XX versus XY datasets at each timepoint, a more systematic analysis of expression and accessibility changes across time for each sex would be valuable. It remains possible that common mechanisms of differentiation to XX and XY could be missing from this analysis that focused on sex-specific differences.

Specific Questions:

(1) Line 461: "the population of E13.5 XX PGCs displaying the strongest Stra8 expression levels corresponded to the same population of XX PGCs with the highest module score of early meiotic prophase I genes (Fig. 3c; Supplementary Fig. 3a-b)" however the Stra8+ XX PGCs that do not robustly express meiotic genes should be examined to understand more about their differentiation potential. The authors are well-poised to identify the likely trajectories available to cell subsets in their dataset, and not doing so is a missed opportunity.

(2) The authors state that "we found that Stra8, Rec8, Rnf2, Sycp1, Sycp2, Ccnb3, and Zglp1 contain the RA receptor motifs in their regulatory sequences (Supplementary Figure 4g)." What is the strength of the RA->meiosis pathway compared to other mechanisms regulating meiosis? Perhaps the authors could take this analysis further with the following questions: (1) ask whether meiotic genes more enriched in RA motifs compared to other expressed genes or other motifs (2) compare the strength of peak-gene correlations for all peaks containing RA receptor motifs vs. those with peaks for Zglp1, Rnf2, etc binding. The strengths of these correlations could provide clues to how much gene expression varies in response to RA exposure vs. modulation of these other factors and thus tell us something about how much RA is playing a role.

(3) In figure 4, the shift from promoters in E11.5 XX PGCs to distal intergenic regions is fascinating. What can we learn about epigenetic reprogramming/methylation changes across gene bodies?

(4) The overlap between gene targets of TCFL5 with other highly expressed TFs differentially upregulated in E13.5 XX PGCs over XY suggests ambiguity regarding its role as a central or high-level regulator of differentiation; as in vivo validation has not been performed, I suggest softening this conclusion.

Reviewer #3 (Public review):

Summary:

Alexander et al. reported the gene-regulatory networks underpinning sex determination of murine primordial germ cells (PGCs) through single-nucleus multiomics, offering a detailed chromatin accessibility and gene expression map across three embryonic stages in both male (XY) and female (XX) mice. It highlights how regulatory element accessibility may precede gene expression, pointing to chromatin accessibility as a primer for lineage commitment before differentiation. Sexual dimorphism in these elements and gene expression increases over time, and the study maps transcription factors regulating sexually dimorphic genes in PGCs, identifying sex-specific enrichment in various transcription factors.

Strengths:

The study includes step-wise multiomic analysis with some computational approach to identify candidate TFs regulating XX and XY PGC gene expression, providing a detailed timeline of chromatin accessibility and gene expression during PGC development, which identifies previously unknown PGC subpopulations and offers a multimodal reference atlas of differentiating PGC clusters. Furthermore, the study maps a complex network of transcription factors associated with sex determination in PGCs, adding depth to our understanding of these processes.

Weaknesses:

While the multiomics approach is powerful, it primarily offers correlational insights between chromatin accessibility, gene expression, and transcription factor activity, without direct functional validation of identified regulatory networks.

Comments on revised version:

The authors have answered my questions and concerns in the revised manuscript and correspondence.

Reviewer #1 (Public review):

Summary:

Authors constructed a novel HSV-based therapeutic vaccine to cure SIV in a primate model. The novel HSV vector is deleted for ICP34.5. Evidence is given that this protein blocks HIV reactivation by interference with the NFkappaB pathway. The deleted construct supposedly would reactivate SIV from latency. The SIV genes carried by the vector ought to elicit a strong immune response. Together the HSV vector would elicit a shock and kill effect. This is tested in a primate model.

Strengths and weaknesses:

(1) Deleting ICP34.5 from the HSV construct has a very strong effect on HIV reactivation. The mechanism underlying increased activation by deleting ICP34.5 is only partially explored. Overexpression of ICP34.5 has a much smaller effect (reduction in reactivation) than deletion of ICP34.5 (strong activation); this is acknowledged by the authors that no full mechanistic explanation can be given at this moment.

(2) No toxicity data are given for deleting ICP34.5. How specific is the effect for HIV reactivation? A RNA seq analysis is required to show the effect on cellular genes.

A RNA seq analysis was done in the revised manuscript comparing the effect of HSV-1 and deleted vector in J-LAT cells (Fig S5). More than 2000 genes are upregulated after transduction with the modified vector in comparison with the WT vector. Hence, the specificity of upregulation of SIV genes is questioned. Authors do NOT comment on these findings. In my view it questions the utility of this approach.

(3) The primate groups are too small and the results to variable to make averages. In Fig 5, the group with ART and saline has two slow rebounders. It is not correct to average those with the single quick rebounder. Here the interpretation is NOT supported by the data.

Although authors provided some promising SIV DNA data, no additional animals were added. Groups of 3 animals are too small to make any conclusion, especially since the huge variability in response. The average numbers out of 3 are still presented in the paper, which is not proper science.

No data are given of the effect of the deletion in primates. Now the deleted construct is compared with an empty vector containing no SIV genes. Authors provide new data in Fig S2 on the comparison of WT and modified vector in cells from PLWH, but data are not that convincing. A significant difference in reactivation is seen for LTR in only 2/4 donors and in Gag in 3/4 donors. (Additional question what is meaning of LTR mRNA, do authors relate to genomic RNA??)

Discussion

HSV vectors are mainly used in cancer treatment partially due to induced inflammation. Whether these are suitable to cure PLWH without major symptoms is a bit questionable to me and should at least be argued for.

The RNA seq data add on to this worry and should at least be discussed.

Comments on revisions:

The authors accept the limitations of the primate study (too small for strong conclusions). The new way of presenting the data clearly shows these limitations.

Reviewer #1 (Public review):

Summary:

By using the biophysical chromosome stretching, the authors measured the stiffness of chromosomes of mouse oocytes in meiosis I (MI) and meiosis II (MII). This study was the follow-up of previous studies in spermatocytes (and oocytes) by the authors (Biggs et al. Commun. Biol. 2020: Hornick et al. J. Assist. Rep. and Genet. 2015). They showed that MI chromosomes are much stiffer (~10 fold) than mitotic chromosomes of mouse embryonic fibroblast (MEF) cells. MII chromosomes are also stiffer than the mitotic chromosomes. The authors also found that oocyte aging increases the stiffness of the chromosomes. Surprisingly, the stiffness of meiotic chromosomes is independent of meiotic chromosome components, Rec8, Stag3, and Rad21L. and aging increases the stiffness.

Strengths

This provides a new insight into the biophysical property of meiotic chromosomes, that is chromosome stiffness. The stiffness of chromosomes in meiosis prophase I is ~10-fold higher than that of mitotic chromosomes, which is independent of meiotic cohesin. The increased stiffness during oocyte aging is a novel finding.

Weaknesses:

A major weakness of this paper is that it does not provide any molecular mechanism underlying the difference between MI and MII chromosomes (and/or prophase I and mitotic chromosomes).

Comments on revisions:

The main text lacks the first page with the authors' names and their affiliations (and corresponding authors etc).

Reviewer #2 (Public review):

Initial Review:

This paper reports investigations of chromosome stiffness in oocytes and spermatocytes> the paper shows that prophase I spermatocytes and MI/MII oocytes yield high Young Modulus values in the assay the authors applied. Deficiency in each one of three meiosis-specific cohesins they claim did not affect this result and increased stiffness was seen in aged oocytes but not in oocytes treated with the DNA-damaging agent etoposide.

The paper reports some interesting observations which are in line with a report by the same authors of 2020 where increased stiffness of spermatocyte chromosomes was already shown. In that sense, it the current manuscript is an extension of that previous paper and thus novelty is somewhat limited. The paper is also largely descriptive as it does neither propose mechanism nor report factors that determine the chromosomal stiffness.

There are several points that need to be considered.

Limitations of the study and the conclusions are not discussed in "Discussion"; that's a significant gap. Even more so as the authors rely on just one experimental system for all their data - no independent verification - and that in vitro system may be prone to artefacts.

It is somewhat unfortunate that they jump between oocytes and spermatocytes to address the cohesin question. Prophase I (pachytene) spermatocytes chromosomes are not directly comparable to MI or MII oocyte chromosomes. In fact, the authors report Young Modulus values of 3700 for MI oocytes and only 2700 for spermatocyte prophase chromosomes, illustrating this difference. Why not using oocyte-specific cohesin deficiencies?

It remains unclear whether the treatment of oocytes with the detergent TritonX-100 affects the spindle and thus the chromosomes isolated directly from the Triton-lysed oocytes. In fact, it is rather likely that the detergent affects chromatin-associated proteins and thus structural features of the chromosomes.

Why did the authors use mouse strains of different genetic background, CD-1 and C57BL/6? That makes comparison difficult. Breeding of heterozygous cohesin mutants will yield the ideal controls, i.e. littermates.

How did the authors capture chromosome axes from STAG3-deficient spermatocytes which feature very little if any axes? How representative are those chromosomes that could be captured?

Line 135: that statement is not substantiated; better to show retraction data and full reversibility.

Line 144: the authors claim that the Young Modulus of MII oocytes is "slightly" higher than that of mitotic cells (MEFs). Well, "slightly" means it is rather similar and therefore the commonly used statement that MII is similar to mitosis is OK - contrary to the authors claim.

There are a lot of awkward sentences in this text. Some sentences lack words, are not sufficiently precise in wording and/or logic, and there are numerous typos. Some examples can be found in lines 89 (grammar), 94, 95 ("looked"), 98, 101 ("difference" - between what?), and some are commonplaces or superficial (lines 92/93, 120..., ). Occasionally the present and past tense are mixed (e.g. in M&M). Thus the manuscript is quite badly written.

Comments on revisions:

In their revised paper, Liu et al have addressed a number of my concerns and thus the paper is clearly improved in several details, e.g. in showing a control for a potential effect of the detergent (new supplies. fig. 5). Other points were not sufficiently addressed though.

I remain sceptical about using mice of a substantially different genetic background (CD1) as controls in the analysis of the cohesin mutants (C57BL/6). The argument that C57BL/6 yield smaller litter size is, frankly, ridiculous. Hundreds of labs worldwide extensively and successfully work with C57BL/6. Further, the paper Liu et al. cite to argue that there are no (or minor) differences in chromosome structure (Biggs et al., 2020, which is from the same lab) of the two mouse strains deals with spermatocyte chromosomes only. Nothing there on oocyte chromosomes. And there is no direct comparison within the same experimental setting since in Biggs et al only C57BL/6 is used (sic!). Thus, this is not a convincing argument. It would also be reassuring to see an independent reference directly comparing different genetic backgrounds (authors may have a look at older papers of Pat Hunt/Terry Hassold where they may find some data). In my experience, differences in genetic background do play a very clear role in meiosis, e.g. in the timing of juvenile spermatogenesis, in the onset of puberty, in the kinetics of oocyte maturation, in the success of PBE, and in biophysical properties as seen in the stability of oocytes during experimental handling. In fact, the authors themselves indicate differences in reproduction by stating the low litter size of C57BL/6. Thus, I strongly advise carrying out at least a few key experiments using C57BL/6 control mice (which can very easily and cheaply be obtained from vendors; the authors have used C57BL/6 wt before - see their 2020 paper).

The answer to my question #5 is not really satisfactory. I asked specifically how the authors isolated the very small chromosomes from Stag3-/- spermatocytes, where the axes are almost non-existing. The authors refer to suppl. fig. 3, but that shows isolation from Rec8-/- spermatocytes, which still have nicely visible, well-formed, shortened axes. Suppl. fig. 4 shows this for Rad21l-/-. Why not show this for the Stag3-/-, which in this respect is the most critical and difficult, and specifically answer my question?

The overall criticism of the lack of conceptual novelty of the basic message of the paper and of very little if any insights into the mechanisms and factors determining the changes in chromosome stiffness remains.

Reviewer #2 (Public review):

Summary:

The authors used a yeast model for analyzing Parkinson's disease-associated synphilin-1 inclusion bodies (SY1 IBs). In this model system, large SY1 IBs are efficiently formed from smaller potentially more toxic SY1 aggregates. Using a genome-wide approach (synthetic genetic array, SGA, combined with a high content imaging approach), the authors identified the sphingolipid metabolic pathway as pivotal for SY1 IBs formation. Disturbances of this pathway increased SY1-triggered growth deficits, loss of mitochondrial membrane potential, increased production of reactive oxygen species (ROS), and decreased cellular ATP levels pointing to an increased energy crisis within affected cells. Notably, SY1 IBs were found to be surrounded by mitochondrial membranes using state-of-the-art super-resolution microscopy. Finally, the effects observed in the yeast for SY1 IBs turned out to be evolutionary conserved in mammalian cells. Thus, sphingolipid metabolism might play an important role in the detoxification of misfolded proteins by large IBs formation at the mitochondrial outer membrane.

Strengths:

• The SY1 IB yeast model is very suitable for the analysis of genes involved in IB formation.<br /> • The genome-wide approach combining a synthetic genetic array (SGA) with a high content imaging approach is a compelling approach and enabled the reliable identification of novel genes. The authors tightly checked the output of the screen.<br /> • The authors clearly showed, including a couple of control experiments, that the sphingolipid metabolic pathway is crucial for SY1 IB formation and cytotoxicity.<br /> • The localization of SY1 IBs at mitochondrial membranes has been clearly demonstrated with state-of-the-art super-resolution microscopy and biochemical methods.<br /> • Pharmacological manipulation of the sphingolipid pathway influenced mitochondrial function and cell survival.<br /> • The authors have carefully redone critical experiments to avoid any misleading interpretation of data.

Weaknesses:

• It remains unclear how sphingolipids are involved in SY1 IB formation.

Comments on revisions: No further comments

Reviewer #1 (Public review):

Summary:

This paper introduces a new approach for modeling human behavioral responses using image-computable models. They create a model (VAM) that is a combination of a standard CNN coupled with a standard evidence accumulation model (EAM). The combined model is then trained directly on image-level data using human behavioral responses. This approach is original and can have wide applicability. However, many of the specific findings reported are less compelling.

Strengths:

(1) The manuscript presents an original approach of fitting an image-computable model to human behavioral data. This type of approach is sorely needed in the field.<br /> (2) The analyses are very technically sophisticated.<br /> (3) The behavioral data are large both in terms of sample size (N=75) and in terms of trials per subject.

Weaknesses:

(1) The main advance here thus appears to be methodological rather than conceptual. It's really cool that VAMs are image computable and are also fit to human data. But what we learn about the mind or brain is perhaps more modest.<br /> (2) In the approach here, a given stimulus is always processed in the same way through the core CNN to produce activations v_k. These v_k's are then corrupted by Gaussian noise to produce drift rates d_k, which can differ from trial to trial even for the same stimulus. In other words, the assumption built into VAM appears to be that the drift rate variability stems entirely from post-sensory (decisional) noise. In contrast, the typical interpretation of EAMs is that the variability in drift rates is sensory. In response to this concern, the authors responded that one can imagine an additional (unmodeled) sensory process that adds variability to the drift rates. However, this process remains unmodeled. The authors motivate their paper by saying "EAMs do not explain how the visual system extracts these representations in the first place" (second sentence of the Abstract). VAM is definitely a step in this direction but there's still a gap between the current VAM implementation and sensory systems.

Reviewer #2 (Public review):

In An image-computable model of speeded decision-making, the authors introduce and fit a combined CCN-EAM (a 'VAM') to flanker-task-like data. They show that the VAM can fit mean RTs and accuracies as well as the congruency effect that is present in the data, and subsequently analyze the VAM in terms of where in the network congruency effects arise.

I have mixed feelings about this manuscript, as I appreciate the innovative efforts to combine CNNs with EAMs in a new class of cognitive models, while also having some reservations from an EAM perspective. The idea of combining these approaches has great potential, and I'm excited to see where this research will lead. However, I do have some concerns about the quality of fit between the behavioral data and the model. Specifically, the RT distributions, delta plots, and conditional accuracy function don't appear to be well-matched by the VAM. The conflict effects on behavioral data are well-established and typically considered crucial to understanding the underlying cognitive process. Unfortunately, it seems that these parts of the data don't fit well with the proposed model.

This disparity is not entirely surprising. The EAM literature suggests that LBA models might not be suitable for conflict tasks, and the presented results seem to confirm this concern. Conflict EAMs, including the DMC (e.g., Ulrich et al., 2015; Evans & Servant, 2022; Lee & Sewell 2024), propose dynamic drift rates with a fast automatic process that is gradually withdrawn from evidence accumulation over time. This approach results in congruency effects arising from temporal dynamics, not spatial representations.<br /> In contrast, the VAM imposes static drift rates in the LBA model, leading to an effect between drift rates that translates to changes in representations. However, this account does not adequately explain the behavioral data, and the proposed representational geometry explanation is therefore limited.

My concerns are addressed in the revised manuscript, but I struggle to understand why the authors distinguish between explaining mean effects across individuals and congruency effects within individuals. These concepts seem related, and issues at the individual level could propagate to the group mean. Furthermore, I find it challenging to accept that dynamics merely act 'in concert' with the orthogonalization mechanism, as it seems possible that an account that uses a time-varying EAM may not require any orthogonalization mechanism in the first place. The orthogonalization mechanism might have arisen because the model does not have the possibility to account for the conflict effect from temporal effects, instead of spatial effects. I could envision a CNN-DMC in which conflict effects arise only at the level of the choice model (e.g., as a time-varying filter that changes which information is read out from the visual system, rather than due to changes in the representations in the visual system itself). This possibility should be acknowledged in the paper, and it would be interesting to discuss how such an account would be tested.

While I appreciate the technological advancement presented in this paper, my concerns are not about implementation details but rather about the choice of models and their consequences. I believe that a more in-depth exploration of which conclusions can be drawn, and which model comparisons would be required to reach a final conclusion.

Reviewer #1 (Public review):

Summary:

The authors aimed to modify the characteristics of the extracellular matrix (ECM) produced by immortalized mesenchymal stem cells (MSCs) by employing the CRISPR/Cas9 system to knock out specific genes. Initially, they established VEGF-KO cell lines, demonstrating that these cells retained chondrogenic and angiogenic properties. Additionally, lyophilized carriage tissues produced by these cells exhibited retained osteogenic properties.

Subsequently, the authors established RUNX2-KO cell lines, which exhibited reduced COLX expression during chondrogenic differentiation and notably diminished osteogenic properties in vitro. Transplantation of lyophilized carriage tissues produced by RUNX2-KO cell lines into osteochondral defects in rat knee joints resulted in the regeneration of articular cartilage tissues as well as bone tissues, a phenomenon not observed with tissues derived from parental cells. This suggests that gene-edited MSCs represent a valuable cell source for producing ECM with enhanced quality.

Strengths:

The enhanced cartilage regeneration observed with ECM derived from RUNX2-KO cells supports the authors' strategy of creating gene-edited MSCs capable of producing ECM with superior quality. Immortalized cell lines offer a limitless source of off-the-shelf material for tissue regeneration.

Weaknesses:

Most of the data align with anticipated outcomes, offering limited novelty to advance scientific understanding. Methodologically, the chondrogenic differentiation properties of immortalized MSCs appeared deficient, evidenced by Safranin-O staining of 3D tissues and histological findings lacking robust evidence for endochondral differentiation. This presents a critical limitation, particularly as authors propose the implantation of cartilage tissues for in vivo experiments. Instead, the bulk of data stemmed from type I collagen scaffold with factors produced by MSCs stimulated by TGFβ.

In the revised version, the authors presented Safranin-O staining results of pellets prior to lyophilization. The inset of figures showing entire pellets revealed that Safranin-O-positive areas were limited, suggesting that cells in the negative regions had not differentiated into chondrocytes. In Figure 3F, DAPI staining showed devitalized cells in the outer layer but was negative in the central part, indicating the absence of cells in these areas and incomplete differentiation induction.

The rationale for establishing VEGF-KO cell lines remains unclear, and the authors' explanation in the revised manuscript is still equivocal. While they mention that VEGF is a late marker for endochondral ossification, the data in Figures 1D and 1E clearly show that VEGF-KO affects the early phase of endochondral ossification.

Insufficient depth was given to elucidate the disparity in osteogenic properties between those observed in ectopic bone formation and those observed in transplantation into osteochondral defects.

In the ectopic bone formation study, most of the collagenous matrix observed at 2 weeks was resorbed by 6 weeks, with only a small amount contributing to bone formation in MSOD-B cells (Figs. 2I and 4C). This finding does not align with the micro-CT data presented in Figures 2H and 4B. For the micro-CT experiments, it would be more appropriate to use a standard window for bone and present the data accordingly.

While the regeneration of articular cartilage in RUNX2-KO ECM presents intriguing results, the study lacked an exploration into underlying mechanisms, such as histological analyses at earlier time points.

Reviewer #3 (Public review):

Summary:

In this study, the authors have started off using an immortalized human cell line and then gene edited it to decrease the levels of VEGF1 (in order to influence vascularization), and the levels of Runx2 (to decrease osteogenesis). They first transplanted these cells with a collagen scaffold. The modified cells showed a decrease in vascularization when VEGF1 was decreased, and suggested an increase in cartilage formation.

In another study, matrix generated by these cells subsequently remodeled into a bone marrow organ. When RUNX2 was decreased, the cells did not mineralize in vitro, and their matrices expressed types I and II collagen but not type X collagen in vitro, in comparison with unedited cells. In vivo, the author claims that remodeling of the matrices into bone was somewhat inhibited. Lastly, they utilized matrices generated by RUNX2-edited cells to regenerate chondro-osteal defects. They suggest that the edited cells regenerated cartilage in comparison with unedited cells.

Strengths:

- The notion that inducing changes in the ECM by genetically editing the cells is a novel one, as it has long been thought that ECM composition influences cell activity.<br /> - If successful, it may be possible to make off the shelf ECMS to carry out different types of tissue repair.

Weaknesses:

- The authors have not demonstrated robust cartilage formation (quantitation would be useful).<br /> - Measuring total GAG content does not prove the presence of cartilage<br /> - There are numerous overstatements about forming and implanting cartilage.<br /> - Although it is implied, RUNX2 deletion did not improve cartilage formation by the modified cells.<br /> - In the control line, MSOD-B there were variability in the amount of safranin O positive material in various histological panels in the figures.; more quantitation is needed.<br /> - In the in vivo articular defect experiments, an untreated injured joint is needed as a negative control.<br /> - Statements about bone generation are often not reflective of the microCT data presented.<br /> - The discussion over-interprets the results.

Reviewer #1 (Public review):

Summary:

In their previous publication (Dong et al. Cell Reports 2024), the authors showed that citalopram treatment resulted in reduced tumor size by binding to the E380 site of GLUT1 and inhibiting the glycolytic metabolism of HCC cells, instead of the classical citalopram receptor. Given that C5aR1 was also identified as the potential receptor of citalopram in the previous report, the authors focused on exploring the potential of the immune-dependent anti-tumor effect of citalopram via C5aR1. C5aR1 was found to be expressed on tumor-associated macrophages (TAMs) and citalopram administration showed potential to improve the stability of C5aR1 in vitro. Through macrophage depletion and adoptive transfer approaches in HCC mouse models, the data demonstrated the potential importance of C5aR1-expressing macrophage in the anti-tumor effect of citalopram in vivo. Mechanistically, their in vitro data suggested that citalopram may regulate the phagocytosis potential and polarization of macrophages through C5aR1. Next, they tried to investigate the direct link between citalopram and CD8+T cells by including an additional MASH-associated HCC mouse model. Their data suggest that citalopram may upregulate the glycolytic metabolism of CD8+T cells, probability via GLUT3 but not GLUT1-mediated glucose uptake. Lastly, as the systemic 5-HT level is down-regulated by citalopram, the authors analyzed the association between a low 5-HT and a superior CD8+T cell function against a tumor. Although the data is informative, the rationale for working on additional mechanisms and logical links among different parts is not clear. In addition, some of the conclusion is also not fully supported by the current data.

Strengths:

The idea of repurposing clinical-in-used drugs showed great potential for immediate clinical translation. The data here suggested that the anti-depression drug, citalopram displayed an immune regulatory role on TAM via a new target C5aR1 in HCC.

Weaknesses:

(1) The authors concluded that citalopram had a 'potential immune-dependent effect' based on the tumor weight difference between Rag-/- and C57 mice in Figure 1. However, tumor weight differences may also be attributed to a non-immune regulatory pathway. In addition, how do the authors calculate relative tumor weight? What is the rationale for using relative one but not absolute tumor weight to reflect the anti-tumor effect?

(2) The authors used shSlc6a4 tumor cell lines to demonstrate that citalopram's effects are independent of the conventional SERT receptor (Figure 1C-F). However, this does not entirely exclude the possibility that SERT may still play a role in this context, as it can be expressed in other cells within the tumor microenvironment. What is the expression profiling of Slc6a4 in the HCC tumor microenvironment? In addition, in Figure 1F, the tumor growth of shSlc6a4 in C57 mice displayed a decreased trend, suggesting a possible role of Slc6a4.

(3) Why did the authors choose to study phagocytosis in Figures 3G-H? As an important player, TAM regulates tumor growth via various mechanisms.

(4) The information on unchanged deposition of C5a has been mentioned in this manuscript (Figures 3D and 3F), the authors should explain further in the manuscript, for example, C5a could bind to receptors other than C5aR1 and/or C5a bind to C5aR1 by different docking anchors compared with citalopram.

(5) Figure 3I-M - the flow cytometry data suggested that citalopram treatment altered the proportions of total TAM, M1 and M2 subsets, CD4+ and CD8+T cells, DCs, and B cells. Why does the author conclude that the enhanced phagocytosis of TAM was one of the major mechanisms of citalopram? As the overall TAM number was regulated, the contribution of phagocytosis to tumor growth may be limited.

(6) Figure 4 - what is the rationale for using the MASH-associated HCC mouse model to study metabolic regulation in CD8+T cells? The tumor microenvironment and tumor growth would be quite different. In addition, how does this part link up with the mechanisms related to C5aR1 and TAM? The authors also brought GLUT1 back in the last part and focused on CD8+T cell metabolism, which was totally separated from previous data.

(7) Figure 5, the authors illustrated their mechanism that citalopram regulates CD8+T cell anti-tumor immunity through proinflammatory TAM with no experimental evidence. Using only CD206 and MHCII to represent TAM subsets obviously is not sufficient.

Reviewer #2 (Public review):

Summary:

Dong et al. present a thorough investigation into the potential of repurposing citalopram, an SSRI, for hepatocellular carcinoma (HCC) therapy. The study highlights the dual mechanisms by which citalopram exerts anti-tumor effects: reprogramming tumor-associated macrophages (TAMs) toward an anti-tumor phenotype via C5aR1 modulation and suppressing cancer cell metabolism through GLUT1 inhibition while enhancing CD8+ T cell activation. The findings emphasize the potential of drug repurposing strategies and position C5aR1 as a promising immunotherapeutic target. However, certain aspects of experimental design and clinical relevance could be further developed to strengthen the study's impact.

Strength:

It provides detailed evidence of citalopram's non-canonical action on C5aR1, demonstrating its ability to modulate macrophage behavior and enhance CD8+ T cell cytotoxicity. The use of DARTS assays, in silico docking, and gene signature network analyses offers robust validation of drug-target interactions. Additionally, the dual focus on immune cell reprogramming and metabolic suppression presents a thorough strategy for HCC therapy. By emphasizing the potential for existing drugs like citalopram to be repurposed, the study also underscores the feasibility of translational applications.

Major weaknesses/suggestions:

The dataset and signature database used for GSEA analyses are not clearly specified, limiting reproducibility. The manuscript does not fully explore the potential promiscuity of citalopram's interactions across GLUT1, C5aR1, and SERT1, which could provide a deeper understanding of binding selectivity. The absence of GLUT1 knockdown or knockout experiments in macrophages prevents a complete assessment of GLUT1's role in macrophage versus tumor cell metabolism. Furthermore, there is minimal discussion of clinical data on SSRI use in HCC patients. Incorporating survival outcomes based on SSRI treatment could strengthen the study's translational relevance.

By addressing these limitations, the manuscript could make an even stronger contribution to the fields of cancer immunotherapy and drug repurposing.

Reviewer #1 (Public review):

Summary:

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

Strengths:

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

Weaknesses:

My major concerns are described below.

If I understand the task design correctly, the monkeys did not need to stop their hand at the target. I think this design may be suboptimal for investigating the role of the cerebellum in control of reaching because a number of earlier works have found that the cerebellum's contributions are particularly significant as the movement ends, i.e., stopping at the target. For example, in mice, interposed nucleus neurons tend to be most active near the end of the reach that requires extension, and their activation produces flexion forces during the reach (Becker and Person 2019). Indeed, the inactivation of interposed neurons that project to the thalamus results in overshooting of reaching movements (Low et al. 2018). Recent work has also found that many Purkinje cells show a burst-pause pattern as the reach nears its endpoint, and stimulation of the mossy fibers tends to disrupt endpoint control (Calame et al. 2023). Thus, the fact that the current paper has no data regarding endpoint control of the reach is puzzling to me.

Because stimulation continued after the cursor had crossed the target, it is interesting to ask whether this disruption had any effects on the movements that were task-irrelevant. The reason for asking this is because we have found that whereas during task-relevant eye or tongue movements the Purkinje cells are strongly modulated, the modulations are much more muted when similar movements are performed but are task-irrelevant (Pi et al., PNAS 2024; Hage et al. Biorxiv 2024). Thus, it is interesting to ask whether the effects of stimulation were global and affected all movements, or were the effects primarily concerned with the task-relevant movements.

If the schematic in Figure 1 is accurate, it is difficult for me to see how any of the reaching movements can be termed single joint. In the paper, T1 is labeled as a single joint, and T2-T4 are labeled as dual-joint. The authors should provide data to justify this.

Because at least part of this work was previously analyzed and published, information should be provided regarding which data are new.

Reviewer #2 (Public review):

This manuscript asks an interesting and important question: what part of 'cerebellar' motor dysfunction is an acute control problem vs a compensatory strategy to the acute control issue? The authors use a cerebellar 'blockade' protocol, consisting of high-frequency stimuli applied to the cerebellar peduncle which is thought to interfere with outflow signals. This protocol was applied in monkeys performing center outreaching movements and has been published from this laboratory in several preceding studies. I found the take-home-message broadly convincing and clarifying - that cerebellar block reduces muscle activation acutely particularly in movements that involve multiple joints and therefore invoke interaction torques, and that movements progressively slow down to in effect 'compensate' for these acute tone deficits. The manuscript was generally well written, and the data was clear, convincing, and novel. My comments below highlight suggestions to improve clarity and sharpen some arguments.

Primary comments:

(1) Torque vs. tone: Is it known whether this type of cerebellar blockade is reducing muscle tone or inducing any type of acute co-contraction that could influence limb velocity through mechanisms different than 'atonia'? If so, the authors should discuss this information in the discussion section starting around line 336, and clarify that this motivates (if it does) the focus on 'torques' rather than muscle activation. Relatedly, besides the fact that there are joints involved, is there a reason there is so much emphasis on torque per se? If the muscle is deprived of sufficient drive, it would seem that it would be more straightforward to conceptualize the deficit as one of insufficient timed drive to a set of muscles than joint force. Some text better contextualizing the choices made here would be sufficient to address this concern. I found statements like those in the introduction "hand velocity was low initially, reflecting a primary muscle torque deficit" to be lacking in substance. Either that statement is self-evident or the alternative was not made clear. Finally, emphasize that it is a loss of self-generated torque at the shoulder that accounts for the velocity deficits. At times the phrasing makes it seem that there is a loss of some kind of passive torque.

(2) Please clarify some of the experimental metrics: Ln 94 RESULTS. The success rate is used as a primary behavioral readout, but what constitutes success is not clearly defined in the methods. In addition to providing a clear definition in the methods section, it would also be helpful for the authors to provide a brief list of criteria used to determine a 'successful' movement in the results section before the behavioral consequences of stimulation are described. In particular, the time and positional error requirements should be clear.

(3) Based on the polar plot in Figure 1c, it seemed odd to consider Targets 1-4 outward and 5-8 inward movements, when 1 and 5 are side-to-side. Is there a rationale for this grouping or might results be cleaner by cleanly segregating outward (targets 2-4) and inward (targets 6-8) movements? Indeed, by Figure 3 where interaction torques are measured, this grouping would seem to align with the hypothesis much more cleanly since it is with T2,T3,and T4 where clear coupling torques deficits are seen with cerebellar block.

4. I did not follow Figure 3d. Both the figure axis labels and the description in the main text were difficult to follow. Furthermore, the color code per animal made me question whether the linear regression across the entire dataset was valid, or would be better performed within animal, and the regressions summarized across animals. The authors should look again at this section and figure.

(5) Line 206+ The rationale for examining movement decomposition with a cerebellar block is presented as testing the role of the cerebellum in timing. Yet it is not spelled out what movement decomposition and trajectory variability have to do with motor timing per se.

Reviewer #3 (Public review):

Summary:

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

Strengths:

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

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

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

Weaknesses:

The argument that there are acute and adaptive effects to perturbing cerebellar circuits is compelling, but there seems to be a lost opportunity to leverage the fast and reversible nature of the perturbations to further test this idea and strengthen the interpretation. Specifically, the authors could have bolstered this argument by looking at the effects of terminating HFS - one might hypothesize that the acute impacts on muscle torques would quickly return to baseline in the absence of HFS, whereas the longer-term adaptive component would persist in the form of aftereffects during the 'washout' period. As is, the reversible nature of the perturbation seems underutilized in testing the authors' ideas.

The analysis showing that there is a gradual reduction in velocity during what the authors call an adaptive phase is convincing. That said, the argument is made that this is due to difficulty in compensating for interaction torques. Even if the inward targets (i.e., targets 6-8) do not show a deficit during the acute phase, these targets still have significant interaction torques (Figure 3c). Given the interpretation of the data as presented, it is not clear why disruption of movement during the adaptive phase would not be seen for these targets as well since they also have large interaction torques. Moreover, it is difficult to delve into this issue in more detail, as the analyses in Figures 4 and 5 omit the inward targets.

The text in the Introduction and in the prior work developing the HFS approach overstates the selectivity of the perturbations. First, there is an emphasis on signals transmitted to the neocortex. As the authors state several times in the Discussion, there are many subcortical targets of the cerebellar nuclei as well, and thus it is difficult to disentangle target-specific behavioral effects using this approach. Second, the superior cerebellar peduncle contains both cerebellar outputs and inputs (e.g., spinocerebellar). Therefore, the selectivity in perturbing cerebellar output feels overstated. Readers would benefit from a more agnostic claim that HFS affects cerebellar communication with the rest of the nervous system, which would not affect the major findings of the study.

The text implies that increased movement decomposition and variability must be due to noise. However, this assumption is not tested. It is possible that the impairments observed are caused by disrupted commands, independent of whether these command signals are noisy. In other words, commands could be low noise but still faulty.

Throughout the text, the use of the term 'feedforward control' seems unnecessary. To dig into the feedforward component of the deficit, the authors could quantify the trajectory errors only at the earliest time points (e.g., in Figure 5d), but even with this analysis, it is difficult to disentangle feedforward- and feedback-mediated effects when deficits are seen throughout the reach. While outside the scope of this study, it would be interesting to explore how feedback responses to limb perturbation are affected in control versus HFS conditions. However, as is, these questions are not explored, and the claim of impaired feedforward control feels overstated.

The terminology 'single-joint' movement is a bit confusing. At a minimum, it would be nice to show kinematics during different target reaches to demonstrate that certain targets are indeed single joint movements. More of an issue, however, is that it seems like these are not actually 'single-joint' movements. For example, Figure 2c shows that target 1 exhibits high elbow and shoulder torques, but in the text, T1 is described as a 'single-joint' reach (e.g. lines 155-156). The point that I think the authors are making is that these targets have low interaction torques. If that is the case, the terminology should be changed or clarified to avoid confusion.

The labels in Figure 3d are confusing and could use more explanation in the figure legend.

In Figure 3d, it is stated that data from all monkeys is pooled. However, if there is a systematic bias between animals, this could generate spurious correlations. Were correlations also calculated for each animal separately to confirm the same trend between velocity and coupling torques holds for each animal?

In Table S1, it would be nice to see target-specific success rates. The data would suggest that targets with the highest interaction torques will have the largest reduction in success rates, especially during later HFS trials. Is this the case?

Reviewer #1 (Public review):

Summary:

Measurement of BOLD MR imaging has regularly found regions of the brain that show reliable suppression of BOLD responses during specific experimental testing conditions. These observations are to some degree unexplained, in comparison with more usual association between activation of the BOLD response and excitatory activation of the neurons (most tightly linked to synaptic activity) in the same brain location. This paper finds two patients whose brains were tested with both non-invasive functional MRI and with invasive insertion of electrodes, which allowed the direct recording of neuronal activity. The electrode insertions were made within the fusiform gyrus, which is known to process information about faces, in a clinical search for the sites of intractable epilepsy in each patient. The simple observation is that the electrode location in one patient showed activation of the BOLD response and activation of neuronal firing in response to face stimuli. This is the classical association. The other patient showed an informative and different pattern of responses. In this person, the electrode location showed a suppression of the BOLD response to face stimuli and, most interestingly, an associated suppression of neuronal activity at the electrode site.

Strengths:

Whilst these results are not by themselves definitive, they add an important piece of evidence to a long-standing discussion about the origins of the BOLD response. The observation of decreased neuronal activation associated with negative BOLD is interesting because, at various times, exactly the opposite association has been predicted. It has been previously argued that if synaptic mechanisms of neuronal inhibition are responsible for the suppression of neuronal firing, then it would be reasonable

Weaknesses:

The chief weakness of the paper is that the results may be unique in a slightly awkward way. The observation of positive BOLD and neuronal activation is made at one brain site in one patient, while the complementary observation of negative BOLD and neuronal suppression actually derives from the other patient. Showing both effects in both patients would make a much stronger paper.

Reviewer #2 (Public review):

Summary:

This is a short and straightforward paper describing BOLD fMRI and depth electrode measurements from two regions of the fusiform gyrus that show either higher or lower BOLD responses to faces vs. objects (which I will call face-positive and face-negative regions). In these regions, which were studied separately in two patients undergoing epilepsy surgery, spiking activity increased for faces relative to objects in the face-positive region and decreased for faces relative to objects in the face-negative region. Interestingly, about 30% of neurons in the face-negative region did not respond to objects and decreased their responses below baseline in response to faces (absolute suppression).

Strengths:

These patient data are valuable, with many recording sessions and neurons from human face-selective regions, and the methods used for comparing face and object responses in both fMRI and electrode recordings were robust and well-established. The finding of absolute suppression could clarify the nature of face selectivity in human fusiform gyrus since previous fMRI studies of the face-negative region could not distinguish whether face < object responses came from absolute suppression, or just relatively lower but still positive responses to faces vs. objects.

Weaknesses:

The authors claim that the results tell us about both 1) face-selectivity in the fusiform gyrus, and 2) the physiological basis of the BOLD signal. However, I would like to see more of the data that supports the first claim, and I am not sure the second claim is supported.

(1) The authors report that ~30% of neurons showed absolute suppression, but those data are not shown separately from the neurons that only show relative reductions. It is difficult to evaluate the absolute suppression claim from the short assertion in the text alone (lines 105-106), although this is a critical claim in the paper.<br /> (2) I am not sure how much light the results shed on the physiological basis of the BOLD signal. The authors write that the results reveal "that BOLD decreases can be due to relative, but also absolute, spike suppression in the human brain" (line 120). But I think to make this claim, you would need a region that exclusively had neurons showing absolute suppression, not a region with a mix of neurons, some showing absolute suppression and some showing relative suppression, as here. The responses of both groups of neurons contribute to the measured BOLD signal, so it seems impossible to tell from these data how absolute suppression per se drives the BOLD response.

Reviewer #3 (Public review):

Summary:

In this paper the authors conduct two experiments an fMRI experiment and intracranial recordings of neurons in two patients P1 and P2. In both experiments, they employ a SSVEP paradigm in which they show images at a fast rate (e.g. 6Hz) and then they show face images at a slower rate (e.g. 1.2Hz), where the rest of the images are a variety of object images. In the first patient, they record from neurons over a region in the mid fusiform gyrus that is face-selective and in the second patient, they record neurons from a region more medially that is not face selective (it responds more strongly to objects than faces). Results find similar selectivity between the electrophysiology data and the fMRI data in that the location which shows higher fMRI to faces also finds face-selective neurons and the location which finds preference to non faces also shows non face preferring neurons.

Strengths:

The data is important in that it shows that there is a relationship between category selectivity measured from electrophysiology data and category-selective from fMRI. The data is unique as it contains a lot of single and multiunit recordings (245 units) from the human fusiform gyrus - which the authors point out - is a humanoid specific gyrus.

Weaknesses:

My major concerns are two-fold:<br /> (i) There is a paucity of data; Thus, more information (results and methods) is warranted; and in particular there is no comparison between the fMRI data and the SEEG data.

(ii) One main claim of the paper is that there is evidence for suppressed responses to faces in the non-face selective region. That is, the reduction in activation to faces in the non-face selective region is interpreted as a suppression in the neural response and consequently the reduction in fMRI signal is interpreted as suppression. However, the SSVEP paradigm has no baseline (it alternates between faces and objects) and therefore it cannot distinguish between lower firing rate to faces vs suppression of response to faces.

(1) Additional data: the paper has 2 figures: figure 1 which shows the experimental design and figure 2 which presents data, the latter shows one example neuron raster plot from each patient and group average neural data from each patient. In this reader's opinion this is insufficient data to support the conclusions of the paper. The paper will be more impactful if the researchers would report the data more comprehensively.

(a) There is no direct comparison between the fMRI data and the SEEG data, except for a comparison of the location of the electrodes relative to the statistical parametric map generated from a contrast (Fig 2a,d). It will be helpful to build a model linking between the neural responses to the voxel response in the same location - i.e., estimate from the electrophysiology data the fMRI data (e.g. Logothetis & Wandell, 2004)

(b) More comprehensive analyses of the SSVEP neural data: It will be helpful to show the results of the frequency analyses of the SSVEP data for all neurons to show that there are significant visual responses and significant face responses. It will be also useful to compare and quantify the magnitude of the face responses compared to the visual responses.

(c) The neuron shown in E shows cyclical responses tied to the onset of the stimuli, is this the visual response? If so, why is there an increase in the firing rate of the neuron before the face stimulus is shown in time 0? The neuron's data seems different than the average response across neurons; This raises a concern about interpreting the average response across neurons in panel F which seems different than the single neuron responses

(d) Related to (c) it would be useful to show raster plots of all neurons and quantify if the neural responses within a region are homogeneous or heterogeneous. This would add data relating the single neuron response to the population responses measured from fMRI. See also Nir 2009.

(e) When reporting group average data (e.g., Fig 2C,F) it is necessary to show standard deviation of the response across neurons.

(f) Is it possible to estimate the latency of the neural responses to face and object images from the phase data? If so, this will add important information on the timing of neural responses in the human fusiform gyrus to face and object images.

(g) Related to (e) In total the authors recorded data from 245 units (some single units and some multiunits) and they found that both in the face and nonface selective most of the recoded neurons exhibited face -selectivity, which this reader found confusing: They write " Among all visually responsive neurons, we 87 found a very high proportion of face-selective neurons (p < 0.05) in both activated 88 and deactivated MidFG regions (P1: 98.1%; N = 51/52; P2: 86.6%; N = 110/127)'. Is the face selectivity in P1 an increase in response to faces and P2 a reduction in response to faces or in both it's an increase in response to faces

(1) Additional methods<br /> (a) it is unclear if the SSVEP analyses of neural responses were done on the spikes or the raw electrical signal. If the former, how is the SSVEP frequency analysis done on discrete data like action potentials?<br /> (b) it is unclear why the onset time was shifted by 33ms; one can measure the phase of the response relative to the cycle onset and use that to estimate the delay between the onset of a stimulus and the onset of the response. Adding phase information will be useful.

(2) Interpretation of suppression:

The SSVEP paradigm alternates between 2 conditions: faces and objects and has no baseline; In other words, responses to faces are measured relative to the baseline response to objects so that any region that contains neurons that have a lower firing rate to faces than objects is bound to show a lower response in the SSVEP signal. Therefore, because the experiment does not have a true baseline (e.g. blank screen, with no visual stimulation) this experimental design cannot distinguish between lower firing rate to faces vs suppression of response to faces.<br /> The strongest evidence put forward for suppression is the response of non-visual neurons that was also reduced when patients looked at faces, but since these are non-visual neurons, it is unclear how to interpret the responses to faces.

Reviewer #1 (Public review):

Summary:

This study demonstrates that strip cropping enhances the taxonomic diversity of ground beetles across organically-managed crop systems in the Netherlands. In particular, strip cropping supported 15% more ground beetle species and 30% more individuals compared to monocultures.

Strengths:

A well-written study with well-analyzed data of a complex design. The data could have been analyzed differently e.g. by not pooling samples, but there are pros and cons for each type of analysis and I am convinced this will not affect the main findings. A strong point is that data were collected for 4 years. This is especially strong as most data on biodiversity in cropping systems are only collected for one or two seasons. Another strong point is that several crops were included.

Weaknesses:

This study focused on the biodiversity of ground beetles and did not examine crop productivity. Therefore, I disagree with the claim that this study demonstrates biodiversity enhancement without compromising yield. The authors should present results on yield or, at the very least, provide a stronger justification for this statement.

Reviewer #2 (Public review):

Summary:

The authors aimed to investigate the effects of organic strip cropping on carabid richness and density as well as on crop yields. They find on average higher carabid richness and density in strip cropping and organic farming, but not in all cases.

Strengths:

Based on highly resolved species-level carabid data, the authors present estimates for many different crop types, some of them rarely studied, at the same time. The authors did a great job investigating different aspects of the assemblages (although some questions remain concerning the analyses) and they present their results in a visually pleasing and intuitive way.

Weaknesses:

The authors used data from four different strip cropping experiments and there is no real replication in space as all of these differed in many aspects (different crops, different areas between years, different combinations, design of the strip cropping (orientation and width), sampling effort and sample sizes of beetles (differing more than 35 fold between sites; L 100f); for more differences see L 237ff). The reader gets the impression that the authors stitched data from various places together that were not made to fit together. This may not be a problem per se but it surely limits the strength of the data as results for various crops may only be based on small samples from one or two sites (it is generally unclear how many samples were used for each crop/crop combination).

One of my major concerns is that it is completely unclear where carabids were collected. As some strips were 3m wide, some others were 6m and the monoculture plots large, it can be expected that carabids were collected at different distances from the plot edge. This alone, however, was conclusively shown to affect carabid assemblages dramatically and could easily outweigh the differences shown here if not accounted for in the models (see e.g. Boetzl et al. (2024) or Knapp et al. (2019) among many other studies on within field-distributions of carabids).

The authors hint at a related but somewhat different problem in L 137ff - carabid assemblages sampled in strips were sampled in closer proximity to each other than assemblages in monoculture fields which is very likely a problem. The authors did not check whether their results are spatially autocorrelated and this shortcoming is hard to account for as it would have required a much bigger, spatially replicated design in which distances are maintained from the beginning. This limitation needs to be stated more clearly in the manuscript.

Similarly, we know that carabid richness and density depend strongly on crop type (see e.g. Toivonen et al. (2022)) which could have biased results if the design is not balanced (this information is missing but it seems to be the case, see e.g. Celeriac in Almere in 2022).

A more basic problem is that the reader neither learns where traps were located, how missing traps were treated for analyses how many samples there were per crop or crop combination (in a simple way, not through Table S7 - there has to have been a logic in each of these field trials) or why there are differences in the number of samples from the same location and year (see Table S7). This information needs to be added to the methods section.

As carabid assemblages undergo rapid phenological changes across the year, assemblages that are collected at different phenological points within and across years cannot easily be compared. The authors would need to standardize for this and make sure that the assemblages they analyze are comparable prior to analyses. Otherwise, I see the possibility that the reported differences might simply be biased by phenology.

Surrounding landscape structure is known to affect carabid richness and density and could thus also bias observed differences between treatments at the same locations (lower overall richness => lower differences between treatments). Landscape structure has not been taken into account in any way.

In the statistical analyses, it is unclear whether the authors used estimated marginal means (as they should) - this needs to be clarified.

In addition, and as mentioned by Dr. Rasmann in the previous round (comment 1), the manuscript, in its current form, still suffers from simplified generalizations that 'oversell' the impact of the study and should be avoided. The authors restricted their analyses to ground beetles and based their conclusions on a design with many 'heterogeneities' - they should not draw conclusions for farmland biodiversity but stick to their system and report what they found. Although I understand the authors have previously stated that this is 'not practically feasible', the reason for this comment is simply to say that the authors should not oversell their findings.

Reviewer #3 (Public review):

Summary:

In this paper, the authors made a sincere effort to show the effects of strip cropping, a technique of alternating crops in small strips of several meters wide, on ground beetle diversity. They state that strip cropping can be a useful tool for bending the curve of biodiversity loss in agricultural systems as strip cropping shows a relative increase in species diversity (i.e. abundance and species richness) of the ground beetle communities compared to monocultures. Moreover, strip cropping has the added advantage of not having to compromise on agricultural yields.

Strengths:

The article is well written; it has an easily readable tone of voice without too much jargon or overly complicated sentence structure. Moreover, as far as reviewing the models in depth without raw data and R scripts allows, the statistical work done by the authors looks good. They have well thought out how to handle heterogenous, yet spatially and temporarily correlated field data. The models applied and the model checks performed are appropriate for the data at hand. Combining RDA and PCA axes together is a nice touch.

Weaknesses:

The evidence for strip cropping bringing added value for biodiversity is mixed at best. Yes, there is an increase in relative abundance and species richness at the field level, but it is not convincingly shown this difference is robust or can be linked to clear structural and hypothesised advantages of the strip cropping system. The same results could have been used to conclude that there are only very limited signs of real added value of strip cropping compared to monocultures.

There are a number of reasons for this:

(1) Significant differences disappear at crop level, as the authors themselves clearly acknowledge, meaning that there are no differences between pairs of similar crops in the strip cropping fields and their respective monoculture. This would mean the strips effectively function as "mini-monocultures". The significant relative differences at the field level could be an artifact of aggregation instead of structural differences between strip cropping and monocultures; with enough data points things tend to get significant despite large variance. This should have been elaborated further upon by the authors with additional analyses, designed to find out where differences originate and what it tells about the functioning of the system. Or it should have provided ample reason for cautioning in drawing conclusions about the supposed effectiveness of strip cropping based on these findings.

(2) The authors report percentages calculated as relative change of species richness and abundance in strip cropping compared to monocultures after rarefaction. This is in itself correct, however, it can be rather tricky to interpret because the perspective on actual species richness and abundance in the fields and treatments is completely lost; the reported percentages are dimensionless. The authors could have provided the average cumulative number of species and abundance after rarefaction. Also, range and/or standard error would have been useful to provide information as to the scale of differences between treatments. This could provide a new perspective on the magnitude of differences between the two treatments which a dimensionless percentage cannot.

(3) The authors appear to not have modelled the abundance of any of the dominant ground beetle species themselves. Therefore it becomes impossible to assess which important species are responsible (if any) for the differences found in activity density between stripcropping and monocultures and the possible life history traits related reasons for the differences, or lack thereof, that are found. A big advantage of using ground beetles is that many life history traits are well studied and these should be used whenever there is reason, as there clearly is in this case. Moreover, it is unclear which species are responsible for the difference in species richness found at the field level. Are these dominant species or singletons? Do the strip cropping fields contain species that are absent in the monoculture fields and are not the cause of random variation or sampling? Unfortunately, the authors do not report on any of these details of the communities that were found, which makes the results much less robust.

(4) In the discussion they conclude that there is only a limited amount of interstrip movement by ground beetles. Otherwise, the results of the crop-level statistical tests would have shown significant deviation from corresponding monocultures. This is a clear indication that the strips function more like mini-monocultures instead of being more than the sum of its parts.

(5) The RDA results show a modelled variable of differences in community composition between strip cropping and monoculture. Percentages of explained variation of the first RDA axis are extremely low, and even then, the effect of location and/or year appear to peak through (Figure S3), even though these are not part of the modelling. Moreover, there is no indication of clustering of strip cropping on the RDA axis, or in fact on the first principal component axis in the larger RDA models. This means the explanatory power of different treatments is also extremely low. The crop level RDA's show some clustering, but hardly any consistent pattern in either communities of crops or species correlations, indicating that differences between strip cropping and monocultures are very small.

Furthermore, there are a number of additional weaknesses in the paper that should be addressed:

The introduction lacks focus on the issues at hand. Too much space is taken up by facts on insect decline and land sharing vs. land sparing and not enough attention is spent on the scientific discussion underlying the statements made about crop diversification as a restoration strategy. They are simply stated as facts or as hypotheses with many references that are not mentioned or linked to in the text. An explicit link to the results found in the large number of references should be provided.

The mechanistic understanding of strip cropping is what is at stake here. Does strip cropping behave similarly to intercropping, a technique that has been proven to be beneficial to biodiversity because of added effects due to increased resource efficiency and greater plant species richness? This should be the main testing point and agenda of strip cropping. Do the biodiversity benefits that have been shown for intercropping also work in strip cropping fields? The ground beetles are one way to test this. Hypotheses should originate from this and should be stated clearly and mechanistically.

One could question how useful indicator species analysis (ISA) is for a study in which predominantly highly eurytopic species are found. These are by definition uncritical of their habitat. Is there any mechanistic hypothesis underlying a suspected difference to be found in preferences for either strip cropping or monocultures of the species that were expected to be caught? In other words, did the authors have any a priori reasons to suspect differences, or has this been an exploratory exercise from which unexplained significant results should be used with great caution?

However, setting these objections aside there are in fact significant results with strong species associations both with monocultures and strip cropping. Unfortunately, the authors do not dig deeper into the patterns found a posteriori either. Why would some species associate so strongly with strip cropping? Do these species show a pattern of pitfall catches that deviate from other species, in that they are found in a wide range of strips with different crops in one strip cropping field and therefore may benefit from an increased abundance of food or shelter? Also, why would so many species associate with monocultures? Is this in any way logical? Could it be an artifact of the data instead of a meaningful pattern? Unfortunately, the authors do not progress along these lines in the methods and discussion at all.

A second question raised in the introduction is whether the arable fields that form part of this study contain rare species. Unfortunately, the authors do not elaborate further on this. Do they expect rare species to be more prevalent in the strip cropping fields? Why? Has it been shown elsewhere that intercropping provides room for additional rare species?

Considering the implications the results of this research can have on the wider discussion of bending the curve and the effects of agroecological measures, bold claims should be made with extreme restraint and be based on extensive proof and robust findings. I am not convinced by the evidence provided in this article that the claim made by the authors that strip cropping is a useful tool for bending the curve of biodiversity loss is warranted.

Reviewer #1 (Public review):

Summary:

Goal: Find downstream targets of cmk-1 phosphorylation, identify one that also seems to act in thermosensory habituation, test for genetic interactions between cmk-1 and this gene, and assess where these genes are acting in the thermosensory circuit during thermosensory habituation.

Methods: Two in vitro analyses of cmk-1 phosphorylation of C. elegans proteins. Thermosensory habituation of cmk-1 and tax-6 mutants and double mutants was assessed by measuring the rate of heat-evoked reversals (reversal probability) of C. elegans before and after 20s ISI repeated heat pulses over 60 minutes.

Conclusions: cmk-1 and tax-6 act in separate habituation processes, primarily in AFD, that interact complexly, but both serve to habituate the thermosensory reversal response. They found that cmk-1 primarily acts in AFD and tax-6 primarily acts in RIM (and FLP for naïve responses). They also identified hundreds of potential cmk-1 phosphorylation substrates in vitro.

Strengths:

The effect size in the genetic data is quite strong and a large number of genetic interaction experiments between cmk-1 and tax-1 demonstrate a complex interaction.

Weaknesses:

The major concern about this manuscript is the assumption that the process they are observing is habituation. The two previously cited papers using this (or a very similar) protocol, Lia and Glauser 2020 and Jordan and Glauser 2023, both use the word 'adaptation' to describe the observed behavioral decrement. Jordan and Glauser 2023 use the words 'habituation' or 'habituation-like' 10 times, however, they use 'adaptation' over 100 times. It is critical to distinguish habituation from sensory adaptation (or fatigue) in this thermal reversal protocol. These processes are often confused/conflated, however, they are very different; sensory adaptation is a process that decreases how much the nervous system is activated by a repeated stimulus, therefore it can even occur outside of the nervous system. Habituation is a learning process where the nervous system responds less to a repeated stimulus, despite (at least part of the nervous system) the nervous system still being similarly activated by the stimulus. Habituation is considered an attentional process, while adaptation is due to the fatigue of sensory transduction machinery. Control experiments such as tests for dishabituation (where the application of a different stimulus causes recovery of the decremented response) or rate of spontaneous recovery (more rapid recovery after short inter-stimulus intervals) are required to determine if habituation or sensory adaptation are occurring. These experiments will allow the results to be interpreted with clarity, without them, it isn't actually clear what biological process is actually being studied.

While the discrepancy between the in vitro phosphorylation experiments and the in silico predictions was discussed, the substantial discrepancy (over 85% of the substrates in the smaller in vitro dataset were not identified in the larger dataset) between the two different in vitro datasets was not discussed. This is surprising, as these approaches were quite similar, and it may indicate a measure of unreliability in the in vitro datasets (or high false negative rates). Additionally, the rationale for, and distinction between, the two separate in vitro experiments is not made clear.

Line 207: After reporting that both tax-6 and cnb-1 mutants have high spontaneous reversals, it is not made clear why cnb-1 is not further explored in the paper. Additionally, this spontaneous reversal data should be in a supplementary figure.

Figure 3 -S1: This model doesn't explain why the cmk-1(gf) group and the cmk-1(gf) +cyclo A group cause enhanced response decrement (presumably by reducing the inhibition by tax-6) but the +cyclo A group (inhibited tax-6) showed weaker response decrement, as here there is even further weakened inhibition of tax-6 on this process. Also, the cmk-1(lf) +cyclo A group is labeled as constitutive habituation, however, this doesn't appear to be the case in Figure 3 (seems like a similar initial level and response decrement phenotype to wildtype).

More discussion of the significance of the sites of cmk-1 and tax-6 function in the neural circuit should take place. Additionally, incorporating the suspected loci of cmk-1 and tax-6 in the neural circuit into the model would be interesting (using proper hypothetical language). For example, as it seems like AFD is not required for the naïve reversal response but just its reduction, cmk-1 activity in AFD might be generating inhibition of the reversal response by AFD. It certainly would be understandable if this isn't workable, given extrasynaptic signaling and other unknowns, but it potentially could also be helpful in generating a working model for these complex interactions. For example, cmk-1 induces AIZ inhibition of AVA (AIZ is electrically coupled to AFD), and tax-6 reduces RIM activation of AVA (these neurons are also electrically coupled according to the diagram). RIM is also a neuropeptide-rich neuron, so this could allow it to interact with the cmk-1-related process(es) in AFD. Some discussion of possibilities like this could be informative.

Provide an explanation for why some of the experiments in Figure 4 have such a high N, compared to other experiments.

Because the loss of function and gain of function mutations in cmk-1 have a similar effect, it is likely that this thermosensory plasticity phenotype is sensitive to levels of cmk-1 activity. Therefore, it is not surprising that the cmk-1 promoter failed to rescue very well as these plasmid-driven rescues often result in overexpression. Given this and that the cmk-1p rescue itself was so modest, these rescue experiments are not entirely convincing (and very hard to interpret; for example, is the AFD rescue or the ASER rescue more complete? The ASER one is actually closer to the cmk-1p rescue). Given the sensitivity to cmk-1 activity levels, a degradation strategy would be more likely to deliver clear results (or perhaps even the overactivation approach used for tax-6).

Reviewer #2 (Public review):

Summary:

The reduction in a response to a specific stimulus after repeated exposures is called habituation. Alterations in habituation to noxious stimuli are associated with chronic pain in humans, however, the underlying molecular mechanisms involved are not clear. This study uses the nematode C. elegans to study genes and mechanisms that underlie habituation to a form of noxious stimuli based on heat, termed thermo-noxious stimuli. The authors previously showed that the Calcium/Calmodulin-dependent protein kinase (CMK-1) regulates thermo-nociceptive habituation in the nematode C. elegans. Although CMK-1 is a kinase with many known substrates, the downstream targets relevant for thermo-nociceptive habituation are not known. In this study, the authors use two different kinase screens to identify phosphorylation targets of CMK-1. One of the targets they identify is Calcineurin (TAX-6). The authors show that CMK-1 phosphorylates a regulatory domain of Calcineurin at a highly conserved site (S443). In a series of elegant experiments, the authors use genetic and pharmacological approaches to increase or decrease CMK-1 and Calcineurin signaling to study their effects on thermo-nociceptive habituation in C. elegans. They also combine these various approaches to study the interactions between these two signaling proteins. The authors use specific promoters to determine in which neurons CMK-1 and Calcineurin function to regulate thermo-nociceptive habituation. The authors propose a model based on their findings illustrating that CMK-1 and Calcineurin act mostly in different neurons to antagonistically regulate habituation to thermo-nociceptive stimuli in a complex manner.

Strengths:

(1) Given the conservation of habituation across phylogeny, identifying genes and mechanisms that underlie nociceptive habituation in C. elegans may be relevant for understanding chronic pain in humans.

(2) The identification of canonical CaM Kinase phosphorylation motifs in the substrates identified in the CMK-1 substrate screen validates the screen.

(3) The use of loss and gain of function approaches to study the effects of CMK-1 and Calcineurin on thermo-nociceptive responses and habituation is elegant.

(4) The ability to determine the cellular place of action of CMK-1 and Calcineurin using neuron-specific promoters in the nematode is a clear strength of the genetic model system.

Weaknesses:

(1) The manuscript begins by identifying Calcineurin as a direct substrate of CMK-1 but ends by showing that CMK-1 and Calcineurin mostly act in different neurons to regulate nociceptive habituation which disrupts the logical flow of the manuscript.

(2) The physiological relevance of CMK-1 phosphorylation of Calcineurin is not clear.

(3) It is not clear if Calcineurin is already a known substrate of CaM Kinases in other systems or if this finding is new.

Reviewer #1 (Public review):

Summary:

This study presents convincing findings that oligodendrocytes play a regulatory role in spontaneous neural activity synchronisation during early postnatal development, with implications for adult brain function. Utilising targeted genetic approaches, the authors demonstrate how oligodendrocyte depletion impacts Purkinje cell activity and behaviours dependent on cerebellar function. Delayed myelination during critical developmental windows is linked to persistent alterations in neural circuit function, underscoring the lasting impact of oligodendrocyte activity.

Strengths:

(1) The research leverages the anatomically distinct olivocerebellar circuit, a well-characterized system with known developmental timelines and inputs, strengthening the link between oligodendrocyte function and neural synchronization.

(2) Functional assessments, supported by behavioral tests, validate the findings of in vivo calcium imaging, enhancing the study's credibility.

(3) Extending the study to assess the long-term effects of early-life myelination disruptions adds depth to the implications for both circuit function and behavior.

Weaknesses:

(1) The study would benefit from a closer analysis of myelination during the periods when synchrony is recorded. Direct correlations between myelination and synchronized activity would substantiate the mechanistic link and clarify if observed behavioral deficits stem from altered myelination timing.

(2) Although the study focuses on Purkinje cells in the cerebellum, neural synchrony typically involves cross-regional interactions. Expanding the discussion on how localized Purkinje synchrony affects broader behaviors - such as anxiety, motor function, and sociality - would enhance the findings' functional significance.

(3) The authors discuss the possibility of oligodendrocyte-mediated synapse elimination as a possible mechanism behind their findings, drawing from relevant recent literature on oligodendrocyte precursor cells. However, there are no data presented supporting this assumption. The authors should explain why they think the mechanism behind their observation extends beyond the contribution of myelination or remove this point from the discussion entirely.

(4) It would be valuable to investigate the secondary effects of oligodendrocyte depletion on other glial cells, particularly astrocytes or microglia, which could influence long-term behavioral outcomes. Identifying whether the lasting effects stem from developmental oligodendrocyte function alone or also involve myelination could deepen the study's insights.

(5) The authors should explore the use of different methods to disturb myelin production for a longer time, in order to further determine if the observed effects are transient or if they could have longer-lasting effects.

(6) Throughout the paper, there are concerns about statistical analyses, particularly on the use of the Mann-Whitney test or using fields of view as biological replicates.

Reviewer #2 (Public review):

Summary:

In this manuscript, the authors use genetic tools to ablate oligodendrocytes in the cerebellum during postnatal development. They show that the oligodendrocyte numbers return to normal post-weaning. Yet, the loss of oligodendrocytes during development seems to result in decreased synchrony of calcium transients in Purkinje neurons across the cerebellum. Further, there were deficits in social behaviors and motor coordination. Finally, they suppress activity in a subset of climbing fibers to show that it results in similar phenotypes in the calcium signaling and behavioral assays. They conclude that the behavioral deficits in the oligodendrocyte ablation experiments must result from loss of synchrony.

Strengths:

Use of genetic tools to induce perturbations in a spatiotemporally specific manner.

Weaknesses:

The main weakness in this manuscript is the lack of a cohesive causal connection between the experimental manipulation performed and the phenotypes observed. Though they have taken great care to induce oligodendrocyte loss specifically in the cerebellum and at specific time windows, the subsequent experiments do not address specific questions regarding the effect of this manipulation. Calcium transients in Purkinje neurons are caused to a large extent by climbing fibers, but there is evidence for simple spikes to also underlie the dF/F signatures (Ramirez and Stell, Cell Reports, 2016). Also, it is erroneous to categorize these calcium signals as signatures of "spontaneous activity" of Purkinje neurons as they can have dual origins. Further, the effect of developmental oligodendrocyte ablation on the cerebellum has been previously reported by Mathis et al., Development, 2003. They report very severe effects such as the loss of molecular layer interneurons, stunted Purkinje neuron dendritic arbors, abnormal foliations, etc. In this context, it is hardly surprising that one would observe a reduction of synchrony in Purkinje neurons (perhaps due to loss of synaptic contacts, not only from CFs but also from granule cells). The last experiment with the expression of Kir2.1 in the inferior olive is hardly convincing. In summary, while the authors used a specific tool to probe the role of developmental oligodendrocytes in cerebellar physiology and function, they failed to answer specific questions regarding this role, which they could have done with more fine-grained experimental analysis.

Reviewer #1 (Public review):

Summary:

The paper by Lee and Ouellette explores the role of cyclic-d-AMP in chlamydial developmental progression. The manuscript uses a collection of different recombinant plasmids to up- and down-regulate cdAMP production, and then uses classical molecular and microbiological approaches to examine the effects of expression induction in each of the transformed strains.

Strengths:

This laboratory is a leader in the use of molecular genetic manipulation in Chlamydia trachomatis and their efforts to make such efforts mainstream is commendable. Overall, the model described and defended by these investigators is thorough and significant.

Weaknesses:

The biggest weakness in the document is their reliance on quantitative data that is statistically not significant, in the interpretation of results. These challenges can be addressed in a revision by the authors.

Reviewer #2 (Public review):

Summary:

This manuscript describes the role of the production of c-di-AMP on the chlamydial developmental cycle. Chlamydia are obligate intracellular bacterial pathogens that rely on eukaryotic host cells for growth. The chlamydial life cycle depends on a cell form developmental cycle that produces phenotypically distinct cell forms with specific roles during the infectious cycle. The RB cell form replicates amplifying chlamydia numbers while the EB cell form mediates entry into new host cells disseminating the infection to new hosts. Regulation of cell form development is a critical question in chlamydia biology and pathogenesis. Chlamydia must balance amplification (RB numbers) and dissemination (EB numbers) to maximize survival in its infection niche. The main findings In this manuscript show that overexpression of the dacA-ybbR operon results in increased production of c-di-AMP and early expression of the transitionary gene hctA and late gene omcB. The authors also knocked down the expression of the dacA-ybbR operon and reported a reduction in the expression of both hctA and omcB. The authors conclude with a model suggesting the amount of c-di-AMP determines the fate of the RB, continued replication, or EB conversion. Overall, this is a very intriguing study with important implications however the data is very preliminary and the model is very rudimentary and is not well supported by the data.

Describing the significance of the findings:

The findings are important and point to very exciting new avenues to explore the important questions in chlamydial cell form development. The authors present a model that is not quantified and does not match the data well.

Describing the strength of evidence:

The evidence presented is incomplete. The authors do a nice job of showing that overexpression of the dacA-ybbR operon increases c-di-AMP and that knockdown or overexpression of the catalytically dead DacA protein decreases the c-di-AMP levels. However, the effects on the developmental cycle and how they fit the proposed model are less well supported.

dacA-ybbR ectopic expression:

For the dacA-ybbR ectopic expression experiments they show that hctA is induced early but there is no significant change in OmcB gene expression. This is problematic as when RBs are treated with Pen (this paper) and (DOI 10.1128/MSYSTEMS.00689-20) hctA is expressed in the aberrant cell forms but these forms do not go on to express the late genes suggesting stress events can result in changes in the developmental expression kinetic profile. The RNA-seq data are a little reassuring as many of the EB/Late genes were shown to be upregulated by dacA-ybbR ectopic expression in this assay.

The authors also demonstrate that this ectopic expression reduces the overall growth rate but produces EBs earlier in the cycle but overall fewer EBs late in the cycle. This observation matches their model well as when RBs convert early there is less amplification of cell numbers.

dacA knockdown and dacA(mut)

The authors showed that dacA knockdown and ectopic expression of the dacA mutant both reduced the amount of c-di-AMP. The authors show that for both of these conditions, hctA and omcB expression is reduced at 24 hpi. This was also partially supported by the RNA-seq data for the dacA knockdown as many of the late genes were downregulated. However, a shift to an increase in RB-only genes was not readily evident. This is maybe not surprising as the chlamydial inclusion would just have an increase in RB forms and changes in cell form ratios would need more time points.

Interestingly, the overall growth rate appears to differ in these two conditions, growth is unaffected by dacA knockdown but is significantly affected by the expression of the mutant. In both cases, EB production is repressed. The overall model they present does not support this data well as if RBs were blocked from converting into EBs then the growth rate should increase as the RB cell form replicates while the EB cell form does not. This should shift the population to replicating cells.

Overall this is a very intriguing finding that will require more gene expression data, phenotypic characterization of cell forms, and better quantitative models to fully interpret these findings.

Reviewer #1 (Public review):

Summary:

In this manuscript, the authors Eapen et al. investigated the peptide inhibitors of Cdc20. They applied a rational design approach, substituting residues found in the D-box consensus sequences to better align the peptides with the Cdc20-degron interface. In the process, the authors designed and tested a series of more potent binders, including ones that contain unnatural amino acids, and verified binding modes by elucidating the Cdc-20-peptide structures. The authors further showed that these peptides can engage with Cdc20 in the cellular context, and can inhibit APC/CCdc20 ubiquitination activity. Finally, the authors demonstrated that these peptides could be used as portable degron motifs that drive the degradation of a fused fluorescent protein.

Strengths:

This manuscript is clear and straightforward to follow. The investigation of different peptide variations was comprehensive and well-executed. This work provided the groundwork for the development of peptide drug modalities to inhibit degradation or apply peptides as portable motifs to achieve targeted degradation. Both of which are impactful.

Weaknesses:

A few minor comments:

(1) In my opinion, more attention to the solubility issue needs to be discussed and/or tested. On page 10, what is the solubility of D2 before a modification was made? The authors mentioned that position 2 is likely solvent exposed, it is not immediately clear to me why the mutation made was from one hydrophobic residue to another. What was the level of improvement in solubility? Are there any affinity data associated with the peptide that differ with D2 only at position 2?

(2) I'm not entirely convinced that the D19 density not observed in the crystal structure was due to crystal packing. This peptide is peculiar as it also did not induce any thermal stabilization of Cdc20 in the cellular thermal shift assay. Perhaps the binding of this peptide could be investigated in more detail (i.e., NMR?) Or at least more explanation could be provided.

Reviewer #2 (Public review):

Summary:

The authors took a well-characterised (partly by them), important E3 ligase, in the anaphase-promoting complex, and decided to design peptide inhibitors for it based on one of the known interacting motifs (called D-box) from its substrates. They incorporate unnatural amino acids to better occupy the interaction site, improve the binding affinity, and lay foundations for future therapeutics - maybe combining their findings with additional target sites.

Strengths:

The paper is mostly strengths - a logical progression of experiments, very well explained and carried out to a high standard. The authors use a carefully chosen variety of techniques (including X-ray crystallography, multiple binding analyses, and ubiquitination assays) to verify their findings - and they impressively achieve their goals by honing in on tight-binders.

Weaknesses:

Some things are not explained fully and it would be useful to have some clarification. Why did the authors decide to model their inhibitors on the D-box motif and not the other two SLiMs that they describe? What exactly do they mean when they say their 'observation is consistent with the idea that high-affinity binding at degron binding sites on APC/C, such as in the case of the yeast 'pseudo-substrate' inhibitor Acm1, acts to impede polyubiquitination of the bound protein'? It's an interesting thing to think about, and probably the paper they cite explains it more but I would like to know without having to find that other paper.

Reviewer #3 (Public review):

Summary:

Eapen and coworkers use a rational design approach to generate new peptide-inspired ligands at the D-box interface of cdc20. These new peptides serve as new starting points for blocking APC/C in the context of cancer, as well as manipulating APC/C for targeted protein degradation therapeutic approaches.

Strengths:

The characterization of new peptide-like ligands is generally solid and multifaceted, including binding assays, thermal stability enhancement in vitro and in cells, X-ray crystallography, and degradation assays.

Weaknesses:

One important finding of the study is that the strongest binders did not correlate with the fastest degradation in a cellular assay, but explanations for this behavior were not supported experimentally. Some minor issues regarding experimental replicates and details were also noted.

Reviewer #1 (Public review):

This study investigates alterations in the autophagic-lysosomal pathway in the Q175 HD knock-in model crossed with the TRGL autophagy reporter mouse. The findings provide valuable insights into autophagy dynamics in HD and the potential therapeutic benefits of modulating this pathway. The study suggests that autophagy stimulation may offer therapeutic benefits in the early stages of HD progression, with mTOR inhibition showing promise in ameliorating lysosomal pathology and reducing mutant huntingtin accumulation.

However, the data raises concerns regarding the strength of the evidence. The observed changes in autophagic markers, such as autolysosome and lysosome numbers, are relatively modest, and the Western blot results do not fully match the quantitative results. These discrepancies highlight the need for further validation and more pronounced effects to strengthen the conclusions. While the study suggests the potential of autophagy regulation as a long-term therapeutic strategy, additional experiments and more reliable data are necessary to confirm the broader applicability of the TRGL/Q175 mouse model.

Furthermore, the 2004 publication by Ravikumar et al. demonstrated that inhibition of mTOR by rapamycin or the rapamycin ester CCI-779 induces autophagy and reduces the toxicity of polyglutamine expansions in fly and mouse models of Huntington's disease. mTOR is a key regulator of autophagy, and its inhibition has been explored as a therapeutic strategy for various neurodegenerative diseases, including HD. Studies suggest that inhibiting mTOR enhances autophagy, leading to the clearance of mHTT aggregates. Given that dysfunction of the autophagic-lysosomal pathway and lysosomal function in HD is already well-established, and that mTOR inhibition as a therapeutic approach for HD is also known, this study does not present entirely novel findings.

Major Concerns:

(1) In Figure 3A1 and A2, delayed and/or deficient acidification of AL causes deficits in the reformation of LY to replenish the LY pool. However, in Figure S2D, there is no difference in AL formation or substrate degradation, as shown by the Western blotting results for CTSD and CTSB. How can these discrepancies be explained?

(2) The results demonstrate that in the brain sections of 17-month-old TRGL/Q175 mice, there was an increase in the number of acidic autolysosomes (AL), including poorly acidified autolysosomes (pa-AL), alongside a decrease in lysosome (LY) numbers. These AL/pa-AL changes were not significant in 2-month-old or 7-month-old TRGL/Q175 mice, where only a reduction in lysosome numbers was observed. This indicates that these changes, representing damage to the autophagy-lysosome pathway (ALP), manifest only at later stages of the disease. Considering that the ALP is affected predominantly in the advanced stages of the disease (e.g., at 17 months), why were 6-month-old TRGL/Q175 mice selected for oral mTORi INK treatment, and why was the treatment duration restricted to just 3 weeks?

(3) Is the extent of motor dysfunction in TRGL/Q175 mice comparable to that in Q175 mice? Does the administration of mTORi INK improve these symptoms?

(4) Why is eGFP expression not visible in Fig. 6A in TRGL-Veh mice? Additionally, why do normal (non-poly-Q) mice have fewer lysosomes (LY) than TRGL/Q175-INK mice? IHC results also show that CTSD levels are lower in TRGL mice compared to TRGL/Q175-INK mice. Does this suggest lysosome dysfunction in TRGL-Veh mice?

(5) In Figure 5A, the phosphorylation of ATG14 (S29) shows minimal differences in Western blotting, which appears inconsistent with the quantitative results. A similar issue is observed in the quantification of Endo-LC3.

(6) In Figure S2A and Figure S2B, 17-month-old TRGL/Q175 mice show a decrease in p-p70S6K and the p-ULK1/ULK1 ratio, but no changes are observed in autophagy-related markers. Do these results indicate only a slight change in autophagy at this stage in TRGL/Q175 mice? Since the mTOR pathway regulates multiple cellular mechanisms, could mTOR also influence other processes? Is it possible that additional mechanisms are involved?

Reviewer #2 (Public review):

Summary:

In this manuscript, the authors have explored the beneficial effect of autophagy upregulation in the context of HD pathology in a disease stage-specific manner. The authors have observed functional autophagy lysosomal pathway (ALP) and its machineries at the early stage in the HD mouse model, whereas impairment of ALP has been documented at the later stages of the disease progression. Eventually, the authors took advantage of the operational ALP pathway at the early stage of HD pathology, in order to upregulate ALP and autophagy flux by inhibiting mTORC1 in vivo, which ultimately reverted back to multiple ALP-related abnormalities and phenotypes. Therefore, this manuscript is a promising effort to shed light on the therapeutic interventions with which HD pathology can be treated at the patient level in the future.

Strengths:

The study has shown the alteration of ALP in the HD mouse model in a very detailed manner. Such stage-dependent in vivo study will be informative and has not been done before. Also, this research provides possible therapeutic interventions for patients in the future.

Weaknesses:

Some constructive comments and suggestions in order to reflect the key aspects and concepts better in the manuscript :

(1) The authors have observed lysosome number alteration in a temporally regulated disease stage-specific manner. In this scenario investigation of regulation, localization, and level of TFEB, the transcription factor required for lysosome biogenesis, would be interesting and informative.

(2) For the general scientific community better clarification of the short forms will be useful. For example, in line 97, page 4, AP full form would be useful. Also 'metabolized via autophagy' can be replaced by 'degraded via autophagy'.

(3) The nuclear vs cytosolic localization of HTT aggregates shown in Figure 2, are very interesting. The increase in cytosolic HTT aggregate formation at 10 months compared to 6 months probably suggests spatio-temporal regulation of aggregate formation. The authors could comment in a more elaborate manner, on the reason and impact of this kind of regulation of aggregate formation in the context of HD pathology.

(4) In this manuscript, the authors have convincingly shown that mTOR inhibition is inducing autophagy in the HD mouse model in vivo. On the other hand, mTOR inhibition would also reduce overall cellular protein translation. This aspect of mTOR inhibition can also potentially contribute to the alleviation of disease phenotype and disease symptoms by reducing protein overload in HD pathology. The authors' comments regarding this aspect would be appreciated.

(5) The authors have shown nuclear inclusion formation and aggregation of mHTT and also commented on its potential removal with the UPS system (proteasomal degradation) in vivo. As there is also a reciprocal relationship present between autophagy and proteasomal machineries, upon upregulation of autophagy machinery by mTOR inhibition proteasomal activity may decrease. How nuclear proteasomal activity increases to tackle nuclear mHTT IBs, would be interesting to understand in the context of HD pathology. Comments from the authors in this aspect would clarify the role of multiple degradation pathways in handling mutant HTT protein in HD pathology.

(6) For the treatment of neurodegenerative disorders taking the temporal regulation into consideration is extremely important, as that will determine the success rate of the treatments in patients. The authors in this manuscript have clearly discussed this scenario. However, for neurodegenerative disordered patients, in most cases, the symptom manifestation is a late onset scenario. In that case, it will be complicated to initiate an early treatment regime in HD patients. If the authors can comment on and discuss the practicality of the early treatment regime for therapeutic purposes that would be impactful.

Reviewer #2 (Public review):

Summary:

In their manuscript, Quian and colleagues identified a novel mechanisms by which Pseudomonas control inflammatory responses upon inflammasome activation. They identified a caspase-11 substrates (VgrG2b) which, upon cleavage, binds and inhibit the NLRP3 to reduce the production of pro-inflammatory cytokines. This is a unique mechanism that allow for the tailoring of the innate immune response upon bacterial recognition.

Strengths:

The authors are presenting here a novel conceptual framework in host-pathogen interactions. Their work is supported by a range of approaches (biochemical, cellular immunology, microbiology, animal models) and their conclusions are supported by multiple independent evidences. The work is likely to have an important impact in the innate immunity field and host-pathogen interactions field and may guide the development of novel inhibitors.

Weaknesses:

Although quite exhaustive, a few of the authors conclusions are not fully supported (e.g, caspase-11 directly cleaving VgrG2b, the unique affinity of VgrG2b-C for NLRP3) and would require complementary approaches to validate their findings fully. This is minimal.

Comments on revisions:

I command the authors's effort to address my comments. They have addressed all my concerns.

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:

The manuscript presents a short report investigating mismatch responses in the auditory cortex, following previous studies focused on visual cortex. By correlating mouse locomotion speed with acoustic feedback levels, the authors demonstrate excitatory responses in a subset of neurons to halts in expected acoustic feedback. They show a lack of responses to mismatch in he visual modality. A subset of neurons show enhanced mismatch responses when both auditory and visual modalities are coupled to the animal's locomotion.<br /> While the study is well-designed and addresses a timely question, several concerns exist regarding the quantification of animal behavior, potential alternative explanations for recorded signals, correlation between excitatory responses and animal velocity, discrepancies in reported values, and clarity regarding the identity of certain neurons.

Strengths:

(1) Well-designed study addressing a timely question in the field.<br /> (2) Successful transition from previous work focused on visual cortex to auditory cortex, demonstrating generic principles in mismatch responses.<br /> (3) Correlation between mouse locomotion speed and acoustic feedback levels provides evidence for prediction signal in the auditory cortex.<br /> (4) Coupling of visual and auditory feedback show putative multimodal integration in auditory cortex.

Weaknesses:

(1) Unclear correlation between excitatory responses and animal velocity during halts, particularly in closed-loop versus playback conditions.<br /> (2) Ambiguity regarding the identity of the [AM+VM] MM neurons.

Reviewer #2 (Public review):

Using multimodal closed-loop behavior and activity monitoring in the neocortex, Solyga and Keller show that the auditory cortex computes the deviation of current sensory input from expectations. Interestingly, in addition, mismatch responses within the auditory stream are non-linearly influenced by concurrent sensorimotor error computations in the visual pathway. These results suggest that non-hierarchical interactions (lateral relational cross-talk) must be considered when analyzing cortical models based on predictive processing. In my opinion, this is a fundamental study that addresses the question of hierarchical vs. no-hierarchical interactions across neocortical areas. Overall, I find the experiments elegantly designed, and the results robust, providing compelling evidence for non-hierarchical interactions across neocortical areas, and more specifically of exchange of sensorimotor prediction error signals across modalities. The authors thoroughly addressed the concerns raised. In my opinion, this has substantially strengthened the manuscript, enabling much clearer interpretation of the results reported.

Reviewer #3 (Public review):

This study explores sensory prediction errors in sensory cortex. It focuses on the question of how these signals are shaped by non-hierarchical interactions, specifically multimodal signals arising from same level cortical areas. The authors used 2-photon imaging of mouse auditory cortex in head-fixed mice that were presented with sounds and/or visual stimuli while moving on a ball. First, responses to pure tones, visual stimuli and movement onset were characterized. The authors then made the running speed of the mouse predictive of sound intensity and/or visual flow (closed loop). Mismatches were created through the interruption of sound and/or visual flow for 1 second, disrupting the expected sensory signal. As a control, sensory stimuli recorded during the close loop phase were presented again decoupled from the movement (open loop). The authors suggest that auditory responses to the unpredicted interruption of the sound, which affected neither running speed nor pupil size, reflect mismatch responses. That these mismatch responses were enhanced when the visual flow was congruently interrupted, indicates cross-modal influence of prediction error signals.

This study's strengths are the relevance of the question and the design of the experiment. The authors are experts in the techniques used. Responses to the interruption of the sound are similar in quality, if not quantity, in the predictive and the control situation, yet the contribution of sound offset sensitivity to the observed mismatch responses is not discussed.

Reviewer #2 (Public review):

Summary:

The authors begin with the stated goal of gaining insight into the known repression of autophagy by Ezrin, a major membrane-actin linker that assembles signaling complexes on membranes. RNA and protein expression analysis is consistent with upregulation of lysosomal proteins in Ezrin-deficient MEFs, which the authors confirm by immunostaining and western blotting for lysosomal markers. Expression analysis also implicates EGF signaling as being altered downstream of Ezrin loss, and the authors demonstrate that Ezrin promotes relocalization of EGFR from the plasma membrane to endosomes. Ezrin loss reduces downstream MAPK and Akt signaling, and represses mTORC1 signaling by promoting lysosomal localization of the TSC complex. An Ezrin mutant Medaka fish line is then generated to test its role in retinal cells, which are known to be sensitive to changes in autophagy regulation. Phenotypes in this model appear generally consistent with observations made in cultured cells, though milder overall.

Strengths:

Data on the impact of Ezrin-loss on relocalization of EGFR from the plasma membrane are extensive, and thoroughly demonstrate that Ezrin is required for EGFR internalization in response to EGF.

A new Ezrin-deficient in vivo model (Medaka fish) is generated.

Strong data demonstrating that Ezrin loss suppresses Akt signaling and mTORC1 signaling by promoting TSC complex localization to the lysosome.

Weaknesses:

The authors have addressed all concerns

Reviewer #3 (Public review):

Summary:

In this study, the authors have attempted to demonstrate a critical role for the cytoskeletal scaffold protein Ezrin, in the upstream regulation of EGFR/AKT/MTOR signaling. They show that in the absence of Ezrin, ligand-induced EGFR trafficking and activation at the endosomes is perturbed, with decreased endosomal recruitment of the TSC complex, and a corresponding decrease in AKT/MTOR signaling.

Strengths:

The authors have used a combination of novel imaging techniques, as well as conventional proteomic and biochemical assays to substantiate their findings. The findings expand our understanding of the upstream regulators of the EGFR/AKT MTOR signaling and lysosomal biogenesis, appear to be conserved in multiple species, and may have important implications for the pathogenesis and treatment of diseases involving endo-lysosomal function, such as diabetes and cancer, as well as neuro-degenerative diseases like macular degeneration. Furthermore, pharmacological targeting of Ezrin could potentially be utilized in diseases with defective TFEB/TFE3 functions like LSDs. While a majority of the findings appear to support the hypotheses, there are substantial gaps in the findings that could be better addressed. Since Ezrin appears to directly regulate MTOR activity, the effects of Ezrin KO on MTOR-regulated, TFEB/TFE3 -driven lysosomal function should be explored more thoroughly. Similarly, a more convincing analysis of autophagic flux should be carried out. Additionally, many immunoblots lack key controls (Control IgG in CO-Ips) and many others merit repetition to either improve upon the quality of the existing data, validate the findings using orthogonal approaches or to provide a more rigorous quantitative assessment of the findings, as highlighted in the recommendation for authors.

Comments on revisions:

The authors have satisfactorily addressed most of the concerns raised in the prior version, and have significantly improved upon the overall findings in the revised version.

Reviewer #1 (Public review):

Summary:

This study examines the cortical modular functional organization of visual texture in comparison with that of color and disparity. While color, disparity, and orientation have been shown to exhibit clear functional organizations within the thin, thick, and thick/pale stripes of V2, whether the feature of texture is also organized within V2 is unknown. Using ultrahigh field 7T fMRI in humans viewing color-, disparity-, and texture-specific visual stimuli, the authors find that, unlike color and disparity, texture does not exhibit stripe-specific organization in V2. Moreover, using laminar imaging methods and calculations of informational connectivity, they find V2 color and disparity stripes exhibit the expected feedforward and feedback relationships with V1 & V4, and with V1 & V3ab, respectively. In contrast, texture activation, found predominantly in the deep layers of V2, is driven preferentially by feedback from V4. Based on these findings, the authors suggest that texture is a visual feature computed in higher-order areas and not generated by local intra-V2 computation.

Strengths:

This study poses an interesting and fundamental question regarding the relationship between functional modularity and hierarchical origin of computed properties. This question is thus highly significant and deserves study. The methodology is appropriate for the question and the areal and laminar resolution achieved across 10 subjects is commendable. The combination of high-resolution functional imaging and informational connectivity analysis introduces a useful way for examining feedforward and feedback relationships in mesoscale imaging data.

Comments on latest version:

The authors have responded adequately to my comments. The lack of texture organization in V2 is now strengthened by the apparently more clustered texture response in V4 (Fig. S9). The paired results in V2 and V4 make the study stronger. The authors may suggest that texture response, while present at the neural level, may not emerge as a primary organizational cue in V2, based on this texture stimulus paradigm. The negative results should still be presented cautiously. The connectivity inferences are interesting but should also be stated cautiously, as there are multiple assumptions. Overall, this study makes a contribution to emerging views about texture processing in the early visual pathways.

Reviewer #2 (Public review):

This study investigates the cortical circuitry at the mesoscopic level of cortical columns in the human secondary visual cortex (V2) using high-resolution fMRI at ultra-high field strength (7T). The findings confirm the columnar organization of color-selective thin and disparity-selective thick stripes, a result previously demonstrated and replicated in human fMRI research. However, this study adds a novel layer of analysis by examining cortical depth, providing insights into feedforward and feedback connections to and from V2. Furthermore, examining texture selectivity in V2 showed no evidence of a columnar structure when compared to color- and disparity-selective activation clusters. Interestingly, texture selectivity in V2 was most pronounced in deeper cortical layers, with significant feedback connectivity from V4. The authors conclude that local columnar circuitry plays a crucial role in color and disparity processing within V2, while texture selectivity is driven by feedback modulation. This research underscores the potential of high-resolution human fMRI to explore the local circuitry of the cortex at the mesoscopic scale.

However, I still have a few comments that I would like to be addressed:

(1) In lines 401-403, the authors state that differential BOLD responses can significantly enhance the laminar specificity. Differential contrasts indeed have the potential to reduce macrovascular contributions that are unspecific to both experimental conditions, which was already discussed in the literature (e.g., Yacoub et al., 2008, High-field fMRI unveils orientation columns in humans). This might be especially true for the pial vasculature that drains a larger surface area of the cortex, e.g., multiple columns, which is probably the key factor that enables cortical column mapping using differential BOLD contrasts despite the relatively large spatial point spread function of the BOLD response. However, this may differ for laminar analyses, where neuronal and vascular responses from intracortical and pial veins might be harder to disentangle. It would, therefore, be advisable to tone down this statement somewhat since it could imply that laminar specificity can be readily achieved with GE-BOLD, while this remains an active area of research. This is not to say that the present results are incorrect, but the broader implications of this statement should be cautiously framed.

(2) Looking at Figure 3, one might also argue (excluding responses from V4) that statistically significant differences in selectivity are only observed where the cortical profiles generally show higher response levels. Could this be simply due to varying signal-to-noise ratios (SNR) achieved by different contrasts (color, disparity, texture)?

(3) In lines 480-484, the authors state that twenty blocks for each stimulus condition should be sufficient to investigate within-subject effects. It would be helpful if they could elaborate on the basis for this claim. High-resolution fMRI is typically limited by low temporal signal-to-noise ratio (tSNR), and extensive averaging is often required to achieve sufficient signal. Clarifying the rationale behind this assertion would strengthen the argument.

Reviewer #3 (Public review):

Summary:

Ai et al. studied texture, color and disparity selectivity in human visual cortex at mesoscale level using high-resolution fMRI. They reproduced earlier monkey and human studies showing interdigitated color-selective and disparity-selective sub-compartments within area V2, likely corresponding to thin and thick stripes, respectively. At least with the stimuli used, no clear evidence for texture-selective mesoscale activations were observed in area V2. The most interesting and novel part of this study focused on cortical-depth-dependent connectivity analyses across areas. The data suggest feedback and feedforward functional connectivity between V1 and V3A for disparity signals and feedback from V4 to the deep layers of V2 for textures.

Strengths:

High-resolution fMRI and highly interesting layer-specific informational connectivity analyses.

Weaknesses:

The authors tend to overclaim their results. Too few data to make conclusive inferences.

Reviewer #1 (Public review):

Summary:

This study investigated the role of PLECTIN, a cytoskeletal crosslinker protein, in liver cancer formation and progression. Using the liver-specific Plectin knockout mouse model, the authors convincingly showed that PLECTIN is critical for hepatocarcinogenesis, as functional inhibition of PLECTIN suppressed tumor formation in several models. They also provided evidence to show that inhibition of PLECTIN inhibited HCC cell invasion and reduced metastatic outgrowth in the lung. Mechanistically, they suggested that PLECTIN inhibition attenuated FAK, MAPK/ERK, and PI3K/AKT signaling.

Strengths:

The authors generated a liver-specific Plectin knockout mouse model. By using DEN and sgP53/MYC models, the authors convincingly demonstrated an oncogenic role of PLECTIN in HCC development. plecstatin-1 (PST), as a plectin inhibitor, showed promising efficacy in inhibiting HCC growth, which provides a basis for potentially treating HCC using PST.

The MIR images for tracking tumor growth in animal models were compelling. The high-quality confocal images and related qualifications convincingly showed the impact of plectin functional inhibition on contractility and adhesions in HCC cells.

Comments on latest version:

My concerns have been largely addressed. The authors did a good job in addressing the questions and clarifying the inconsistent results. I have two comments:

(1) The current data still cannot support the conclusion that plectin inactivation attenuates HCC oncogenic potential through FAK, Erk1/2, and PI3K/Akt axis, unless they can reactivate these signaling to restore the HCC congenic potential in plectin inactivated cells. It might be more appropriate to claim that plectin inactivation suppresses FAK, Erk1/2, and PI3K/Akt oncogenic signaling.

(2) I think it would be beneficial to include the H&E and HNF4α staining from lung tissue of mice inoculated with WT Huh7 cells indicated in the rebuttal letter.

Reviewer #2 (Public review):

Summary:

Plectin is a cytolinker that associates with cytoskeletal and intercellular junction proteins and is essential for epithelial integrity and cell migration. Previous reports showed that PLEC regulates tumor growth and metastasis in different cancers. In this manuscript, the authors describe PLEC as a target in initiation and growth of HCC. They show that inhibiting PLEC reduced tumorigenesis in different in vitro and in vivo HCC models, including in a xenograft model, DEN model, oncogene-induced HCC model and a lung metastasis model. A drug PST had similar effects, a purported Plectin inhibitor, suggesting that PLEC inhibition could be a tumor prevention or treatment strategy. Mechanistically, the authors show that inhibiting PLEC results in a disorganized cytoskeleton, deficiency in cell migration, and changes in cancer-relevant signaling pathways. This study demonstrates the importance of understanding mechanobiology of HCC for the development of new treatment strategies.

Strengths:

(1) This study used a variety of in vivo models to explore the role of Plectin in HCC formation and metastasis, which extend beyond the cell line-based studies reported in prior research.<br /> (2) Blocking PLEC disrupts pathways that promote tumors and cell migration, thus preventing tumor progression.<br /> (3) Overall, the anti-cancer phenotype is promising, strengthening the important role of PLEC and related factors in tumor growth and metastasis.

Weaknesses:

(1) There is limited novel mechanistic insights as the effect of inhibiting PLEC on the cytoskeleton, cell migration and related signaling pathways have previously been reported.<br /> (2) The results associated with PST, should be interpretated with caution. Although it is reported as an inhibitor of PLECTIN, and the phenotypes and pathways affected are similar to the knock-out, additional research is needed to support whether it will be safe and specific in treating or preventing HCC.

Reviewer #3 (Public review):

Summary:

In this manuscript, Outla Z et al described the analysis of Plectin in HCC pathogenesis. Specifically, it was found that elevated Plectin levels in liver tumors, correlated with poor prognosis for HCC patients. Mechanistically, it showed that Plectin-dependent disruption of cytoskeletal networks leads to the attenuation of oncogenic FAK, MAPK/Erk, and PI3K/AKT signals. Finally, the authors showed that Plectin inhibitor plecstatin-1 (PST) is well-tolerated and capable of overcoming therapy resistance in HCC.

Strengths:

The studies of Plectin are not entirely novel (Pubmed: 36613521). Nevertheless, the current manuscript provides a much more detailed mechanistic study and the results have translational implications. Additional strengths include convincing cell biology data, such as Plectin regulates cytoskeletal networks, and HCC migration/invasion.

Comments on latest version:

The authors have addressed my comments.

Reviewer #2 (Public review):

Summary:

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

Strengths:

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

Weaknesses:

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

Clinical relevance is unclear.

Reviewer #3 (Public review):

Summary:

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

Major strengths:

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

Major weaknesses:

• The effect of CCR4 deficiency on the Th1/Th17 balance was not evaluated. Although the role of Th17 cells in atherosclerosis remains controversial, RORγt+ cells constituted, on average, more than 10% of the effector TCD45+CD3+CD4+ lymphocytes in the aorta of Apoe-/- mice (Fig 4H). Changes in the Th1/Th17 balance in lymphoid tissues and aortic lesions may influence the type and functional properties of inflammatory cells recruited to the atherosclerotic aorta.

• Lack of in vivo evidence for Treg suppressive effects on DC activation. The proposed CCR4 requirement for the Treg suppressive activity on DC activation is supported by in vitro co-culture assays, in which CCR4-deficiency partially reverted Treg regulatory actions. Higher expression of CD86, a DC activation marker, was found in spleen DCs from Ccr4-/- Apoe-/- mice compared to Apoe-/- mice (Supplementary Fig 5), which would be worth commenting on and discussing.

• Methodological limitations. Controls in flow cytometry analysis were suboptimal (no viability and doublets were checked) which may have introduced artefacts, especially when measuring less-represented cell populations within complex samples. In addition, assessing Treg migration to the aorta in atherosclerotic mice faced methodological limitations that hindered statistical comparisons between Tregs from Apoe-/- and Ccr4-/- Apoe-/- mice, leading to inconclusive results. The dependence on CCR4 expression for Treg migration to the atherosclerotic aorta was not established.

• Treg transference experiments did not allow the detection of a reduction in the aortic lesion area by transferred CCR4 expressing Tregs (comparison between saline and Apoe-/- Tregs groups). Using Apoe-/- mice as recipients, the CCR4-dependent protective effect of Tregs was mostly evidenced by analysis of aortic inflammation, which was valuable. When using Ccr4-/- Apoe-/- mice as recipients, analysis of aortic inflammation was not mentioned.

Study limitations:

This investigation has some limitations. Current tools for single-cell characterization have revealed the phenotypic heterogeneity and dynamics of aortic leukocytes, including T cells, which are among the principal aortic leukocytes found in mouse and human atherosclerotic lesions (doi:10.1161/CIRCRESAHA.117.312513). The flow cytometry analysis applied in this study cannot distinguish the generation of particular phenotypes within T CD4+ subsets, including putative phenotypes of no-suppressive T cells expressing low levels of Foxp3, as seems could occur in other chronic inflammatory disorders (doi: 10.1038/nm.3432; doi: 10.1172/JCI79014). Limitations due to the use of a complete CCR4 knockout mouse and putative differences in CCR4-mediated mechanisms along atherosclerosis stages and in human atherosclerosis were commented on by the authors in the discussion.

Global Impact:

This work opens the way for a deeper analysis of the contribution of CCR4 and its ligands to the activation and differentiation of T CD4+ lymphocytes during atherosclerosis development, with these lymphocytes being fundamental players in the generation of pro-atherogenic and anti-atherogenic immune responses. Differences in the mechanisms mediated by the CCL17/CCL22-CCR4 axis among early and advanced atherosclerosis highlight the complex landscape to examine and validate in human samples and the need to achieve a deep knowledge for identifying genuine and safe targets capable of promoting protective anti-atherogenic immune responses.

Reviewer #1 (Public review):

Summary:

In this manuscript, Liu et al have tried to dissect the neural and molecular mechanisms that C. elegans use to avoid digestion of harmful bacterial food. Liu et al show that C. elegans use the ON-OFF state of AWC olfactory neurons to regulate the digestion of harmful gram-positive bacteria S. saprophyticus (SS). The authors show that when C. elegans are fed on SS food, AWC neurons switch to OFF fate which prevents digestion of S. saprophyticus and this helps C. elegans avoid these harmful bacteria. Using genetic and transcriptional analysis as well as making use of previously published findings, Liu et al implicate the p38 MAPK pathway (in particular, NSY-1, the C. elegans homolog of MAPKKK ASK1) and insulin signaling in this process.

Strengths:

The authors have used multiple approaches to test the hypothesis that they present in this manuscript.

Weaknesses:

Overall, I am not convinced that the authors have provided sufficient evidence to support the various components of their hypothesis. While they present data that loosely align with their hypothesis, they fail to consider alternative explanations and do not use rigorous approaches to strengthen their overall hypothesis. The selective picking of genes from the RNA sequencing data and forcing the data to fit the proposed hypothesis based on previously published findings, without exploring other approaches, indicates a lack of thoroughness and rigor. These critical shortcomings significantly diminish enthusiasm for the manuscript in its totality. In my opinion, this is the biggest weakness in this manuscript.

Reviewer #2 (Public review):

Summary:

Using C. elegans as a model, the authors present an interesting story demonstrating a new regulatory connection between olfactory neurons and the digestive system. Mechanistically, they identified key factors (NSY-1, STR-130 et.al) in neurons, as well as critical 'signaling factors' (INS-23, DAF-2) that bridge different cells/tissues to execute the digestive shutdown induced by poor-quality food (Staphylococcus saprophyticus, SS).

Strengths:

The conclusions of this manuscript are mostly well supported by the experimental results shown.

Weaknesses:

Several issues could be addressed and clarified to strengthen their conclusions.

(1) The word "olfactory" should be carefully used and checked in this manuscript. Although AWCs are classic olfactory neurons in C. elegans, no data in this manuscript supports the idea that olfactory signals from SS drive the responses in the digestive system. To validate that it is truly olfaction, the authors may want to check the responses of worms (e.g. AWC, digestive shutdown, INS-23 expression) to odors from SS.

(2) In line 113, what does "once the digestive system is activated" mean? The authors need to provide a clearer statement about 'digestive activation' and 'digestive shutdown'.

(3) No control data on OP50. This would affect the conclusions generated from Figures 2A, 2B, 2D, 3B, 3C, 3G, 4D-G, 5D-E, 6B-D.

(4) Do the authors know which factors are released from AWC neurons to drive the digestive shutdown?

Reviewer #3 (Public review):

Summary:

The study explores a molecular mechanism by which C. elegans detects low-quality food through neuron-digestive crosstalk, offering new insights into food quality control systems. Liu and colleagues demonstrated that NSY-1, expressed in AWC neurons, is a key regulator for sensing Staphylococcus saprophyticus (SS), inducing avoidance behavior and shutting down the digestive system via intestinal BCF-1. They further revealed that INS-23, an insulin peptide, interacts with the DAF-2 receptor in the gut to modulate SS digestion. The study uncovers a food quality control system connecting neural and intestinal responses, enabling C. elegans to adapt to environmental challenges.

Strengths:

The study employs a genetic screening approach to identify nsy-1 as a critical regulator in detecting food quality and initiating adaptive responses in C. elegans. The use of RNA-seq analysis is particularly noteworthy, as it reveals distinct regulatory pathways involved in food sensing (Figure 4) and digestion of Staphylococcus saprophyticus (Figure 5). The strategic application of both positive and negative data mining enhances the depth of analysis. Importantly, the discovery that C. elegans halts digestion in response to harmful food and employs avoidance behavior highlights a physiological adaptation mechanism.

Weaknesses:

Major points:

(1) While NSY-1 positively regulates str-130 expression in AWC neurons and is critical for SS avoidance and survival, the authors should examine whether similar phenotypes are observed in str-130 mutants.

(2) NSY-1 promotes the AWC-OFF state through str-130, inhibiting SS digestion. The authors should investigate whether STR-130 in AWC neurons regulates bcf-1 expression levels in the intestine.

(3) The current results rely on str-2 expression levels to indicate the AWC state. Ablating AWC neurons and testing the effects on digestion would provide stronger evidence for their role in digestive regulation.

(4) The claim that NSY-1 inhibits INS-23 and that INS-23 interacts with DAF-2 to regulate bcf-1 expression (Line 339-340) requires further validation. Neuron-specific disruption of INS-23 and gut-specific rescue of DAF-2 should be tested.

(5) Figure Reference Errors: Lines 296-297 mention Figure 6E, which does not exist in the main text. This appears to refer to Figure 5E, which has not been described.

Reviewer #1 (Public review):

Summary:

In their paper, Tutunji et al aim to investigate the dynamic effects of stress on activity of different brain networks (salience network, executive network, and default mode network). Crucially they differentiate between rapid (<1 h) and late (>1) effects of stress. Lastly, they connect acute changes in brain activity with inter-individual differences in stress reactivity in real-life assessed using EMA.

They first show the expected dynamics in stress-induced brain activity with a transient increase in salience network activity and a decrease in default mode network activity although in contrast to expectations, this did not disappear in the late phase. Notably, the increase in salience network activity was associated with a 'resilience index' derived from EMA that captures whether an individual responds with more or less reduction in positive effect than expected based on the number of above average stress events.

Linking acute stress to long-term affective stress reactivity is a crucial step to better understand how adaptive or maladaptive stress responses play out in the long term and how they might be related to mental health problems.

Strengths:

The link of the acute stress response to stress reactivity in daily life is highly relevant and a major strength of the paper. Moreover, the design of the EMA component assessing a week with low stress and one with high stress (exam week) in all participants and thus including a naturalistic manipulation enables a quantification of stress reactivity that captures 'real life'.

The authors do not only quantify the magnitude of the acute stress response but take into account an early as well as late response to disentangle the dynamic nature of the stress response. In that way, it is possible to establish which parts of the stress response are relevant for the affective response.

In addition to reporting changes in network activation, the authors also report behavioral outcomes of the tasks which is crucial to evaluate the meaning and relevance of the neural outcomes.

Weaknesses:

Although the authors assess multiple physiological outcomes to the stress task, only the cortisol response is analyzed with regard to its association with the stress-induced changes in network activity. Considering that it is mainly the salience network that shows an increase and this in the early phase that is characterized by the noradrenaline and not so much the cortisol response, an association with a marker of the NA response would be interesting.

To evaluate the association of the acute stress response with stress reactivity in real life more conclusively it would be interesting to see whether and how the affective response to the acute stress is related to stress reactivity in real life.

In the introduction, the authors hypothesize that all networks show distinct activation patterns during the stress response and expect all of them to be associated with the stress reactivity during EMA. However, no correction for multiple comparisons across the many tests (each network at two phases) is reported.

All stress-induced changes in activity are assessed by using other tasks since it is not trivial to measure changes in activation of specific regions without comparing different conditions of a task. Nonetheless, with the chosen approach it is not completely clear whether stress only modulates brain responses to other tasks or changes activation within those networks independently of any other tasks. Moreover, one of the tasks did not elicit the expected activation contrast and it is unclear whether this affects stress-effects.

Some of the less central results that are discussed in the paper such as the association of the real-life stress reactivity measure with neuroticism, the sex-effect of the cortisol response or the mediation and moderation models of the stress-induced changes in network activity and performance in the tasks seem slightly overinterpreted considering that they are either not quite significant or not hypothesized and thus it is not clear why for example once a mediation and in another outcome a moderation model was chosen.

Reviewer #2 (Public review):

Summary:

This study aimed to investigate changes in neural responses over time after acute stress and their association with real-life stress. To this end, functional MRI data was collected from 3 tasks (Oddball, 2-back, Associative retrieval) early and late following stress and control conditions. Emotional ratings during a stressful week before an exam and a non-stressful week without an exam were used to index real-world stress. In total, data from 70 individuals were used for the analyses in the paper. Results showed increased oddball related activation early after stress whereas activation to the associative retrieval was reduced across early and late trials following stress compared with control. Brain activation during the oddball task after stress contrasted against control correlated with the index used to measure stress in the real-world. This is a very ambitious study and the findings that stress has opposite effects on the oddball and the associative retrieval tasks is new. However, I am not convinced that brain responses are correlated with real-world stress from the results presented in the paper. I also have several other concerns listed below.

Strengths:

The study uses a unique design based on hypothesis firmly grounded in theories of stress related brain function. Large amounts of data are collected for all of the 70 participants included in the analyses and the hypotheses tested using paired tests have strong statistical power. Data collection methods are sound aiming to reduce stress induced by being in the scanner environment for the first time and reducing variation in cortisol due to circadian rhythm.

Weaknesses:

An important argument in the paper is that neural responses associated with stress in the lab correspond to stress in real life. This conclusion is based on a single correlation analysis. This is weak evidence because the correlation is based on 70 individuals and may be driven by outliers. In fact, the correlation between the difference in stress-related SN activation (Stress-Control) and real life stress residual is likely to be driven by outliers. In fig 5b, there are 3 persons with SN values of around 2, which is twice as much as the fourth highest value. There is also 1 person with a Real life stress residual of -3 or -4, which is three to four times as much as the person with the second lowest value. These 4 outliers should be removed before calculating the correlation coefficient. Also, no power analysis is presented in the paper showing what effect size is needed for significant results given a sample size of 70.

It is not clear why the activation maps from the tasks performed in the scanner are referred to as the SN, ECN, and DMN. They are discussed as if they were resting state networks. They are however not resting state networks because they are the results of contrasting two task conditions to each other and not the results from correlating BOLD time-series data from different regions within subjects. Even though masks corresponding to SN, ECN, and DMN are used to calculate means of all voxels, I think these contrasts should be referred to as the tasks that were used to evoke them. It becomes misleading to call them networks which usually refers to nodes and edges in fMRI studies. The first scan was a resting state scan, but these data are not presented in the paper.

Introduction<br /> In the introduction it is said that there are genomically driven effects of cortisol 1 to 2 hours after stress. This is repeated in the discussion: "[the late stress phase] is thought to be dominated by genomically driven effects of glucocorticoids". (There is no reference to this statement however.) This idea, that gene expression should only be regulated by corticosteroids following stress seems unrealistic. The increase in cortisol was only around 60% from baseline in the current study which seems to be similar to other studies. This means that the baseline cortisol level is far from zero. Therefore, effects of cortisol on gene expression must occur all the time and be tightly regulated by circadian clocks. To propose that genomically driven effects of cortisol only exist 1 to 2 hours following stress is therefore too simplistic.

In the last paragraph, it says that n=83. However, the final sample consists of 70 people. Correct this number.

Methods<br /> The EMA data analysis is difficult to understand. Why are the residuals used instead of means for example? I could not understand how the residual values used in the analysis should be interpreted from the way this section was written. Therefore, I cannot judge whether the index is valid or reliable. Using mean values is more common than using residuals when investigating individual differences in stress responses. The use of residuals needs justification and clarification. The results from an analysis using mean values should also be reported.

How was AUCi calculated? What software was used to calculate AUCi?

How was the mediation analysis performed? The only information I found was: "We additionally ran separate models with an interaction term modelled for neural activity in the targeted ROI's to examine the relationship between task performance and neural responses, with random slopes and intercepts also modelled for ROI activity." This is not how mediation analyses are done conventionally. It is common to use structural equation modelling or a series of regression analyses. What is meant by separate models? Was a reduced model compared to a full model with an interaction term? In this case, this is not a mediation analysis. I think the term moderation is better to describe this analysis.

Reviewer #3 (Public review):

This is a very interesting study that aims to examine the effect of stress induction across about two hours on physiological, behavioral, and neural measures in several brain areas. This aim is of importance for the study of stress response and recovery and their neural bases. There are several strengths to the design, including a within-subject design, adequate sample size, and multiple levels of assessment (including lab-based and real-life), and the authors should really be commended for that. The results indicate an acute cortisol response following stress induction, although HR data show that the manipulation may have been effective only among those who did the stress scan first. Behaviorally, stress induction resulted in effects on one of the tasks. Neurally, temporal changes in response were observed in what is referred to as SN and DMN networks, and associations with real-life stress were evident for SN during early stress response. Together, evidence emerged for some temporal changes in stress response on neural function and its associations with behavior and real-life stress response as indicated by self-report EMA.

These findings, both positive and null, provide important insight to the field, and the authors should be praised for that. At the same time, it is important to emphasize that some aspects or findings complicate interpretation and limit the extent of inference, that many places in the manuscript could benefit from clarification, and that more discussion should be given to the null findings.

All in all, given the importance of the questions and the strengths of the design, this study could provide a major contribution to future research. But, to accurately and optimally guide research, it is important to accurately describe and interpret both what was tested and found, and what was not found. Some more specific points are noted below, where improvements could be made to facilitate extraction of insight by the reader, and thus increase the impact of the study on the field.

Reviewer #1 (Public review):

Summary:

This is an important and interesting study that uses the split-GFP approach. Localization of receptors and correlating them to function is important in understanding the circuit basis of behavior.

Strengths:

The split-GFP approach allows visualization of subcellular enrichment of dopamine receptors in the plasma membrane of GAL4-expressing neurons allowing for high level of specificity.

The authors resolve the presynaptic localization of DopR1 and Dop2R, in "giant" Drosophila neurons differentiated from cytokinesis-arrested neuroblasts in culture as its not clear in the lobes and calyx.

Starvation induced opposite responses of dopamine receptor expression in the PPL1 and PAM DANs provides key insights into models of appetitive learning.<br /> Starvation induced increase in D2R allows for increased negative feedback that the authors test in D2R knockout flies where appetitive memory is diminished.<br /> This dual autoreceptor system is an attractive model for how amplitude and kinetics of dopamine release can be fine tunes and controlled depending on the cellular function and this paper presents a good methodology to do it and a good system where dynamics of dopamine release can be tested at the level of behavior.

Weaknesses:

Key weaknesses have been resolved: 

1) Receptor expression is consistent between time of the day and the authors picked two time points. The authors mention that the states of animals could affect LI (e.g. feeding state and anesthesia for sorting, see methods) were kept constant. These data and discussion are helpful. <br /> 2) Giant fiber system is argued to be a great model and authors have added additional references. However I am not very deeply familiar with these references or the giant fiber system so I am not completely clear but the argument seems reasonable. <br /> 3) The revised manuscript, shows data in the γ KCs (Figure 4C, Figure 5 - figure supplement 1) in addition to α/β KCs, so it appears there is consistency between lobes. <br /> 4) The new data for Dop1R1 and Dop2R in MBON-γ1pedc>αβ helps with thinking about dopamine receptor co-localization and it would be a herculean talk to do this for all the regions but still keeps room open for different scenarios. 

The papers discussion has been expanded to account for different possibilities which will help the readers get a more complete picture. I appreciate the review efforts and detailed response to reviewer comments.

Reviewer #2 (Public review):

Summary:

Hiramatsu et al. investigated how cognate neurotransmitter receptors with antagonizing downstream effects localize within neurons when co-expressed. They focus on mapping the dopaminergic Dop1R1 and Dop2R receptors, corresponding to the mammalian D1- and D2-like dopamine receptors, which have opposing effects on intracellular cAMP levels, in neurons of the Drosophila mushroom body (MB). To visualize specific receptors in single neuron types within the crowded MB neuropil, the authors use existing dopamine receptor alleles tagged with 7 copies of split GFP to target the reconstitution of GFP tags specifically in the neurons of interest, providing a readout of receptor localization.

The authors demonstrate that both Dop1R1 and Dop2R are enriched, to differing degrees, in the axonal compartments of Kenyon cells cholinergic presynaptic inputs and in different dopamine neurons (DANs) that project axons to the MB. Co-localization studies of dopamine receptors with the presynaptic marker Brp suggest that Dop1R1, and to a greater extent Dop2R, localize near release sites. This pattern in DANs suggests Dop1R1 and Dop2R serve as dual-feedback autoreceptors. Finally, they provide evidence that the balance of Dop1R1 and Dop2R in the axons of two different DAN populations is differentially modulated by starvation, which plays a role in regulating appetitive behaviors.

In their revised manuscript, Hiramatsu et al. revisited the localization and functional integrity of Dop1R1 and Dop2R within the Drosophila mushroom body. This revision strengthens their claims with new high-resolution imaging data and additional behavioral assays, supporting the functional integrity of 7X split GFP-tagged receptors and their distinct localizations within neural circuits.

The revised manuscript by Hiramatsu et al. demonstrates substantial improvements in experimental design and data presentation, effectively addressing concerns raised during the initial review. The addition of advanced imaging techniques and behavioral data confirms the functionality of tagged receptors, while providing deeper insights into their spatial and functional dynamics within neural circuits modulating responses to environmental changes like starvation. This study makes an important contribution to neuroscience, enhancing our understanding of dopamine receptor distribution in circuits underlying learning and memory.

Strengths:

The authors use reconstitution of GFP fluorescence of split GFP tags integrated at the endogenous locus of dopamine receptors, providing a precise readout of receptor localization. This method preserves endogenous transcriptional and post-transcriptional regulation, a critical feature for protein localization studies.

The choice of the Drosophila mushroom body as a model system is excellent, as it is well-studied, its connectome is carefully reconstructed, and its role in behaviors and associative memory enables linking receptor localization patterns to circuit function and behavior. This approach allows the authors to demonstrate that antagonizing dopamine receptors can act as autoreceptors within the axonal compartments of MB-innervating DANs. Moreover, they show that starvation differentially modulates the balance of these receptors in distinct DANs, highlighting the role of this regulation in circuit function and behavior.

The incorporation of higher-resolution Airyscan microscopy and functional assays in the revision provide evidence that tagged receptors retain functionality and predominantly localize at presynaptic sites within Kenyon cells and DANs. These findings support the dual autoreceptor feedback model proposed.

Weaknesses:

While the revision significantly strengthens the manuscript, the absence of specific antibodies against these receptors remains a limitation. This is understandable given the challenges of generating antibodies against such proteins. However, the use of more direct validation methods, such as specific antibodies (if available), and employing higher-resolution techniques like expansion microscopy, could further validate and enhance the robustness of the findings.

Reviewer #1 (Public review):

Shen et al. conducted three experiments to study the cortical tracking of the natural rhythms involved in biological motion (BM), and whether these involve audiovisual integration (AVI). They presented participants with visual (dot) motion and/or the sound of a walking person. They found that EEG activity tracks the step rhythm, as well as the gait (2-step cycle) rhythm. The gait rhythm specifically is tracked superadditively (power for A+V condition is higher than the sum of the A-only and V-only condition, Experiments 1a/b), which is independent of the specific step frequency (Experiment 1b). Furthermore, audiovisual integration during tracking of gait was specific to BM, as it was absent (that is, the audiovisual congruency effect) when the walking dot motion was vertically inverted (Experiment 2). Finally, the study shows that an individual's autistic traits are negatively correlated with the BM-AVI congruency effect.

Reviewer #2 (Public review):

The authors evaluate spectral changes in electroencephalography (EEG) data as a function of the congruency of audio and visual information associated with biological motion (BM) or non-biological motion. The results show supra-additive power gains in the neural response to gait dynamics, with trials in which audio and visual information was presented simultaneously producing higher average amplitude than the combined average power for auditory and visual conditions alone. Further analyses suggest that such supra-additivity is specific to BM and emerges from temporoparietal areas. The authors also find that the BM-specific supra-additivity is negatively correlated with autism traits.

Reviewer #1 (Public review):

Summary:

This paper investigates the mechanism of axon growth directed by the conserved guidance cue UNC-6/Netrin. Experiments were designed to distinguish between alternative models in which UNC-6/Netrin functions as either a short range (haptotactic) cue or a diffusible (chemotactic) signal that steers axons to their final destinations. In each case, axonal growth cones execute ventrally directed outgrowth toward a proximal source of UNC-6/Netrin. This work concludes that UNC-6/Netrin functions as both a haptotactic and chemotactic cue to polarize the UNC-40/DCC receptor on the growth cone membrane facing the direction of growth. Ventrally directed axons initially contact a minor longitudinal nerve tract (vSLNC) at which UNC-6/Netrin appears to be concentrated before proceeding in the direction of the ventral nerve cord (VNC) from which UNC-6/Netrin is secreted. Time lapse imaging revealed that growth cones appear to pause at the vSLNC before actively extending ventrally directed filopodia that eventually contact the VNC. Growth cone contacts with the vSLNC were unstable in unc-6 mutants but were restored by expression of a membrane tethered UNC-6 in vSLNC neurons. In addition, expression of membrane tethered UNC-6/Netrin in the VNC was not sufficient to rescue initial ventral outgrowth in an unc-6 mutant. Finally, dual expression of membrane tethered UNC-6/Netrin in both vSLNC and VNC partially rescued the unc-6 mutant axon guidance defect, thus suggesting that diffusible UNC-6 is also required. This work is important because it potentially resolves the controversial question of how UNC-6/Netrin directs axon guidance by proposing a model in which both of the competing mechanisms, e.g., haptotaxis vs chemotaxis, are successively employed. The impact of this work is bolstered by its use of powerful imaging and genetic methods to test models of UNC-6/Netrin function in vivo thereby obviating potential artifacts arising from in vitro analysis.

Strengths:

A strength of this approach is the adoption of the model organism C. elegans to exploit its ready accessibility to live cell imaging and powerful methods for genetic analysis.

Weaknesses:

In the revised version of this manuscript, the authors have redressed the weaknesses highlighted in my review of the original paper.

Reviewer #2 (Public review):

Nichols et al studied the role of axon guidance molecules and their receptors and how these work as long-range and/or local cues, using in-vivo time-lapse imaging in C. elegans. They found that the Netrin axon guidance system, work in different modes when acting as a long-range (chemotaxis) cue vs local cue (haptotaxis). As an initial context, they take advantage of the postembryonic-born neuron, PDE, to understand how its axon grows and then is guided into its target. They found that this process occurs in various discrete steps, during which the growth cone migrates and pauses at specific structures, such as the vSLNC. The role of the UNC-6/Netrin and UNC-40/DCC axon guidance ligand-receptor pair was then looked at in terms of its requirement for (1) initial axon outgrowth direction, (2) stabilization at the intermediate target, (3) directional branching from the sublateral region or (4) ventral growth from intermediate target to the VNC. They found that each step is disrupted in the unc-6/Netrin and unc-40/DCC mutants and observed how the localization of these proteins changed during the process of axon guidance in wild type and mutant contexts. These observations were further supported by analysis of a mutant important for the regulation of Netrin signaling, the E3 ubiquitin ligase madd-2/Trim9/Trim67. Remarkably, the authors identified that this mutant affected axonal adhesion and stabilization, but not directional growth. Using membrane-tethered UNC-6 to specific localities, they then found this to be a consequence of the availability of UNC-6 at specific localities within the axon growth path. Altogether, this data and in-vivo analysis provide compelling evidence of the mechanistic foundation of Netrin-mediated axon guidance and how it works step by step.

The conclusions are well-supported, with both imaging and quantification of each step of axon guidance and localization of UNC-6 and UNC-40. Using a different type of neuron to validate their findings further supports their conclusions and strengthens their model. They also probe the role of the axon guidance ligand-receptor pair SLT-1/Slit and SAX-3/ROBO in this process and find it to work in parallel to UNC-6. This work sets up the stage for future analysis of other axon guidance molecules or regulators using time-lapse in-vivo imaging to better understand their role as long-range and/or local cues.

Reviewer #3 (Public review):

Summary:

This manuscript from Nichols, Lee, and Shen tackles an important question of how unc6/netrin promotes axon guidance: i.e. haptotaxis vs chemotaxis. This has recently been a large topic of investigation and discussion in the axon guidance field. Using live cell imaging of unc6/netrin and unc40/DCC in several neurons that extend axons ventrally during development, as well as TM localized mutants of Unc6, they suggest that unc6 promotes first haptotaxis of the emerging growth cone followed by chemotaxis of the growth cone. This is timely, as a recent preprint from the Lundquist group, using a similar strategy to make only a TM anchored unc6 similarly found that this could rescue only the haptotaxis like growth of the PDE neuron, but not the second phase of growth. However, their conclusions were quite different based on the overexpression of unc6 everywhere rescuing the second phase, and thus they conclude that a gradient is not present.

Strengths:

As this has been quite a controversy in both the invertebrate and vertebrate fields, one strength of this paper is that they use a unc6-neon green to demonstrate unc6 localization, and show localization. Further, they provide localisation of the transmembrane tether version of netrin, showing its restriction to nerve cords.

Reviewer #1 (Public review):

Summary:

This interesting and well-written article by Tuckowski et al. summarizes work connecting the flavin-containing monooxygenase FMO-4 with increased lifespan through a mechanism involving calcium signaling in the nematode Caenorhabditis elegans.

The authors have previously studied another fmo in worms, FMO-2, prompting them to look at additional members of this family of proteins. They show that fmo-4 is up in dietary restricted worms and necessary for the increased lifespan of these animals as well as of rsks-1 (s6 kinase) knockdown animals. They then show that overexpression of fmo-4 is sufficient to significantly increase lifespan, as well as healthspan and paraquat resistance. Further, they demonstrate that overexpression of fmo-4 solely in the hypodermis of the animal recapitulates the entire effect of fmo-4 OE.

In terms of interactions between fmo-2 and fmo-4 they show that fmo-4 is necessary for the previously reported effects of fmo-2 on lifespan, while the effects of fmo-4 do not depend on fmo-2.

Next the authors use RNASeq to compare fmo-4 OE animals to wild type. Their analyses suggested the possibility that FMO-4 was modulating calcium signaling, and through additional experiments specifically identified the calcium signaling genes crt-1, itr-1, and mcu-1 as important fmo-4 interactors in this context. As previously published work has shown that loss of the worm transcription factor atf-6 can extend lifespan through crt-1, itr-1 and mcu-1, the authors asked about interactions between fmo-4 and atf-6. They showed that fmo-4 is necessary for both lifespan extension and increased paraquat resistance upon RNAi knockdown of atf-6.

Overall this clearly written manuscript summarizes interesting and novel findings of great interest in the biology of aging, and suggests promising avenues for future work in this area.

Strengths:

This paper contains a large number of careful, well executed and analysed experiments in support of its existing conclusions, and which also point toward significant future directions for this work. In addition it is clear and very well written.

Weaknesses:

Within the scope of the current work there are no major weaknesses. That said, the authors themselves note pressing questions beyond the scope of this study that remain unanswered. For instance, the mechanistic nature of the interactions between FMO-4 and the other players in this story, for example in terms of direct protein-protein interactions, is not at all understood yet. Further, powerful tools such as GCaMP expressing animals will enable a much more detailed understanding of what exactly is happening to calcium levels, and where and when it is happening, in these animals.

Reviewer #2 (Public review):

Summary:

Members of a conserved family of flavin-containing monooxygenases (FMOs) play key roles in lifespan extension induced by diet restriction and hypoxia. In C. elegans, fmo-2 has received the majority of attention, but there are multiple fmo genes in both worms and mammals, and how overlapping or distinct the functional roles of these paralogs are remains unclear. Here Tuckowski et al. identify that a new family member, fmo-4, is also a positive modulator of lifespan. Based on differential requirements of fmo-2 and fmo-4 in stress resistance and lifespan extension paradigms, however, the authors conclude that fmo-4 acts through mechanisms that are distinct from fmo-2. Ultimately, the authors place fmo-2 genetically within a pathway involving atf-6, calreticulin, the IP3 receptor, and mitochondrial calcium uniporter, which was previously shown to link ER calcium homeostasis to mitochondrial homeostasis and longevity. The authors thus achieve their overarching aim to reveal that different FMO family members regulate stress resistance and lifespan through distinct mechanisms. Furthermore, because the known enzymatic activity of FMOs involves oxygenating xenobiotic and endogenous metabolites, these findings highlight a potential new link between redox/metabolic homeostasis and ER-mitochondrial calcium signaling.

Strengths:

The authors demonstrate links between multiple conserved life-extending signaling pathways and fmo-4, expanding both the significance and mechanistic diversity of FMO-family genes in aging and stress biology.

The authors use genetics to discover an interesting and unanticipated new link between FMOs and calcium pathways known to regulate lifespan.

The genetic epistasis patterns for lifespan and stress resistance phenotypes are generally clean and compelling.

Weaknesses:

The authors achieve a necessary and valuable first step with regard to linking FMO-4 to calcium homeostasis, but the mechanisms involved remain preliminary at this stage. Specifically, the genetic interactions between fmo-4 and conserved mediators of calcium transport and signaling are convincing, but a putative molecular mechanism by which the activity of FMO-4 would alter subcellular calcium transport remains unclear and potentially indirect. The authors effectively highlight this gap as a key pursuit for subsequent studies.

The authors have shown that carbachol and EDTA produce the expected effects on a cytosolic calcium reporter in neurons, supporting the utility of the chemical approach in general, but validating that carbachol, EDTA and fmo-4 itself have an impact on calcium in the tissues and subcellular compartments relevant to the lifespan phenotypes would still be valuable in supporting the overall model. Notably, however, the hypodermal-specific role of FMO-4 suggests potential cell non-autonomous regulation of lifespan, such that this pathway may ultimately involve complex inter-cellular signaling that would necessitate substantially more time and effort.

Employing mutants and more sophisticated genetic tools for modulating calcium transport or signaling (in addition to RNAi) would strengthen key conclusions and/or help to elucidate tissue- or age-specific aspects of the proposed mechanism.

Reviewer #3 (Public review):

Summary:

The authors assessed the potential involvement of fmo-4 in a diverse set of longevity interventions, showing that this gene is required for DR and S6 kinase knockdown related lifespan extension. Using comprehensive epistasis experiments they find this gene to be a required downstream player in the longevity and stress resistance provided by fmo-2 overexpression. They further showed that fmo-4 ubiquitous overexpression is sufficient to provide longevity and paraquat (mitochondrial) stress resistance, and that overexpression specifically in the hypodermis is sufficient to recapitulate most of these effects.

Interestingly, they find that fmo-4 overexpression sensitizes worms to thapsigargin during development, an effect that they link with a potential dysregulation in calcium signalling. They go on to show that fmo-4 expression is sensitive to drugs that both increase or decrease calcium levels, and these drugs differentially affect lifespan of fmo-4 mutants compared to wild-type worms. Similarly, knockdown of genes involved in calcium binding and signalling also differentially affect lifespan and paraquat resistance of fmo-4 mutants.

Finally, they suggest that atf-6 limits the expression of fmo-4, and that fmo-4 is also acting downstream of benefits produced by atf-6 knockdown.

Strengths:

• comprehensive lifespans experiments: clear placement of fmo-4 within established longevity interventions.<br /> • clear distinction in functions and epistatic interactions between fmo-2 and fmo-4 which lays a strong foundation for a longevity pathway regulated by this enzyme family.

Weaknesses:

• no obvious transcriptomic evidence supporting a link between fmo-4 and calcium signalling: either for knockout worms or fmo-4 overexpressing strains.<br /> • no direct measures of alterations in calcium flux, signalling or binding that strongly support a connection with fmo-4.<br /> • no measures of mitochondrial morphology or activity that strongly support a connection with fmo-4.<br /> • lack of a complete model that places fmo-4 function downstream of DR and mTOR signalling (first Results section), fmo-2 (second Results section) and at the same time explains connection with calcium signalling.

Comments on revisions:

The authors have addressed and fixed all the private comments we had made. In terms of the public comments, I think nothing has changed in terms of strengths and weaknesses. They have multiple independent results (drugs, RNAi and transcriptomics) that suggest a connection between fmo-4 and calcium regulation, but there is no strong evidence for what this connection is. The work still lacks direct measures of calcium, ER or mitochondrial function in relation to fmo-4 (which they acknowledge in the discussion). The first four sections strongly place fmo-4 within established longevity interventions, but their model doesn't explain how calcium regulation would fit into these.

Reviewer #1 (Public review):

Hüppe and colleagues had already developed an apparatus and an analytical approach to capture swimming activity rhythms in krill. In a previous manuscript they explained the system, and here they employ it to show a circadian clock, supplemented by exogenous light, produces an activity pattern consistent with "twilight" diel vertical migration (DVM; a peak at sunset, a midnight sink, and a peak in the latter half of the night).

They used light:dark (LD) followed by dark:dark (DD) photoperiods at two times of the year to confirm the circadian clock, coupled with DD experiments at four times of year to show rhythmicity occurs throughout the year along with DVM in the wild population. The individual activity data show variability in the rhythmic response, which is expected. However, their results showed rhythmicity was sustained in DD throughout the year, although the amplitude decayed quickly. The interpretation of a weak clock is reasonable, and they provide a convincing justification for the adaptive nature of such a clock in a species that has a wide distributional range and experiences various photic environments. These data also show that exogenous light increases the activity response and can explain the morning activity bouts, with the circadian clock explaining the evening and late-night bouts. This acknowledgement that vertical migration can be driven by multiple proximate mechanisms is important.

The work is rigorously done, and the interpretations are sound. I see no major weaknesses in the manuscript. Because a considerable amount of processing is required to extract and interpret the rhythmic signals (see Methods and previous AMAZE paper), it is informative to have the individual activity plots of krill as a gut check on the group data.

The manuscript will be useful to the field as it provides an elegant example of looking for biological rhythms in a marine planktonic organism and disentangling the exogenous response from the endogenous one. Furthermore, as high latitude environments change, understanding how important organisms like krill have the potential to respond will become increasingly important. This work provides a solid behavioral dataset to complement the earlier molecular data suggestive of a circadian clock in this species.

Reviewer #2 (Public review):

Summary:

This manuscript provides experimental evidence on circadian behavioural cycles in Antarctic krill. The krill were obtained directly from krill fishing vessels and the experiments were carried out on board using an advanced incubation device capable of recording activity levels over a number of days. A number of different experiments were carried out where krill were first exposed to simulated light:dark (L:D) regimes for some days followed by continuous darkness (DD). These were carried out on krill collected during late autumn and late summer. A further set of experiments was performed on krill across three different seasons (summer, autumn, winter), where incubations were all DD conditions. Activity was measured as the frequency by which an infrared beam close to the top of the incubation tube was broken over unit time. Results showed that patterns of increased and decreased activity that appeared synchronised to the LD cycle persisted during the DD period. This was interpreted as evidence of the operation of an internal (endogenous) clock. The amplitude of the behavioural cycles decreased with time in DD, which further suggests that this clock is relatively weak. The authors argued that the existence of a weak endogenous clock is an adaptation to life at high latitudes since allowing the clock to be modulated by external (exogenous) factors is an advantage when there is a high degree of seasonality. This hypothesis is further supported by seasonal DD experiments which showed that the periodicity of high and low activity levels differed between seasons.

Strengths

Although there has been a lot of field observations of various circadian type behaviour in Antarctic krill, relatively few experimental studies have been published considering this behaviour in terms of circadian patterns of activity. Krill are not a model organism and obtaining them and incubating them in suitable conditions are both difficult undertakings. Furthermore, there is a need to consider what their natural circadian rhythms are without the overinfluence of laboratory-induced artefacts. For this reason alone, the setup of the present study is ideal to consider this aspect of krill biology. Furthermore, the equipment developed for measuring levels of activity is well-designed and likely to minimise artefacts.

Weaknesses

I have little criticism of the rationale for carrying out this work, nor of the experimental design. Nevertheless, the manuscript would benefit from a clearer explanation of the experimental design, particularly aimed at readers not familiar with research into circadian rhythms. Furthermore, I have a more fundamental question about the relationship between levels of activity and DVM on which I will expand below. Finally, it was unclear how the observational results made here related to the molecular aspects considered in the Discussion.

(1) Explanation of experimental design - I acknowledge that the format of this particular journal insists that the Results are the first section that follows the Introduction. This nevertheless presents a problem for the reader since many of the concepts and terms that would generally be in the Methods are yet to be explained to the reader. Hence, right from the start of the Results section, the reader is thrown into the detail of what happened during the LD-DD experiments without being fully aware of why this type of experiment was carried out in the first place. Even after reading the Methods, further explanation would have been helpful. Circadian cycle type research of this sort often entrains organisms to certain light cycles and then takes the light away to see if the cycle continues in complete darkness, but this critical piece of knowledge does not come until much later (e.g. lines 369-372) leaving the reader guessing until this point why the authors took the approach they did. I would suggest the following (1) that more effort is made in the Introduction to explain the exact LD/DD protocols adopted (2) that a schematic figure is placed early on in the manuscript where the protocol is explained including some logical flow charts of e.g. if behavioural cycle continues in DD then internal clock exists versus if cycle does not continue in DD, the exogenous cues dominate - followed by - major decrease in cyclic amplitude = weak clock versus minor decrease = strong clock and so on

(2) Activity vs kinesis - in this study, we are shown data that (i) krill have a circadian cycle - incubation experiments; (ii) that krill swarms display DVM in this region - echosounder data (although see my later point). My question here is regarding the relationship between what is being measured by the incubation experiments and the in situ swarm behaviour observations. The incubation experiments are essentially measuring the propensity of krill to swim upwards since it logs the number of times an individual (or group) break a beam towards the top of the incubation tube. I argue that krill may be still highly active in the rest of the tube but just do not swim close to the surface, so this approach may not be a good measure of "activity". Otherwise, I suggest a more correct term of what is being measured is the level of "upward kinesis". As the authors themselves note, krill are negatively buoyant and must always be active to remain pelagic. What changes over the day-night cycle is whether they decide to expend that activity on swimming upwards, downwards or remaining at the same depth. Explaining the pattern as upward kinesis then also explains by swarms move upwards during the night. Just being more active at night may not necessarily result in them swimming upwards.

(3) Molecular relevance - Although I am interested in molecular clock aspects behind these circadian rhythms, it was not made clear how the results of the present study allow any further insight into this. In lines 282 to 284, the findings of the study by Biscontin et al (2017) are discussed with regard to how TIM protein is degraded by light via the clock photreceptor CRYTOCHROME 1. This element of the Discussion would be a lot more relevant if the results of the present study were considered in terms of whether they supported or refuted this or any other molecular clock model. As it stands, this paragraph is purely background knowledge and a candidate for deletion in the interest of shortening the Discussion.

Other aspects<br /> (i) 'Bimodal swimming' was used in the Abstract and later in the text without the term being fully explained. I could interpret it to mean a number of things so some explanation is required before the term is introduced.<br /> (ii) Midnight sinking - I was struck by Figure 2b with regards to the dip in activity after the initial ascent, as well as the rise in activity predawn. Cushing (1951) Biol Rev 26: 158-192 describes the different phases of a DVM common to a number of marine organisms observed in situ where there is a period of midnight sinking following the initial dusk ascent and a dawn rise prior to dawn descent. Tarling et al (2002) observe midnight sinking pattern in Calanus finmarchicus and consider whether it is a response to feeding satiation or predation avoidance (i.e. exogenous factors). Evidence from the present study indicates that midnight sinking (and potential dawn rise) behaviour could alternatively be under endogenous control to a greater or lesser degree. This is something that should certainly be mentioned in the Discussion, possibly in place of the molecular discussion element mentioned above - possibly adding to the paragraph Lines 303-319.

(iii) Lines 200-207 - I struggled to follow this argument regarding Piccolin et al identifying a 12 h rhythm whereas the present study indicates a ~24 h rhythm. Is one contradicting the other - please make this clear.

(iv) Although I agree that the hydroacoustic data should be included and is generally supportive of the results, I think that two further aspects should be made clear for context (a) whether there was any groundtruthing that the acoustic marks were indeed krill and not potentially some other group know to perform DVM such as myctophids (b) how representative were these patterns - I have a sense that they were heavily selected to show only ones with prominent DVM as opposed to other parts of the dataset where such a pattern was less clear - I am aware of a lot of krill research where DVM is not such a clear pattern and it is disingenuous to provide these patterns as the definitive way in which krill behaves. I ask this be made clear to the reader (note also that there is a suggestion of midnight sinking in Fig 5b on 28/2).

Reviewer #1 (Public review):

Summary:

The authors' research group had previously demonstrated the release of large multivesicular body-like structures by human colorectal cancer cells. This manuscript expands on their findings, revealing that this phenomenon is not exclusive to colorectal cancer cells but is also observed in various other cell types, including different cultured cell lines, as well as cells in the mouse kidney and liver. Furthermore, the authors argue that these large multivesicular body-like structures originate from intracellular amphisomes, which they term "amphiectosomes." These amphiectosomes release their intraluminal vesicles (ILVs) through a "torn-bag mechanism." Finally, the authors demonstrate that the ILVs of amphiectosomes are either LC3B positive or CD63 positive. This distinction implicates that the ILVs either originate from amphisomes or multivesicular bodies, respectively.

Strengths:

The manuscript reports a potential origin of extracellular vesicle (EV) biogenesis. The reported observations are intriguing.

Weaknesses:

In their revised version, the authors have addressed the majority of my criticisms. I have no further concerns regarding this manuscript.

Reviewer #2 (Public review):

Summary:

authors had previously identified that a colorectal cancer cell line generates small extracellular vesicles (sEVs) via a mechanism where a larger intracellular compartment containing these sEVs is secreted from the surface of the cell and then tears to release its contents. Previous studies had suggested that intraluminal vesicles (ILVs) inside endosomal multivesicular bodies and amphisomes can be secreted by fusion of the compartment with the plasma membrane. The 'torn bag mechanism' considered in this manuscript is distinctly different, because it involves initial budding off of a plasma membrane-enclosed compartment (called the amphiectosome in this manuscript, or MV-lEV). The authors successfully set out to investigate whether this mechanism is common to many cell types and to determine some of the subcellular processes involved.

The strengths of the study are:

(1) The high-quality imaging approaches used, including live-cell imaging and EN, which seem to show good examples of the proposed mechanism.<br /> (2) They screen several cell lines for these structures, also search for similar structures in vivo, and show the tearing process by real-time imaging.<br /> (3) Regarding the intracellular mechanisms of ILV production, the authors also try to demonstrate the different stages of amphiectosome production and differently labelled ILVs using immuno-EM.

Several of the techniques employed are technically challenging to do well, and so these are critical strengths of the manuscript.

Overall, I think the authors have been successful in identifying amphiectosomes secreted from multiple cell lines and cells in vivo, and in demonstrating that the ILVs inside them have at least two origins (autophagosome membrane and late endosomal multivesicular body) based on the markers that they carry. Inevitably, it remains unclear how universal this mechanism is in vivo and its overall contribution to EV function.<br /> I think there could be a significant impact on the EV field and consequently on our understanding of cell-cell signalling based on these findings. It will flag the importance of investigating the release of amphiectosomes in other studies, especially as the molecular mechanisms involved in this type of 'ectosomal-style' release will be different from multivesicular compartment fusion to the plasma membrane and should be possible to be manipulated independently.<br /> In general, the EV field has struggled to link up analysis of the subcellular biology of sEV secretion and the biochemical/physical analysis of the sEVs themselves, so from that perspective, the manuscript provides a novel angle on this problem.

Reviewer #2 (Public review):

Summary:

Here Vogt et al., provide new insights into the need for sleep and the molecular and physiological response to sleep loss. The authors expand on their previously published work (Bjorness et al., 2020) and draw from recent advances in the field to propose a neuron-centric molecular model for the accumulation and resolution of sleep need and basis of restorative sleep function. While speculative, the proposed model successfully links important observations in the field and provides a framework to stimulate further research and advances on the molecular basis of sleep function. In my review, I highlight the important advances of this current work, the clear merits of the proposed model, and indicate areas of the model that can serve to stimulate further investigation.

Strengths: Reviewer comment on new data in Vogt et al., 2024<br /> Using classic slice electrophysiology, the authors conclude that wakefulness (sleep deprivation (SD)) drives a potentiation of excitatory glutamate synapses, mediated in large part by "un-silencing" of NMDAR-active synapses to AMPAR-active synapses. Using a modern single nuclear RNAseq approach the authors conclude that SD drives changes in gene expression primarily occurring in glutamatergic neurons. The two experiments combined highlight the accumulation and resolution of sleep need centered on the strength of excitatory synapses onto excitatory neurons. This view is entirely consistent with a large body of extant and emerging literature and provides important direction for future research.

Consistent with prior work, wakefulness/SD drives an LTP-type potentiation of excitatory synaptic strength on principle cortical neurons. It has been proposed that LTP associated with wake, leads to the accumulation of sleep need by increasing neuronal excitability, and by the "saturation" of LTP capacity. This saturation subsequently impairs the capacity for further ongoing learning. This new data provides a satisfying mechanism of this saturation phenomenon by introducing the concept of silent synapses. The new data show that in mice well rested, a substantial number of synapses are "silent", containing an NMDAR component but not AMPARs. Silent synapses provide a type of reservoir for learning in that activity can drive the un-silencing, increasing the number of functional synapses. SD depletes this reservoir of silent synapses to essentially zero, explaining how SD can exhaust learning capacity. Recovery sleep led to restoration of silent synapses, explaining how recovery sleep can renew learning capacity. In their prior work (Bjorness et al., 2020) this group showed that SD drives an increase in mEPSC frequency onto these same cortical neurons, but without a clear change in pre-synaptic release probability, implying a change in the number of functional synapses. This prediction is now born out in this new dataset.

The new snRNAseq dataset indicates the sleep need is primarily seen (at the transcriptional level) in excitatory neurons, consistent with a number of other studies. First, this conclusion is corroborated by two independent, contemporary snRNAseq analysis recently published in iScience 2024 doi: 10.1016/j.isci.2024.110752 and Neuroscience Research 2024 https://doi.org/10.1016/j.neures.2024.03.004. A recently published analysis on the effects of SD in drosophila imaged synapses in every brain region in a cell-type dependent manner (Weiss et al., PNAS 2024), concluding that SD drives brain wide increases in synaptic strength almost exclusively in excitatory neurons. Further, Kim et al., Nature 2022, heavily cited in this work, show that the newly described SIK3-HDAC4/5 pathway promotes sleep depth via excitatory neurons and not inhibitory neurons.

The new experiments provided in Fig1-3 are expertly conducted and presented. This reviewer has no comments of concern regarding the execution and conclusions of these experiments.

Reviewer comment on model in Vogt et al., 2024

To the view of this reviewer the new model proposed by Vogt et al., is an important contribution. The model is not definitively supported by new data, and in this regard should be viewed as a perspective, providing mechanistic links between recent molecular advances, while still leaving areas that need to be addressed in future work. New snRNAseq analysis indicates SD drives expression of synaptic shaping components (SSCs) consistent with the excitatory synapse as a major target for the restorative basis of sleep function. SD induced gene expression is also enriched for autism spectrum disorder (ASD) risk genes. As pointed out by the authors, sleep problems are commonly reported in ASD, but the emphasis has been on sleep amount. This new analysis highlights the need to understand the impact on sleep's functional output (synapses) to fully understand the role of sleep problems in ASD.

Importantly, SD induced gene expression in excitatory neurons overlap with genes regulated by the transcription factor MEF2C and HDAC4/5 (Fig. 4). In their prior work, the authors show loss of MEF2C in excitatory neurons abolished the SD transcriptional response and the functional recovery of synapses from SD by recovery sleep. Recent advances identified HDAC4/5 as major regulators of sleep depth and duration (in excitatory neurons) downstream of the recently identified sleep promoting kinase SIK3. In Zhou et al., and Kim et al., Nature 2022, both groups propose a model whereby "sleep-need" signals from the synapse activate SIK3, which phosphorylates HDAC4/5, driving cytoplasmic targeting, allowing for the de-repression and transcriptional activation of "sleep genes". Prior work shows that HDAC4/5 are repressors of MEF2C. Therefore, the "sleep genes" derepressed by HDAC4/5 may be the same genes activated in response to SD by MEF2C. The new model thereby extends the signaling of sleep need at synapses (through SIK3-HDAC4/5) to the functional output of synaptic recovery by expression of synaptic/sleep genes by MEF2C. The model thereby links aspects of expression of sleep need with the resolution of sleep need by mediating sleep function: synapse renormalization.

Weaknesses:

Areas for further investigation.<br /> In the discussion section Vogt et al., explore the links between excitatory synapse strength, arguably the major target of "sleep function", and NREM slow-wave activity (SWA), the most established marker of sleep need. SIK3-HDAC4/5 have major effects on the "depth" of sleep by regulation NREM-SWA. The effects of MEF2C loss of function on NREM SWA activity are less obvious, but clearly impact the recovery of glutamatergic synapses from SD. The authors point out how adenosine signaling is well established as a mediator of SWA, but the links with adenosine and glutamatergic strength are far from clear. The mechanistic links between SIK3/HDAC4/5, adenosine signaling, and MEF2C, are far from understood. Therefore, the molecular/mechanistic links between a synaptic basis of sleep need and resolution with NREM-SWA activity requires further investigation.

Additional work is also needed to understand the mechanistic links between SIK3-HDAC4/5 signaling and MEF2C activity. The authors point out that constitutively nuclear (cn) HDAC4/5 (acting as a repressor) will mimic MEF2C loss of function. This is reasonable, however, there are notable differences in the reported phenotypes of each. Notably, cnHDAC4/5 suppresses NREM amount and NREM SWA but had no effect on the NREM-SWA increase following SD (Zhou et al., Nature 2022). Loss of MEF2C in CaMKII neurons had no effect on NREM amount and suppressed the increase in NREM-SWA following SD (Bjorness et al., 2020). These instances indicate that cnHDAC4/5 and loss of MEF2C do not exactly match suggesting additional factors are relevant in these phenotypes. Likely HDAC4/5 have functionally important interactions with other transcription factors, and likewise for MEF2C, suggesting areas for future analysis.

One emerging theme may be that the SIK3-HDAC4/5 axis are major regulators of the sleep state, perhaps stabilizing the NREM state once the transition from wakefulness occurs. MEF2C is less involved in regulating sleep per se, and more involved in executing sleep function, by promoting the restorative synaptic modifications to resolve sleep need.

Finally, advances in the roles of the respective SIK3-HDAC4/5 and MEF2C pathways point towards transcription of "sleep genes", as clearly indicated in the model of Fig.4. Clearly more work is needed to understand how the expression of such genes ultimately lead to resolution of sleep need by functional changes at synapses. What are these sleep genes and how do they mechanistically resolve sleep need? Thus, the current work provides a mechanistic framework to stimulate further advances in understanding the molecular basis for sleep need and the restorative basis of sleep function.

Comments on revisions:

No further comments or concerns. I believe that the manuscript has been suitably revised, and the concerns raised by reviewers have been addressed. I am completely satisfied by the revisions and responses provided by the authors.

Reviewer #1 (Public review):

The study by Aguirre-Botero et al. shows the dynamics of 3D11 anti-CSP monoclonal antibody (mAb) mediated elimination of rodent malaria Plasmodium berghei (Pb) parasites in the liver. The authors show that the anti-CSP mAb could protect against intravenous (i.v.) Pb sporozoite challenge along with the cutaneous challenge, but requires higher concentration of antibody. Importantly, the study shows that the anti-CSP mAb not only affects sporozoite motility, sinusoidal extravasation, and cell invasion but also partially impairs the intracellular development inside the liver parenchyma, indicating a late effect of this antibody during liver stage development. While the study is interesting and conducted well, the only novel yet very important observation made in this manuscript is the effect of the anti-CSP mAb on liver stage development.

Comments on latest version:

No further comments.

Reviewer #1 (Public review):

The study by Aguirre-Botero et al. shows the dynamics of 3D11 anti-CSP monoclonal antibody (mAb) mediated elimination of rodent malaria Plasmodium berghei (Pb) parasites in the liver. The authors show that the anti-CSP mAb could protect against intravenous (i.v.) Pb sporozoite challenge along with the cutaneous challenge, but requires higher concentration of antibody. Importantly, the study shows that the anti-CSP mAb not only affects sporozoite motility, sinusoidal extravasation, and cell invasion but also partially impairs the intracellular development inside the liver parenchyma, indicating a late effect of this antibody during liver stage development. While the study is interesting and conducted well, the only novel yet very important observation made in this manuscript is the effect of the anti-CSP mAb on liver stage development.

Comments on latest version:

No further comments.

Reviewer #3 (Public review):

Summary:

Aguirre-Botero et al have studied the effect of a potent monoclonal antibody against the circumsporozoite protein, the major surface protein of the malaria sporozoite. This is an elegantly designed, performed, and analyzed study. They have efficiently delineated the mode of action of anti-CSP repeat mAb and confirmed previous in vitro work (not cited) that demonstrated the same intracellular effect.

Major comments from the previous round of review:

Line 51: The authors claim a correlation between high antibody levels and protection. However, they did not provide direct proof that these antibodies were responsible for protection, nor did they establish a cut-off level of anti-CSP antibodies that would distinguish between protected and unprotected individuals.

Line 326: The late intrahepatic effect of mAb against the CSP repeat has been previously reported (see Figure 2, Nudelman et al, J Immunol, 1989). The effect was shown to affect the transition from liver trophozoites to liver schizonts. This study should be cited and discussed.

Significance:

A well-done study that elucidates the mechanisms of a protective monoclonal antibody against malaria sporozoites. These data are important and will interest a large audience of researchers working in infectious diseases and immunology.

Comments on latest version:

With the addition of new experiments and proper addition of missing references and minor text correction, the manuscript has been improved.

Reviewer #1 (Public review):

Summary:

This manuscript by Kaya et al. studies the effect of food consumption on hippocampal sharp wave ripples (SWRs) in mice. The authors use multiple foods and forms of food delivery to show that the frequency and power of SWRs increase following food intake, and that this effect depends on the caloric content of food. The authors also studied the effects of the administration of various food-intake-related hormones on SWRs during sleep, demonstrating that ghrelin negatively affects SWR rate and power, but not GLP-1, insulin, or leptin. Finally, the authors use fiber photometry to show that GABAergic neurons in the lateral hypothalamus, increase activity during a SWR event.

Strengths:

The experiments in this study seem to be well performed, and the data are well presented, visually. The data support the main conclusions of the manuscript that food intake enhances hippocampal SWRs. Taken together, this study is likely to be impactful to the study of the impact of feeding on sleep behavior, as well as the phenomena of hippocampal SWRs in metabolism.

Weaknesses:

Details of experiments are missing in the text and figure legends. Additionally, the writing of the manuscript could be improved.

Reviewer #2 (Public review):

Summary:

Kaya et al uncover an intriguing relationship between hippocampal sharp wave-ripple production and peripheral hormone exposure, food intake, and lateral hypothalamic function. These findings significantly expand our understanding of hippocampal function beyond mnemonic processes and point a direction for promising future research.

Strengths:

Some of the relationships observed in this paper are highly significant. In particular, the inverse relationship between GLP1/Leptin and Insulin/Ghrelin are particularly compelling as this aligns well with opposing hormone functions on satiety.

Weaknesses: I would be curious if there were any measurable behavioral differences that occur with different hormone manipulations.

Reviewer #3 (Public review):

Summary:

The manuscript by Kaya et al. explores the effects of feeding on sharp wave-ripples (SWRs) in the hippocampus, which could reveal a better understanding of how metabolism is regulated by neural processes. Expanding on prior work that showed that SWRs trigger a decrease in peripheral glucose levels, the authors further tested the relationship between SWRs and meal consumption by recording LFPs from the dorsal CA1 region of the hippocampus before and after meal consumption. They found an increase in SWR magnitude during sleep after food intake, in both food restricted and ad libitum fed conditions. Using fiber photometry to detect GABAergic neuron activity in the lateral hypothalamus, they found increased activity locked to the onset of SWRs. They conclude that the animal's satiety state modulates the amplitude and rate of SWRs, and that SWRs modulate downstream circuits involved in regulating feeding. These experiments provide an important step forward in understanding how metabolism is regulated in the brain. However, currently, the paper lacks sufficient analyses to control for factors related to sleep quality and duration; adding these analyses would further support the claim that food intake itself, as opposed to sleep quality, is primarily responsible for changes in SWR activity. Adding this, along with some minor clarifications and edits, would lead to a compelling case for SWRs being modulated by a satiety state. The study will likely be of great interest in the field of learning and memory while carrying broader implications for understanding brain-body physiology.

Strengths:

The paper makes an innovative foray into the emerging field of brain-body research, asking how sharp wave-ripples are affected by metabolism and hunger. The authors use a variety of advanced techniques including LFP recordings and fiber photometry to answer this question. Additionally, they perform comprehensive and logical follow-up experiments to the initial food-restricted paradigm to account for deeper sleep following meal times and the difference between consumption of calories versus the experience of eating. These experiments lay the groundwork for future studies in this field, as the authors pose several follow-up questions regarding the role of metabolic hormones and downstream brain regions.

Weaknesses:

Major comments:

(1) The authors conclude that food intake regulates SWR power during sleep beyond the effect of food intake on sleep quality. Specifically, they made an attempt to control for the confounding effect of delta power on SWRs through a mediation analysis. However, a similar analysis is not presented for SWR rate. Moreover, this does not seem to be a sufficient control. One alternative way to address this confound would be to subsample the sleep data from the ad lib and food restricted conditions (or high calorie and low calorie, etc), to match the delta power in each condition. When periods of similar mean delta power (i.e. similar sleep quality) are matched between datasets, the authors can then determine if a significant effect on SWR amplitude and rate remains in the subsampled data.

(2) Relatedly, are the animals spending the same amount of time sleeping in the ad lib vs. food restricted conditions? The amount of time spent sleeping could affect the probability of entering certain stages of sleep and thus affect SWR properties. A recent paper (Giri et al., Nature, 2024) demonstrated that sleep deprivation can alter the magnitude and frequency of SWRs. Could the authors quantify sleep quantity and control for the amount of time spent sleeping by subsampling the data, similar to the suggestion above?

(3) Plot 5I only reports significance but does not clearly show the underlying quantification of LH GABAergic activity. Upon reading the methods for how this analysis was conducted, it would be informative to see a plot of the pre-SWR and post-SWR integral values used for the paired t-test whose p-values are currently shown. For example, these values could be displayed as individual points overlaid on a pair of box-and-whisker plots of the pre- and post-distribution within the session (perhaps for one example session per mouse with the p-value reported, to supplement a plot of the distribution of p-values across sessions and mice). If these data are non-normal, the authors should also use a non-parametric statistical test.

Minor comments:

(4) A brief explanation (perhaps in the discussion) of what each change in SWR property (magnitude, rate, duration) could indicate in the context of the hypothesis may be helpful in bridging the fields of metabolism and memory. For example, by describing the hypothesized mechanistic consequence of each change, could the authors speculate on why ripple rate may not increase in all the instances where ripple power increases after feeding? Why do the authors speculate that ripple duration does not increase, given that prior work (Fernandez-Ruiz et al. 2019) has shown that prolonged ripples support enhanced memory?

(5) The authors suggest that "SWRs could modulate peripheral metabolism" as a future implication of their work. However, the lack of clear effects from GLP-1, leptin and insulin complicates this interpretation. It might be informative for readers if the authors expanded their discussion of what specific role they speculate that SWRs could play in regulating metabolism, given these negative results.

Reviewer #1 (Public review):

Summary:

In this manuscript, the authors identified that<br /> (1) CDK4/6i treatment attenuates the growth of drug-resistant cells by prolongation of the G1 phase;<br /> (2) CDK4/6i treatment results in an ineffective Rb inactivation pathway and suppresses the growth of drug-resistant tumors;<br /> (3) Addition of endocrine therapy augments the efficacy of CDK4/6i maintenance;<br /> (4) Addition of CDK2i with CDK4/6 treatment as second-line treatment can suppress the growth of resistant cell;<br /> (5) The role of cyclin E as a key driver of resistance to CDK4/6 and CDK2 inhibition.

Strengths:

To prove their complicated proposal, the authors employed orchestration of several kinds of live cell markers, timed in situ hybridization, IF and Immunoblotting. The authors strongly recognize the resistance of CDK4/6 + ET therapy and demonstrated how to overcome it.

Weaknesses:

The authors need to underscore their proposed results from what is to be achieved by them and by other researchers.

Reviewer #2 (Public review):

Summary:

This study elucidated the mechanism underlying drug resistance induced by CDK4/6i as a single agent and proposed a novel and efficacious second-line therapeutic strategy. It highlighted the potential of combining CDK2i with CDK4/6i for the treatment of HR+/HER2- breast cancer.

Strengths:

The study demonstrated that CDK4/6 induces drug resistance by impairing Rb activation, which results in diminished E2F activity and a delay in G1 phase progression. It suggests that the synergistic use of CDK2i and CDK4/6i may represent a promising second-line treatment approach. Addressing critical clinical challenges, this study holds substantial practical implications.

Weaknesses:

(1) Drug-resistant cell lines: Was a drug concentration gradient treatment employed to establish drug-resistant cell lines? If affirmative, this methodology should be detailed in the materials and methods section.

(2) What rationale informed the selection of MCF-7 cells for the generation of CDK6 knockout cell lines? Supplementary Figure 3. A indicates that CDK6 expression levels in MCF-7 cells are not notably elevated.

(3) For each experiment, particularly those involving mice, the author must specify the number of individuals utilized and the number of replicates conducted, as detailed in the materials and methods section.

(4) Could this treatment approach be extended to triple-negative breast cancer?

Reviewer #3 (Public review):

Summary:

In their manuscript, Armand and colleagues investigate the potential of continuing CDK4/6 inhibitors or combining them with CDK2 inhibitors in the treatment of breast cancer that has developed resistance to initial therapy. Utilizing cellular and animal models, the research examines whether maintaining CDK4/6 inhibition or adding CDK2 inhibitors can effectively control tumor growth after resistance has set in. The key findings from the study indicate that the sustained use of CDK4/6 inhibitors can slow down the proliferation of cancer cells that have become resistant, and the combination of CDK2 inhibitors with CDK4/6 inhibitors can further enhance the suppression of tumor growth. Additionally, the study identifies that high levels of Cyclin E play a significant role in resistance to the combined therapy. These results suggest that continuing CDK4/6 inhibitors along with the strategic use of CDK2 inhibitors could be an effective strategy to overcome treatment resistance in hormone receptor-positive breast cancer.

Strengths:

(1) Continuous CDK4/6 Inhibitor Treatment Significantly Suppresses the Growth of Drug-Resistant HR+ Breast Cancer: The study demonstrates that the continued use of CDK4/6 inhibitors, even after disease progression, can significantly inhibit the growth of drug-resistant breast cancer.

(2) Potential of Combined Use of CDK2 Inhibitors with CDK4/6 Inhibitors: The research highlights the potential of combining CDK2 inhibitors with CDK4/6 inhibitors to effectively suppress CDK2 activity and overcome drug resistance.

(3) Discovery of Cyclin E Overexpression as a Key Driver: The study identifies overexpression of cyclin E as a key driver of resistance to the combination of CDK4/6 and CDK2 inhibitors, providing insights for future cancer treatments.

(4) Consistency of In Vitro and In Vivo Experimental Results: The study obtained supportive results from both in vitro cell experiments and in vivo tumor models, enhancing the reliability of the research.

(5) Validation with Multiple Cell Lines: The research utilized multiple HR+/HER2- breast cancer cell lines (such as MCF-7, T47D, CAMA-1) and triple-negative breast cancer cell lines (such as MDA-MB-231), validating the broad applicability of the results.

Weaknesses:

(1) The manuscript presents intriguing findings on the sustained use of CDK4/6 inhibitors and the potential incorporation of CDK2 inhibitors in breast cancer treatment. However, I would appreciate a more detailed discussion of how these findings could be translated into clinical practice, particularly regarding the management of patients with drug-resistant breast cancer.

(2) While the emergence of resistance is acknowledged, the manuscript could benefit from a deeper exploration of the molecular mechanisms underlying resistance development. A more thorough understanding of how CDK2 inhibitors may overcome this resistance would be valuable.

(3) The manuscript supports the continued use of CDK4/6 inhibitors, but it lacks a discussion on the long-term efficacy and safety of this approach. Additional studies or data to support the safety profile of prolonged CDK4/6 inhibitor use would strengthen the manuscript.

Reviewer #1 (Public review):

Summary:

The authors study the effect of the addition of synthetic amphiphile on the gating mechanisms of the mechano-sensitive channel MscL. They observe that the amphiphile reduces the membrane stretching and bending modulii, and increases the channel activation pressure. They then conclude that gating is sensitive to these two membrane parameters. This is explained by the effect of the amphiphile on the so-called membrane interfacial tension.

Strengths:

The major strength is that the authors found a way to tune the membrane's mechanical properties in a controlled manner, and find a progressive change of the suction pressure at which MscL gates. If analysed thoroughly, these results could give valuable information.

Weaknesses:

The weakness is the analysis and the discussion. I would like to have answers to some basic questions.

(1) The explanation of the phenomenon involves a difference between interfacial tension and tension, without the difference between these being precisely defined. In the caption of Figure 4, one can read "Under tension, the PEO groups adsorb to the bilayer, suggesting adsorption is a thermodynamically favorable process that lowers the interfacial tension." What does this mean? Under what tension is the interfacial tension lowered? The fact that the system's free energy could be lowered by putting it under mechanical tension would result in a thermodynamic unstable situation. Is this what the authors mean?

(2) From what I understand, a channel would feel the tension exerted by the membrane at its periphery, which is what I would call membrane tension. The fact that polymers may reorganise under membrane stretch to lower the system's free energy would certainly affect the membrane stretching modulus (as measured Figure 2E), but what the channel cares about is the tension (I would say). If the membrane is softer, a larger pipette pressure is required to reach the same level of tension, so it is not surprising that a given channel requires a larger activation pressure in softer membranes. To me, this doesn't mean that the channel feels the membrane stiffness, but rather that a given pressure leads to different tensions (which is what the channel feels) for different stiffnesses.

(3) In order to support the authors' claim, the micropipette suction pressure should be appropriately translated into a membrane tension. One would then see whether the gating tension is affected by the presence of amphiphiles. In the micropipette setup used here, one can derive a relationship between pressure and tension, that involves the shape of the membrane. This relationship is simple (tension=pressure difference times pipette radius divided by 2) only in the limit where the membrane tongue inside the pipette ends with a hemisphere of constant radius independent of the pressure, and the pipette radius is much smaller than the GUV radius. None of these conditions seem to hold in Figure 2C. On the other hand, the authors do report absolute values of tension in the y-axis of Figure 2D. It seems quite straightforward to plot the activation tension (rather than pressure) as a function of the amphiphile volume fraction in Figure 2B. This is what needs to be shown.

(4) The discussion needs to be improved. I could not find a convincing explanation of the role of interfacial tension in the discussion. The equation (p.14) distinguishes three contributions, which I understand to be (i) an elastic membrane deformation such as hydrophobic mismatch or other short-range effects, (ii) the protein conformation energy, and (iii) the work done by membrane tension. Apparently, the latter is where the effect is (which I agree with), but how this consideration leads to a gating energy difference (between lipid only and modified membrane) proportional to the interfacial tension is completely obscure (if not wrong).

(5) I am rather surprised at the very small values of stretching and bending modulii found under high-volume fraction. These quantities are obtained by fitting the stress-strain relationship (Figure 2D). Such a plot should be shown for all amphiphile volume fraction, so one can assess the quality of the fits.

Reviewer #2 (Public review):

Summary:

The manuscript describes how synthetic polymers, primarily poloxamers of different sizes, influence bacterial mechanosensitive channel MscL gating by modifying the interfacial tension of the membrane. The authors expressed MscL in U2OS cells and chemically blebbed the cells to derive giant plasma membrane vesicles (GPMVs) containing MscL G22S. They applied micropipette aspiration on GPMVs to obtain bending rigidity (kc) and area expansion modulus (kA) and used patch clamping to obtain activation pressure. They found a negative correlation between kc and kA with activation pressure and attributed the changes to activation pressure to the lowering of the interfacial tension in the presence of polymers. They carried out coarse-grain molecular dynamics simulations and showed that under tension the hydrophilic PEO group adsorbs to the bilayer more, thereby lowering the interfacial tension. Besides MscL, they showed similar results with TREK-1 activation. The conclusion that differences in interfacial tension are what drive the changes in activation pressure is based on using a thermodynamic model.

Strengths:

(1) Reveals that synthetic polymer that lowers bending rigidity and area expansion modulus increases activation pressure of mechanosensitive channel by lowering interfacial tension - this is an important finding.

(2) General data quality is high with detailed and thorough analysis. The use of both micropipette aspiration and patch clamp in the same study is noteworthy.

(3) Discussion on nanoplastics and their effect on membrane properties and therefore their impact on mechanosensitivity is interesting.

Weaknesses:

Interfacial tension is not experimentally measured. Given the main argument of this paper is that synthetic polymers reduce interfacial tension, which increases MS channel activation pressure, it would be prudent to show experimental measurements to bolster their analysis.

Reviewer #3 (Public review):

Summary:

In this manuscript, the authors set out to test the "force from lipids" mechanism of mechanosensitive channel gating, which posits that mechanical properties of the membrane are directly responsible for converting membrane tension into useful energy for channel gating. They employ amphiphilic polymers called poloxamers to alter membrane mechanical properties and relate those to the threshold of mechanical activation of the MscL channel of E.coli.

The authors heterologously express the channel, perform electrical recordings, and assess the mechanical properties of vesicles derived from the same membranes. This allows them to directly compare derived mechanical parameters to channel gating in the same environment.

They further repeat experiments in an eukaryotic mechano-channel and show that the same principles apply to gating in this very different protein, providing support for the force from lipids hypothesis.

Strengths:

In this work, characterization of the mechanical properties of the plasma membrane and electrical recordings of channel activity are carried out in membranes derived from the same cells. This is a nice contribution to these experiments since usually these two properties are measured in separate membranes with differing compositions. The experiments are of high quality and the data analysis and interpretation are careful.

Weaknesses:

It is not clear to this reviewer what the relationship is between the mechanical properties the authors measure, the membrane area expansion modulus, and bending rigidity, to what they call "interfacial tension".

Reviewer #1 (Public review):

Summary

In this manuscript, the authors generate an AAV-deliverable tool that generates action potentials in response to red light, but not blue light, when expressed in neurons. To do this, they screen some red light-excitatory/blue light-inhibitory opsin pairs to find ones that are spectrally and temporally matched. They first show that this works with Chrimson and GtACR2, however, they expand their search after finding that the tau-off (inactivation after light cessation) kinetics of these two opsins are not well-matched. They directly examine a small set of options based on a literature search and settle on a variant of red light-excitatory Chrimson and blue light-inhibitory ZipACR. To even more closely match the kinetics of this pair, the authors create a structure homology model of the ZipACR retinal binding pocket and use this to guide generation of a small mutant panel, leading to a more optimized ZipACR mutant. They then show that a bicistronically expressed fusion arrangement of these opsins, plus some functional peptides, can drive action potentials up to 20hz with red light and does not do so with blue light, in hippocampal cells transduced by AAV. They also show function in vivo, in a mouse, using a physiological readout. They conclude that their new tool may be useful for complex experimental designs requiring multiple optical channels for write-in/read-out.

The major advantage claimed by the authors over existing tools is the temporal time-locking of their inhibitory opsin - this is driven by the contrast between tau-off kinetics of their ZipACR variant compared to gtACR2, which is used by the leading competitor tool (BiPOLES).

Big thoughts<br /> While the authors were carefully thoughtful about the potential influence of temporal kinetics on the efficiency of a tool such as this one, there were no experiments conducted that make use of the unique properties of this molecular strategy (although the authors state that these experiments are now underway in their lab). They share some examples of how the tool could be useful in the discussion. Where do I think this could be useful?

First, experimental designs that require multiple optical channels of control. This appears to be aligned with the author's thoughts, as they state, correctly, that opsins utilizing retinal as a light-sensing chromophore are universally activated by blue light (the so-called 'blue shoulder'). Therefore, their tool may be useful for stimulating multiple populations using a blue excitatory opsin in neuron A and their tool for red excitation of neuron B - or, in the author's own words, "A potential solution to the problem of cross-talk...". In this manuscript, the authors provide state that there this is possible in theory and that there are no obvious reasons that it would not work, but do not present data that showcases their new tool for this purpose (e.g. Vierock, Johannes, et al. "BiPOLES is an optogenetic tool developed for bidirectional dual-color control of neurons." Nature communications 12.1 (2021): 4527. Figure 4f-I; 6). The same set-up could be imagined for green GECI (or equivalent) imaging of cells in the same volume that their tool is being used in - for instance, interleaving red stimulation light and blue imaging light, (perhaps) without the typical concern of imaging light bleed-through activating the opsin itself. I agree that it will likely work for multi-channel control, but only time will tell, at this point.

Second, for high-frequency temporal control over both excitation and inhibition in the same neuron. Red light turns the cell on, and blue light turns the cell off (see, for instance, Zhang, Feng, et al. "Multimodal fast optical interrogation of neural circuitry." Nature 446.7136 (2007): 633-639. Figure 2; Vierock as above, Figure 4a,b). Again, here the authors are long on theory ("The new system...can drive time-locked high-frequency action potentials in response to red pulses") and short on explicit data. While they do show that red light = excitation and blue light = inhibition, they neither show 1) all-optical on/off modulation of the same cell; nor 2) high-frequency inhibition or excitation (max stim rate of 20hz, which is the same as the BiPOLES paper used for their LC stimulation paradigm; Vierock, as above, Figure 7a-d). They did provide a response to this critique that data showing excitation and inhibition spread across multiple panels were largely collected from the same cells.

Despite these major shortcomings, the further development and characterization of tandem opsins, such as this one, is of interest to the community. There is on-going work by the BiPOLES team to create new iterations (e.g. Wahid, J., et al. "P-15 BiPOLES2 is a bidirectional optogenetic tool with a narrow activation spectrum and low red-light excitability." Clinical Neurophysiology 148 (2023): e16.). The authors have collected a substantial amount of additional data along the course of review and, even aside from the final tool, the overall data and approaches shown are useful.

Reviewer #1 (Public review):

Summary:

Audio et al. measured cerebral blood volume (CBV) across cortical areas and layers using high-resolution MRI with contrast agents in non-human primates. While the non-invasive CBV MRI methodology is often used to enhance fMRI sensitivity in NHPs, its application for baseline CBV measurement is rare due to the complexities of susceptibility contrast mechanisms. The authors determined the number of large vessels and the areal and laminar variations of CBV in NHP, and compared those with various other metrics.

Strengths:

Noninvasive mapping of relative cerebral blood volume is novel for non-human primates. A key finding was the observation of variations in CBV across regions; primary sensory cortices had high CBV, whereas other higher areas had low CBV. The measured CBV values correlated with previously reported neuronal and receptor densities.

Weaknesses:

A weakness of this manuscript is that the quantification of CBV with postprocessing approaches to remove susceptibility effects from pial and penetrating vessels is not fully validated, especially on a laminar scale. Further specific comments follow.

(1) Baseline CBV indices were determined using contrast agent-enhanced MRI (deltaR2*). Although this approach is suitable for areal comparisons, its application at a laminar scale poses challenges due to significant contributions from large vessels including pial vessels. The primary concern is whether large-vessel contributions can be removed from the measured deltaR2* through processing techniques.

(2) High-resolution MRI with a critical sampling frequency estimated from previous studies (Weber 2008, Zheng 1991) was performed to separate penetrating vessels. However, this approach is still insufficient to accurately identify the number of vessels due to the blooming effects of susceptibility and insufficient spatial resolution. The reported number of penetrating vessels is only applicable to the experimental and processing conditions used in this study, which cannot be generalized.

(3) Baseline R2* is sensitive to baseline R2, vascular volume, iron content, and susceptibility gradients. Additionally, it is sensitive to imaging parameters; higher spatial resolution tends to result in lower R2* values (closer to the R2 value). Thus, it is difficult to correlate baseline R2* with physiological parameters.

(4) CBV-weighted deltaR2* is correlated with various other metrics (cytoarchitectural parcellation, myelin/receptor density, cortical thickness, CO, cell-type specificity, etc.). While testing the correlation between deltaR2* and these other metrics may be acceptable as an exploratory analysis, it is challenging for readers to discern a causal relationship between them. A critical question is whether CBV-weighted deltaR2* can provide insights into other metrics in diseased or abnormal brain states.

Reviewer #2 (Public review):

Summary:

This manuscript presents a new approach for non-invasive, MRI-based, measurements of cerebral blood volume (CBV). Here, the authors use ferumoxytol, a high-contrast agent and apply specific sequences to infer CBV. The authors then move to statistically compare measured regional CBV with known distribution of different types of neurons, markers of metabolic load and others. While the presented methodology captures and estimated 30% of the vasculature, the authors corroborated previous findings regarding lack of vascular compartmentalization around functional neuronal units in the primary visual cortex.

Strengths:

Non invasive methodology geared to map vascular properties in vivo.

Implementation of a highly sensitive approach for measuring blood volume.

Ability to map vascular structural and functional vascular metrics to other types of published data.

Weaknesses:

The key issue here is the underlying assumption about the appropriate spatial sampling frequency needed to captures the architecture of the brain vasculature. Namely, ~7 penetrating vessels / mm2 as derived from Weber et al 2008 (Cer Cor). The cited work, begins by characterizing the spacing of penetrating arteries and ascending veins using vascular cast of 7 monkeys (Macaca mulatta, same as in the current paper). The ~7 penetrating vessels / mm2 is computed by dividing the total number of identified vessels by the area imaged. The problem here is that all measurements were made in a "non-volumetric" manner and only in V1. Extrapolating from here to the entire brain seems like an over-assumption, particularly given the region-dependent heterogeneity that the current paper reports.

Comments on revisions:

I appreciate the effort made to improve the manuscript. That said, the direct validation of the underlying assumption about spatial resolution sampling remains unaddressed in the final version of this manuscript. With the only intention to further strengthen the methodology presented here, I would encourage again the authors to seek a direct validation of this assumption for other brain areas.

In their reply, the authors stated "... line scanning or single-plane sequences, at least on first impression, seem inadequate for whole-brain coverage and cortical surface mapping. ". This seems to emanate for a misunderstanding as the method could be used to validate the mapping, not to map per-se.

Reviewer #1 (Public review):

Summary:

Boldt et al test several possible relationships between trandiagnostically-defined compulsivity and cognitive offloading in a large online sample. To do so, they develop a new and useful cognitive task to jointly estimate biases in confidence and reminder-setting. In doing so, they find that over-confidence is related to less utilization of reminder-setting, which partially mediates the negative relationship between compulsivity and lower reminder-setting. The paper thus establishes that, contrary to the over-use of checking behaviors in patients with OCD, greater levels of transdiagnostically-defined compulsivity predicts less deployment of cognitive offloading. The authors offer speculative reasons as to why (perhaps it's perfectionism in less clinically-severe presentations that lowers the cost of expending memory resources), and sets an agenda to understand the divergence in cognitive between clinical and nonclinical samples. Because only a partial mediation had robust evidence, multiple effects may be at play, whereby compulsivity impacts cognitive offloading via overconfidence and also by other causal pathways.

Strengths:

The study develops an easy-to-implement task to jointly measure confidence and replicates several major findings on confidence and cognitive offloading. The study uses a useful measure of cognitive offloading - the tendency to set reminders to augment accuracy in the presence of experimentally manipulated costs. Moreover, the utilizes multiple measures of presumed biases -- overall tendency to set reminders, the empirically estimated indifference point at which people engage reminders, and a bias measure that compares optimal indifference points to engage reminders relative to the empirically observed indifference points. That the study observes convergenence along all these measures strengthens the inferences made relating compulsivity to the under-use of reminder-setting. Lastly, the study does find evidence for one of several a priori hypotheses and sets a compelling agenda to try to explain why such a finding diverges from an ostensible opposing finding in clinical OCD samples and the over-use of cognitive offloading.

Weaknesses:

Although I think this design and study are very helpful for the field, I felt that a feature of the design might reduce the tasks's sensitivity to measuring dispositional tendencies to engage cognitive offloading. In particular, the design introduces prediction errors, that could induce learning and interfere with natural tendencies to deploy reminder-setting behavior. These PEs comprise whether a given selected strategy will be or not be allowed to be engaged. We know individuals with compulsivity can learn even when instructed not to learn (e.g., Sharp, Dolan and Eldar, 2021, Psychological Medicine), and that more generally, they have trouble with structure knowledge (eg Seow et al; Fradkin et al), and thus might be sensitive to these PEs. Thus, a dispositional tendency to set reminders might be differentially impacted for those with compulsivity after an NPE, where they want to set a reminder, but aren't allowed to. After such an NPE, they may avoid moreso the tendency to set reminders. Those with compulsivity likely have superstitious beliefs about how checking behaviors lead to a resolution of catastrophes, that might in part originate from inferring structure in the presence of noise or from purely irrelevant sources of information for a given decision problem.<br /> It would be good to know if such learning effects exist, if they're modulated by PE (you can imagine PEs are higher if you are more incentivized - e.g., 9 points as opposed to only 3 points - to use reminders, and you are told you cannot use them), and if this learning effect confounds the relationship between compulsivity and reminder-setting.

A more subtle point, I think this study can be more said to be an exploration than a deductive of test of a particular model -> hypothesis -> experiment. Typically, when we test a hypothesis, we contrast it with competing models. Here, the tests were two-sided because multiple models, with mutually exclusive predictions (over-use or under-use of reminders) were tested. Moreover, it's unclear exactly how to make sense of what is called the direct mechanism, which is supported by the partial (as opposed to complete) mediation.

Reviewer #2 (Public review):

Summary:

Boldt et al., investigated whether previously established relationships between transdiagnostic psychiatric symptom dimensions and confidence distortions would result in downstream influences on the confidence-related behaviour of reminder setting. 600 individuals from the general population completed a battery of psychiatric symptom questionnaires and an online reminder-setting task. In line with previous studies, individuals high in compulsivity (CIT) showed over-confidence in their task performance, whereas individuals high in anxious-depression (AD) tended to be under-confident. Crucially, the over-confidence associated with CIT partially mediated a decreased tendency to use external reminders during task performance, whereas the under-confidence associated with AD did not result in any alteration in external reminder setting. The authors suggest that metacognitive monitoring is impaired in CIT which has a knock-on effect on reminder setting behaviour, but that a direct link also exists between CIT and reduced reminder setting independently of confidence.

Strengths:

The study combines the latest advances in transdiagnostic approaches to psychopathology with a cleverly designed external reminder-setting task. The approach allows for investigation of what some of the downstream consequences associated with impaired metacognition in sub-clinical psychopathology may be.

The experimental design and hypotheses were pre-registered prior to data collection.

The manuscript is well written and rigorous analysis approaches are used throughout.

Weaknesses:

Participants only performed a single task so it remains unclear if the observed effects would generalise to reminder setting in other cognitive domains.

The sample consisted of participants recruited from the general population. Future studies should investigate whether the effects observed extend to individuals with the highest levels of symptoms (including clinical samples).

Reviewer #1 (Public review):

Summary:

The authors measured glutamate transients in the DMS of rats as they performed an action selection task. They identified diverse patterns of behavior and glutamate dynamics depending on the pre-existing behavioral phenotype of the rat (sign tracker or goal tracker). Using pathway-specific DREADDs, they showed that these behavioral phenotypes and their corresponding glutamate transients were differentially dependent on input from the prelimbic cortex to the DMS.

Strengths:

Overall there are some very interesting results that make an important contribution to the field. Notably, the results seem to point to differential recruitment of the PL-DMS pathway in goal-tracking vs sign-tracking behaviors.

Weaknesses:

(1) The controls for off-target effects of CNO are not given sufficient importance both in terms of power and in reporting of their results. There is precedent to accept that CNO at the dosage given is unlikely to disrupt the behaviour, this doesn't justify the assumption that glutamate transmission won't be affected, and this possibility hasn't been sufficiently ruled out.<br /> (2) The specificity of the viral approach needs to be clarified. Figure 8 indicates a large proportion of the PL neuron population that expresses mCherry in the absence of AAV-Cre. This infers that there are a large number of neurons inhibited by CNO administration that were outside the projection pathway, drawing into question the specificity of the effects.

Reviewer #2 (Public review):

Summary:

The authors aimed to determine whether goal-directed and cue-driven attentional strategies (goal- and sign-tracking phenotypes) were associated with variation in cued motor responses and dorsomedial striatal (DMS) glutamate transmission. They used a treadmill task in which cues indicated whether rats should turn or stop to receive a reward. They collected and analyzed several behavioral measures related to task performance with a focus on turns (performance, latency, duration) for which there are more measures than for stops. First, they established that goal-trackers perform better than sign-trackers in post-criterion turn performance (cued turns completed) and turn initiation. They used glutamate sensors to measure glutamate transmission in DMS. They performed analyses on glutamate traces that suggest phasic glutamate DMS dynamics to cues were primarily associated with successful turn performance and were more characteristic of goal-trackers (ie. rats with "goal-directed" attentional strategy). Smaller and more frequent DMS glutamate peaks were associated with other task events, cued misses (missed turns), cued stops, and reward delivery and were more characteristic of sign-trackers (i.e. rats with "cue-driven" attentional strategies). Consistent with the reported glutamate findings, chemogenetic inhibition of prelimbic-DMS glutamate transmission had an effect on goal-trackers' turn performance without affecting sign-trackers' performance in the treadmill task.

Strengths:

The power of the sign- and goal-tracking model to account for neurobiological and behavioral variability is critically important to the field's understanding of heterogeneity of the brain in health and disease. The approach and methodology are sound in their contribution to this important effort.

The authors establish behavioral differences, measure a neurobiological correlate of relevance, and then manipulate that correlate in a broader circuitry and show a causal role in behavior that is consistent with neurobiological measurements and phenotypic differences.

Sophisticated analyses provide a compelling description of the authors' observations.

Limitations:

Considerable transparency was added in the revised preprint. The "n" for each analysis is now available in Tables 1 and 3, carefully cross-referenced by figure. Readers may now carefully consider the n's in drawing their own conclusions from reported data.

While more conventional trial-averaged population activity traces are not presented or analyzed, the unique nature of the peak phenotypes is likely to "wash out" potentially meaningful signals if averaged across subjects. The distribution of peaks analyses (and shifts observed with chemogenetic inhibition) are improved in the revised preprint and are informative to illustrate this likelihood. Representative traces should theoretically be consistent with population averages within phenotype, and if not, discussion of such inconsistencies may have enriched the conclusions drawn from the study. For example, population traces of the phasic cue response in GT may resemble the representative peak examples, while smaller irregular peaks of ST may "wash out" in a population average (possibly resulting in a prolonged elevation) and could have strengthened the rationale for more sophisticated analyses of peak probability that remain the focus of the revised preprint.

Reviewer #3 (Public review):

Summary:

Avila and colleagues investigate the role of glutamate signaling in the dorsomedial striatum in a treadmill-based task where rats learn to turn or stop their walking based on learning cue-associations that allow them to acquire rewards. Phenotypic variation in Pavlovian conditioned sign and goal-tracking behavior was examined, where behavioral differences in stopping and turning were observed. Glutamate signals in the DMS were recording during the treadmill task, and were related to features of cue-controlled movement, with a stronger relationship seen for goal trackers. Finally, chemogenic inhibition of prelimbic neurons projecting to the DMS (the predicted source of those glutamate signals), preferentially affected cued movement in goal trackers. The authors couch these experiments in the context of cognitive control-attentional mechanisms, movement disorders, and individual differences in cue reactivity.

Strengths:

Overall these studies are interesting and are of general relevance to a number of research questions in neurology and psychiatry. The assessment of intersection of individual differences in cue-related learning strategies with movement-related questions - in this case cued turning behavior - is interesting and understudied question. The link between this work and growing notions of corticostriatal control of action selection makes it timely.

Weaknesses:

The clarity of the manuscript could be improved in several places, including in the graphical visualization of data. It is difficult to interpret the glutamate results, as presented, in the context of specific behaviors. It is difficult to assess how many trials/subjects are represented in the data shown, and too much emphasis is placed on representative examples. Averages traces of the glutamate data and other standard analysis approaches would improve the paper and allow for easier interpretation of the data.

Reviewer #1 (Public review):

Summary:

This paper investigates the effects of the explicit recognition of statistical structure and sleep consolidation on the transfer of learned structure to novel stimuli. The results show a striking dissociation in transfer ability between explicit and implicit learning of structure, finding that only explicit learners transfer structure immediately. Implicit learners, on the other hand, show an intriguing immediate structural interference effect (better learning of novel structure) followed by successful transfer only after a period of sleep.

Strengths:

This paper is very well written and motivated, and the data are presented clearly with a logical flow. There are several replications and control experiments and analyses that make the pattern of results very compelling. The results are novel and intriguing, providing important constraints on theories of consolidation. The discussion of relevant literature is thorough. In sum, this work makes an exciting and important contribution to the literature.

Weaknesses:

There have been several recent papers which have identified issues with alternative forced choice (AFC) tests as a method of assessing statistical learning (e.g. Isbilen et al. 2020, Cognitive Science). A key argument is that while statistical learning is typically implicit, AFC involves explicit deliberation and therefore does not match the learning process well. The use of AFC in this study thus leaves open the question of whether the AFC measure benefits the explicit learners in particular, given the congruence between knowledge and testing format, and whether, more generally, the results would have been different had the method of assessing generalization been implicit. Prior work has shown that explicit and implicit measures of statistical learning do not always produce the same results (eg. Kiai & Melloni, 2021, bioRxiv; Liu et al. 2023, Cognition).

The authors argued in their response to this point that this issue could have quantitative but not qualitative impacts on the results, but we see no reason that the impact could not be qualitative. In other words, it should be acknowledged that an implicit test could potentially result in the implicit group exhibiting immediate structure transfer.

Given that the explicit/implicit classification was based on an exit survey, it is unclear when participants who are labeled "explicit" gained that explicit knowledge. This might have occurred during or after either of the sessions, which could impact the interpretation of the effects and deserves discussion.

Reviewer #2 (Public review):

Summary:

Sleep has not only been shown to support the strengthening of memory traces, but also their transformation. A special form of such transformation is the abstraction of general rules from the presentation of individual exemplars. The current work used large online experiments with hundreds of participants to shed further light on this question. In the training phase participants saw composite items (scenes) that were made up of pairs of spatially coupled (i.e., they were next to each other) abstract shapes. In the initial training, they saw scenes made up of six horizontally structured pairs and in the second training phase, which took place after a retention phase (2 min awake, 12 hour incl. sleep, 12 h only wake, 24 h incl. sleep), they saw pairs that were horizontally or vertically coupled. After the second training phase, a two-alternatives-forced-choice (2-AFC) paradigm, where participants had to identify true pairs versus randomly assembled foils, was used to measure performance on all pairs. Finally, participants were asked five questions to identify, if they had insight into the pair structure and post-hoc groups were assigned based on this. Mainly the authors find that participants in the 2 minute retention experiment without explicit knowledge of the task structure were at chance level performance for the same structure in the second training phase, but had above chance performance for the vertical structure. The opposite was true for both sleep conditions. In the 12 h wake condition these participants showed no ability to discriminate the pairs from the second training phase at all.

Strengths:

All in all, the study was performed to a high standard and the sample size in the implicit condition was large enough to draw robust conclusions. The authors make several important statistical comparisons and also report an interesting resampling approach. There is also a lot of supplemental data regarding robustness.

Weaknesses:

My main concern regards the small sample size in the explicit group and the lack of experimental control.

Reviewer #3 (Public review):

In this project, Garber and Fiser examined how the structure of incidentally learned regularities influences subsequent learning of regularities, that either have the same structure or a different one. Over a series of six online experiments, it was found that the structure (spatial arrangement) of the first set of regularities affected learning of the second set, indicating that it has indeed been abstracted away from the specific items that have been learned. The effect was found to depend on the explicitness of the original learning: Participants who noticed regularities in the stimuli were better at learning subsequent regularities of the same structure than of a different one. On the other hand, participants whose learning was only implicit had an opposite pattern: they were better in learning regularities of a novel structure than of the same one. However, when an overnight sleep separated the first and second learning phases, this opposite effect was reversed and came to match the pattern of the explicit group, suggesting that the abstraction and transfer in the implicit case were aided by memory consolidation.

In their revision the authors addressed my major comments successfully and I commend them for that.

Reviewer #1 (Public review):

Summary:

The authors investigate the role of the melanocortin system in puberty onset. They conclude that POMC neurons within the arcuate nucleus of the hypothalamus provide important but differing input to kisspeptin neurons in the arcuate or rostral hypothalamus.

Strengths:

Innovative and novel<br /> Technically sound<br /> Well-designed<br /> Thorough

Weaknesses:

There were no major weaknesses identified.

Reviewer #2 (Public review):

Summary:

This interesting manuscript describes a study investigating the role of MC4R signalling on kisspeptin neurons. The initial question is a good one. Infertility associated with MC4 mutations in humans has typically been ascribed to the consequent obesity and impaired metabolic regulation. Whether there is a direct role for MC4 in regulating the HPG axis has not been thoroughly examined. Here, the researchers have assembled an elegant combination of targetted loss of function and gain of function in vivo experiments, specifically targetting MC4 expression in kisspeptin neurons. This excellent experimental design should provide compelling evidence for whether melanocortin signalling dirently affects arcuate kisspeptin neurons to support normal reproductive function. There were definite effects on reproductive function (irregular estrous cycle, reduced magnitude of LH surge induced by exogenous estradiol). However, the magnitude of these responses and the overall effect on fertility were relatively minor. The mice lacking MC4R in kisspeptin neurons remained fertile despite these irregularities. The second part of the manuscript describes a series of electrophysiological studies evaluating the pharmacological effects of melanocortin signalling in kisspeptin cells in ex-vivo brain slides. These studies characterised interesting differential actions of melanocortins in two different populations of kisspeptin neurons. Collectively, the study provides some novel insights into how direct actions of melanocortin signalling via the MC4 receptor in kisspeptin neurons contribute to the metabolic regulation of the reproductive system. Importantly, however, it is clear that other mechanisms are also at play.

Strengths:

The loss of function/gain of function experiments provides a conceptually simple but hugely informative experimental design. This is the key strength of the current paper - especially the knock-in study that showed improved reproductive function even in the presence of ongoing obesity. This is a very convincing result that documents that reproductive deficits in MC4R knockout animals (and humans with deleterious MC4R gene variants) can be ascribed to impaired signalling in the hypothalamic kisspeptin neurons and not necessarily caused as a consequence of obesity. As concluded by the authors: "reproductive impairments observed in MC4R deficient mice, which replicate many of the conditions described in humans, are largely mediated by the direct action of melanocortins via MC4R on Kiss1 neurons and not to their obese phenotype." This is important, as it might change how such fertility problems are treated.

I would like to see the validation experiments for the genetic manipulation studies given greater prominence in the manuscript because they are critical to interpretation. Presently, only single unquantified images are shown, and a much more comprehensive analysis should be provided.

Weaknesses:

(1) Given that mice lacking MC4R in kisspeptin neurons remained fertile despite some reproductive irregularities, this can be described as a contributing pathway, but other mechanisms must also be involved in conveying metabolic information to the reproductive system. This is now appropriately covered in the discussion.

(2) The mechanistic studies evaluating melanocortin signalling in kisspeptin neurons were all completed in ovariectomised animals (with and without exogenous hormones) that do not experience cyclical hormone changes. Such cyclical changes are fundamental to how these neurons function in vivo and may dynamically alter how they respond to hormones and neuropeptides. Eliminating this variable makes interpretation difficult, but the authors have justified this as a reductionist approach to evaluate estradiol actions specifically. However, this does not reflect the actual complexity of reproductive function.

For example, the authors focus on a reduced LH response to exogenous estradiol in ovariectomised mice as evidence that there might be a sub-optimal preovulatory LH surge. However, the preovulatory LH sure (in intact animals) was not measured.

They have not assessed why some follicles ovulated, but most did not. They have focused on the possibility that the ovulation signal (LH surge) was insufficient rather than asking why some follicles responded and others did not. This suggests some issue with follicular development, likely due to changes in gonadotropin secretion during the cycle and not simply due to an insufficient LH surge.

Reviewer #3 (Public review):

The manuscript by Talbi R et al. generated transgenic mice to assess the reproduction function of MC4R in Kiss1 neurons in vivo and used electrophysiology to test how MC4R activation regulated Kiss1 neuronal firing in ARH and AVPV/PeN. This timely study is highly significant in neuroendocrinology research for the following reasons.

(1) The authors' findings are significant in the field of reproductive research. Despite the known presence of MC4R signaling in Kiss1 neurons, the exact mechanisms of how MC4R signaling regulates different Kiss1 neuronal populations in the context of sex hormone fluctuations are not entirely understood. The authors reported that knocking out Mc4r from Kiss1 neurons replicates the reproductive impairment of MC4RKO mice, and Mc4r expression in Kiss1 neurons in the MC4R null background partially restored the reproductive impairment. MC4R activation excites Kiss1 ARH neurons and inhibits Kiss1 AVPV/PeN neurons (except for elevated estradiol).

(2) Reproduction dysfunction is one of obesity comorbidities. MC4R loss-of-function mutations cause obesity phenotype and impaired reproduction. However, it is hard to determine the causality. The authors carefully measured the body weight of the different mouse models (Figure 1C, Figure 2A, Figure 3B). For example, the Kiss1-MC4RKO females showed no body weight difference at puberty onset. This clearly demonstrated the direct function of MC4R signaling in reproduction but was not a consequence of excessive adiposity.

(3) Gene expression findings in the "KNDy" system align with the reproduction phenotype.

(4) The electrophysiology results reported in this manuscript are innovative and provide more details of MC4R activation and Kiss1 neuronal activation.

Overall, the authors have presented sufficient background in a clear, logical, and organized structure, clearly stated the key question to be addressed, used the appropriate methodology, produced significant and innovative main findings, and made a justified conclusion.

Comments on revisions:

The authors have addressed my comments.

Reviewer #2 (Public review):

This work describes a highly complex automated algorithm for analyzing vascular imaging data from two-photon microscopy. This tool has the potential to be extremely useful to the field and to fill gaps in knowledge of hemodynamic activity across a regional network. The biological application provided, however, has several problems that make many of the scientific claims in the paper questionable.

The authors have commented on my main concerns. They have provided some limited evidence in the literature of prolonged vascular signals - though still nothing close to the several hundred-second long vascular responses oscillating between dilation and constriction shown here. And they have added a nice experiment showing they can resolve small beads (though still quite bigger than their average capillary diameter) with their system. They have also added comparisons with other software which shows some modest but clear improvement in some aspects. All these make the paper stronger.

However, I still think the main overall problem from the biological interpretation side of the paper is still not fixed. Perhaps I am too skeptical but I have a hard time accepting the conclusions about dilators and constrictors (depth dependence, distance from nearest neuron, etc.) because the data are just too temporally sparse and too unconventional in their duration and fluctuation. Also, the differences are often very small compared to the variability.

Regarding the spatial resolution, I was more concerned that if the pixel size is about 1 micron, then detecting around 1 micron dilations (or even less) is really below the resolution of the system. While the bead imaging is good for showing they can extract these diameters very close to the real value, this is still not like a living brain with imaging and motion artifacts. Given the temporal resolution issues already mentioned, this makes me highly skeptical of the biological claims. I think the discussion should at least strongly emphasize that a major caveat in their analysis is that the diameters are only sampled every 42 seconds, and , given the fluctuation in vessel diameter above and below baseline, this makes classification of the vessel as constrictor/dilator and by how much highly dependent on what time point the vessel diameter was sampled.

Although the computational side of the paper is not my strong point, it seems there is potential for the pipeline to be useful in other applications. But given the limitations of the system they are using, I feel that it is a methods paper in its current form more than anything that should be making the biological claims included.

Reviewer #2 (Public review):

In this study, the authors measured extracellular electrical features of colliding APs travelling in different directions down an isolated earthworm axon. They then used these features to build a model of the potential ephaptic effects of AP annihilation, i.e. the electrical signals produced by colliding/annihilating APs that may influence neighbouring tissue. The model was then applied to some different hypothetical scenarios involving synaptic connections. In a revised version of the manuscript, it was also applied, with success, to published experimental data on the cerebellar basket cell-to-Purkinje cell pinceau connection. The conclusion is that an annihilating AP at a presynaptic terminal can emphatically influence the voltage of a postsynaptic cell (the 'electrical coupling between neurons' of the title), and that the nature of this influence depends on the physical configuration of the synapse.

As an experimental neuroscientist who has never used computational approaches, I am unable to comment on the rigour of the analytical approaches that form the bulk of this paper. The experimental approaches appear very well carried out, and the data showing equal conduction velocity of anti- and orthodromically propagating APs in every preparation are convincing.

The conclusions drawn from the synaptic modelling are considerably strengthened by the data in Figure 5. Here, the authors' model - including AP annihilation at a synaptic terminal - is used to predict the amplitude and direction of experimentally observed effects at the cerebellar basket cell-to-Purkinje cell synapse (Blot & Barbour 2014). One particular form of the model (RTM with tau=0.5ms and realistic non-excitability of the terminal) matches the experimental data extremely well. The authors also include a convincing demonstration (Panel A) that a propagating but not annihilating AP has almost no effect on a neighbouring neuron's activity. Given that the authors' model of ephaptic effects can quantitatively explain key features of experimental data pertaining to synaptic function, the implications for the relevance of ephaptic coupling at different synaptic contacts may be widespread and important.

Reviewer #1 (Public review):

Summary:

The authors of this study investigated the development of interoceptive sensitivity in the context of cardiac and respiratory interoception in 3-, 9-, and 18-month-old infants using a combination of both cross-sectional and longitudinal designs. They utilised the cardiac interoception paradigm developed by Maister et al (2017) and also developed a new paradigm to investigate respiratory interoception in infants. The main findings of this research are that 9-month-old infants displayed a preference for stimuli presented synchronously with their own heartbeat and respiration. The authors found less reliable effects in the 18-month-old group, and this was especially true for the respiratory interoceptive data. The authors replicated a visual preference for synchrony over asynchrony for the cardiac domain in 3-month-old infants, while they found inconclusive evidence regarding the respiratory domain. Considering the developmental nature of the study, the authors also investigated the presence of developmental trajectories and associations between the two interoceptive domains. They found evidence for a relationship between cardiac and respiratory interoceptive sensitivity at 18 months only and preliminary evidence for an increase in respiratory interoception between 9 and 18 months.

Strengths:

The conclusions of this paper are mostly well supported by data, and the data analysis procedures are rigorous and well-justified. The main strengths of the paper are:

- A first attempt to explore the association between two different interoceptive domains. How different organ-specific axes of interoception relate to each other is still open and exploring this from a developmental lens can help shed light into possible relationships. The authors have to be commended for developing a novel interoceptive tasks aimed at assessing respiratory interoceptive sensitivity in infants and toddlers, and for trying to assess the relationship between cardiac and respiratory interoception across developmental time.<br /> - A thorough justification of the developmental ages selected for the study. The authors provide a rationale behind their choice to examine interoceptive sensitivity at 3, 9, and 18-months of age. These are well justified based on the literature pertaining to self- and social development. Sometimes, I wondered whether explaining the link between these self and social processes and interoception would have been beneficial as a reader not familiar with the topics may miss the point.<br /> - An explanation of direction of looking behaviour using latent curve analysis. I found this additional analysis extremely helpful in providing a better understanding of the data based on previous research and analytical choices. As the authors explain in the manuscript, it is often difficult to interpret the direction of infant looking behaviour as novelty and familiarity preferences can also be driven by hidden confounders (e.g. task difficulty). The authors provide compelling evidence that analytical choices can explain some of these effects. Beyond the field of interoception, these findings will be relevant to development psychologists and will inform future studies using looking time as a measure of infants' ability to discriminate among stimuli.<br /> - The use of simulation analysis to account for small sample size. The authors acknowledge that some of the effects reported in their study could be explained by a small sample size (i.e. the 3-month-olds and 18-month-olds data). Using a simulation approach, the authors try to overcome some of these limitations and provide convincing evidence of interoceptive abilities in infancy and toddlerhood (but see also my next point).

Comments on revision:

The authors have clearly addressed the comments on the previous version of this manuscript. I have no further comments.

Reviewer #2 (Public review):

Summary:

This study by Tünte et al. investigated the development of interoceptive sensitivity during the first year of life, focusing specifically on cardiac and respiratory sensitivity in infants aged 3, 9, and 18 months. The research employed a previously developed experimental paradigm for the cardiac domain and adapted it for a novel paradigm in the respiratory domain. This approach assessed infants' cardiac and respiratory sensitivity based on their preferential looking behavior toward visuo-auditory stimuli displayed on a monitor, which moved either in sync or out of sync with the infants' own heartbeats or breathing. The results in the cardiac domain showed that infants across all age groups preferred stimuli moving synchronously rather than asynchronously with their heartbeat, suggesting the presence of cardiac sensitivity as early as 3 months of age. However, it is noteworthy that this preference direction contradicts a previous study, which found that 5-month-old infants looked longer at stimuli moving asynchronously with their heartbeat (Maister et al., 2017). In the respiratory domain, only the group of 9-month-old infants showed a preference for stimuli presented synchronously with their breathing. The authors conducted various statistical analyses to thoroughly examine the obtained data, providing deeper insights valuable for future research in this field.

Strengths:

Few studies have explored the early development of interoception, making the replication of the original study by Maister et al. (2017) particularly valuable. Beyond replication, this study expands the investigation into the respiratory domain, significantly enhancing our understanding of interoceptive development. The provision of longitudinal and cross-sectional data from infants at 3, 9, and 18 months of age is instrumental in understanding their developmental trajectory.

Weaknesses:

Due to a technical error, this study failed to counterbalance the conditions of the first trial in both the iBEAT and iBREATH tests. Although the authors addressed this issue as much as possible by employing alternative analyses, it should be noted that this error may have critically influenced the results and, thus, the conclusions.

Reviewer #1 (Public Review):

The authors observed a decline in autophagy and proteasome activity in the context of Milton knockdown. Through proteomic analysis, they identified an increase in the protein levels of eIF2β, subsequently pinpointing a novel interaction within eIF subunits where eIF2β contributes to the reduction of eIF2α phosphorylation levels. Furthermore, they demonstrated that overexpression of eIF2β suppresses autophagy and leads to diminished motor function. It was also shown that in a heterozygous mutant background of eIF2β, Milton knockdown could be rescued. This work represents a novel and significant contribution to the field, revealing for the first time that the loss of mitochondria from axons can lead to impaired autophagy function via eIF2β, potentially influencing the acceleration of aging.

Reviewer #2 (Public Review):

In the manuscript, the authors aimed to elucidate the molecular mechanism that explains neurodegeneration caused by the depletion of axonal mitochondria. In Drosophila, starting with siRNA depletion of Milton and Miro, the authors attempted to demonstrate that the depletion of axonal mitochondria induces the defect in autophagy. From proteome analyses, the authors hypothesized that autophagy is impacted by the abundance of eIF2β and the phosphorylation of eIF2α. The authors followed up the proteome analyses by testing the effects of eIF2β overexpression and depletion on autophagy. With the results from those experiments, the authors proposed a novel role of eIF2β in proteostasis that underlies neurodegeneration derived from the depletion of axonal mitochondria.

The manuscript has several weaknesses. The reader should take extra care while reading this manuscript and when acknowledging the findings and the model in this manuscript.

The defect in autophagy by the depletion of axonal mitochondria is one of the main claims in the paper. The authors should work more on describing their results of LC3-II/LC3-I ratio, as there are multiple ways to interpret the LC3 blotting for the autophagy assessment. Lysosomal defects result in the accumulation of LC3-II thus the LC3-II/LC3-I ratio gets higher. On the other hand, the defect in the early steps of autophagosome formation could result in a lower LC3-II/LC3-I ratio. From the results of the actual blotting, the LC3-I abundance is the source of the major difference for all conditions (Milton RNAi and eIF2β overexpression and depletion).

Another main point of the paper is the up-regulation of eIF2β by depleting the axonal mitochondria leads to the proteostasis crisis. This claim is formed by the findings from the proteome analyses. The authors should have presented their proteomic data with much thorough presentation and explanation. As in the experiment scheme shown in Figure 4A, the author did two proteome analyses: one from the 7-day-old sample and the other from the 21-day-old sample. The manuscript only shows a plot of the result from the 7-day-old sample, but that of the result from the 21-day-old sample. For the 21-day-old sample, the authors only provided data in the supplemental table, in which the abundance ratio of eIF2β from the 21-day-old sample is 0.753, meaning eIF2β is depleted in the 21-day-old sample. The authors should have explained the impact of the eIF2β depletion in the 21-day-old sample, so the reader could fully understand the authors' interpretation of the role of eIF2β on proteostasis.

Joint Public Review:

Engineered artificial gene regulatory networks ("circuits") have a wide range of applications, but their design is often hindered by unforeseen interactions between the host and circuit processes. This manuscript employs computational modeling to investigate how growth feedback influences the performance of synthetic gene circuits capable of adaptation. By analyzing 425 hypothetical circuits previously identified as achieving nearly perfect adaptation (Ma et al., 2009; Shi et al., 2017), the authors introduce growth feedback into their models using additional terms in ordinary differential equations. Their simulations reveal that growth feedback can disrupt adaptation dynamics in diverse ways but also identify core motifs that ensure robust performance under such conditions. Additionally, they establish a scaling law linking circuit robustness to the strength of growth feedback. The findings have important implications for synthetic biology, where host-circuit interactions frequently compromise desired behaviors, and for systems biology, by advancing the understanding of network motif dynamics. The authors' classification schemes will be highly valuable to the community, offering a framework for addressing growth-related challenges in circuit design.

Strengths<br /> - A detailed investigation into the reasons for adaptation failure upon the introduction of cell growth was conducted, distinguishing this work from other studies of functional screening in gene regulatory network topologies. The comprehensiveness of the analysis is particularly noteworthy.<br /> - Approaches for assessing robustness, such as the survival ratio Q, were employed, providing tools that may be applicable to a broad range of network topologies beyond adaptation. The scaling law derived from these approaches is both novel and insightful.<br /> - A thorough numerical analysis of three gene regulatory networks exhibiting adaptation was performed. For each of the 425 topologies analyzed, approximately 2e5 circuits were sampled using Latin hypercube sampling, ensuring robust coverage of the parameter space. Among these, 1.5e5 circuits were identified as showing adaptation and subsequently subjected to further analysis, yielding approximately 350 parametric designs per topology for deeper investigation.<br /> - The systematic approach and depth of the analysis position this study as a significant contribution to the understanding of gene regulatory networks and their response to growth feedback. The combination of detailed investigation, novel robustness metrics, and rigorous computational techniques enhances the impact of this work within the field.

Weaknesses<br /> - The study focuses exclusively on a preselected set of 425 topologies previously shown to achieve adaptation, limiting the exploration of whether growth feedback could enable adaptation in circuits not inherently adaptive. While the authors have discussed and justified this choice, the focus restricts the generality of the conclusions, as the potential for growth feedback to induce adaptation in non-adaptive circuits remains unaddressed. The analysis includes scenarios where higher growth feedback restores adaptation in circuits that lose it at intermediate levels, but further elaboration on the implications for circuit design would strengthen the impact. The numerical framework and parameter choices align well with established methods, and an overview of the selected topologies has been provided. However, offering detailed information in supplementary materials or a public repository would further enhance the paper's accessibility and reproducibility.

- The model fails to capture the influence of protein levels on growth. To ensure accurate modeling of protein-level effects on growth, the b(t) term should be scaled appropriately, similar to Tan et al. Nature Chemical Biology 5:842-848 (2009).

- The authors propose bistability or multistability as the primary mechanisms behind different types of adaptation failure, explaining why the failures do not occur precisely at bifurcation points. They argue that their ODE simulations provide evidence for oscillation-related bifurcations, and an included appendix explores this phenomenon further, detailing how it can be observed in their results. While the authors choose not to apply semi-analytic methods, such as numerical continuation and eigenvalue analysis, to validate the existence of bifurcations, their approach offers valuable insights into the underlying dynamics of adaptation failures.

- The analysis in this work is carried out exclusively in a deterministic regime, as the focus is on scenarios where the effects of noise are assumed to be minimal. This approach is justified, and the authors acknowledge the complexity of extending their analysis to include stochasticity, which they suggest as an avenue for future research. The discussion has been expanded to address the potential impact of noise, its handling, and the assumptions underlying its exclusion. It is important to note, however, that noise can significantly alter system behavior-for instance, stabilizing trajectories and removing oscillations, as shown in prior studies (e.g., 10.1016/j.cels.2016.01.004). Additionally, variability in experimental implementations may influence the dynamics beyond what is predicted in deterministic models. These factors should be considered when interpreting the results.

Reviewer #2 (Public review):

Summary:

This manuscript provides a comprehensive overview of potential resistance mutations within MET Receptor Tyrosine Kinase and defines how specific mutations affect different inhibitors and modes of target engagement. The goal is to identify inhibitor combinations with the lowest overlap in their sensitivity to resistant mutations and determine if certain resistance mutations/mechanisms are more prevalent for specific modes of ATP-binding site engagement. To achieve this, the authors measured the ability of ~6000 single mutants of MET's kinase domain (in the context of a cytosolic TPR fusion) to drive IL-3-independent proliferation (used as a proxy for activity) of Ba/F3 cells (deep mutational profiling) in the presence of 11 different inhibitors. The authors then used co-crystal and docked structures of inhibitor-bound MET complexes to define the mechanistic basis of resistance and applied a protein language model to develop a predictive model of inhibitor sensitivity/resistance.

Strengths:

The major strengths of this manuscript are the comprehensive nature of the study and the rigorous methods used to measure the sensitivity of ~6000 MET mutants in a pooled format. The dataset generated will be a valuable resource for researchers interested in understanding kinase inhibitor sensitivity and, more broadly, small molecule ligand/protein interactions. The structural analyses are systematic and comprehensive, providing interesting insights into resistance mechanisms. Furthermore, the use of machine learning to define inhibitor-specific fitness landscapes is a valuable addition to the narrative. Although the ESM1b protein language model is only moderately successful in identifying the underlying mechanistic basis of resistance, the authors' attempt to integrate systematic sequence/function datasets with machine learning serves as a foundation for future efforts.

Weaknesses:

The main limitation of this study is that the authors' efforts to define general mechanisms between inhibitor classes were only moderately successful due to the challenge of uncoupling inhibitor-specific interaction effects from more general mechanisms related to the mode of ATP-binding site engagement. However, this is a minor limitation that only minimally detracts from the impressive overall scope of the study.

Reviewer #3 (Public review):

Summary:

In the manuscript 'Mapping kinase domain resistance mechanisms for the MET receptor tyrosine kinase via deep mutational scanning' by Estevam et al, deep mutational scanning is used to assess the impact of ~5,764 mutants in the MET kinase domain on the binding of 11 inhibitors. Analyses were divided by individual inhibitor and kinase inhibitor subtype (I,II, I 1/2, and III). While a number of mutants were consistent with previous clinical reports, novel potential resistance mutants were also described. This study has implications for the development of combination therapies, namely which combination of inhibitors to avoid based on overlapping resistance mutant profiles. While one suggested pair of inhibitors with least overlapping resistance mutation profiles was suggested, this manuscript presents a proof of concept toward a more systematic approach for improved selection of combination therapeutics. Furthermore, in a final part of this manuscript the data was used to train a machine learning model, the ESM-1b protein language model augmented with an XG Boost Regressor framework, and found that they could improve predictions of resistance mutations above the initial ESM-1b model.

Strengths:

Overall this paper is a tour-de-force of data collection and analysis to establish a more systematic approach for the design of combination therapies, especially in targeting MET and other kinases, a family of proteins significant to therapeutic intervention for a variety of diseases. The presentation of the work is mostly concise and clear with thousands of data points presented neatly and clearly. The discovery of novel resistance mutants for individual MET inhibitors, kinase inhibitor subtypes within the context of MET, and all resistance mutants across inhibitor subtypes for MET has clinical relevance. However, probably the most promising outcome of this paper is the proposal of the inhibitor combination of Crizotinib and Cabozantib as Type I and Type II inhibitors, respectively, with the least overlapping resistance mutation profiles and therefore potentially the most successful combination therapy for MET. While this specific combination is not necessarily the point, it illustrates a compelling systematic approach for deciding how to proceed in developing combination therapy schedules for kinases. In an insightful final section of this paper, the authors approach using their data to train a machine learning model, perhaps understanding that performing these experiments for every kinase for every inhibitor could be prohibitive to applying this method in practice.

Weaknesses:

This paper presents a clear set of experiments with a compelling justification. The content of the paper is overall of high quality. Below are mostly regarding clarifications in presentation.

Two places could use more computational experiments and analysis, however. Both are presented as suggestions, but at least a discussion of these topics would improve the overall relevance of this work. In the first case it seems that while the analyses conducted on this dataset were chosen with care to be the most relevant to human health, further analyses of these results and their implications of our understanding of allosteric interactions and their effects on inhibitor binding would be a relevant addition. For example, for any given residue type found to be a resistance mutant are there consistent amino acid mutations to which a large or small or effect is found. For example is a mutation from alanine to phenylalanine always deleterious, though one can assume the exact location of a residue matters significantly. Some of this analysis is done in dividing resistance mutants by those that are near the inhibitor binding site and those that aren't, but more of these types of analyses could help the reader understand the large amount of data presented here. A mention at least of the existing literature in this area and the lack or presence of trends would be worthwhile. For example, is there any correlation with a simpler metric like the Grantham score to predict effects of mutations (in a way the ESM-1b model is a better version of this, so this is somewhat implicitly discussed).

Indeed, this discussion relates to the second point this manuscript could improve upon: the machine learning section. The main actionable item here is that this results section seems the least polished and could do a better job describing what was done. In the figure it looks like results for certain inhibitors were held out as test data - was this all mutants for a single inhibitor, or some other scheme? Overall I think the implications of this section could be fleshed out, potentially with more experiments. As mentioned in the 'Strengths' section, one of the appealing aspects of this paper is indeed its potential wide applicability across kinases -- could you use this ML model to predict resistance mutants for an entirely different kinase? This doesn't seem far-fetched, and would be an extremely compelling addition to this paper to prove the value of this approach.

Another area in which this paper could improve its clarity is in the description of caveats of the assay. The exact math used to define resistance mutants and its dependence on the DMSO control is interesting, it is worth discussing where the failure modes of this procedure might be. Could it be that the resistance mutants identified in this assay would differ significantly from those found in patients? That results here are consistent with those seen in the clinic is promising, but discrepancies could remain. Furthermore a more in depth discussion of the MetdelEx14 results is warranted. For example, why is the DMSO signature in Figure 1 - supplement 4 so different from that of Figure 1? And finally, there is a lot of emphasis put on the unexpected results of this assay for the tivantinib "type III" inhibitor - could this in fact be because the molecule "is highly selective for the inactive or unphosphorylated form of c-Met" according to Eathiraj et al JBC 2011? These points are addressed in previous work (Estevam et al 2024) or in the detailed methods section, but are not obvious in the main text of the paper.

This paper is crisply written with beautiful figures, and the complexity of the data is easy to understand from an in depth discussion of the mutants that have been previously reported.

Finally, the potential impacts and follow-ups of this excellent study could be used as a resource for the community both as a dataset and as a proof of concept. It is exciting that his approach can be altered and/or improved in the future to facilitate the general application of this approach for combination therapies and the understanding of mechanism for other targets.

Comments on revisions:

Thank you for your additions and changes - they have improved the quality of this paper.

Reviewer #1 (Public review):

Summary:

In this study from Zhu and colleagues, a clear role for MED26 in mouse and human erythropoiesis is demonstrated that is also mapped to amino acids 88-480 of the human protein. The authors also show the unique expression of MED26 in later-stage erythropoiesis and propose transcriptional pausing and condensate formation mechanisms for MED26's role in promoting erythropoiesis. Despite the author's introductory claim that many questions regarding Pol II pausing in mammalian development remain unanswered, the importance of transcriptional pausing in erythropoiesis has actually already been demonstrated (Martell-Smart, et al. 2023, PMID: 37586368, which the authors notably did not cite in this manuscript). Here, the novelty and strength of this study is MED26 and its unique expression kinetics during erythroid development.

Strengths:

The widespread characterization of kinetics of mediator complex component expression throughout the erythropoietic timeline is excellent and shows the interesting divergence of MED26 expression pattern from many other mediator complex components. The genetic evidence in conditional knockout mice for erythropoiesis requiring MED26 is outstanding. These are completely new models from the investigators and are an impressive amount of work to have both EpoR-driven deletion and inducible deletion. The effect on red cell number is strong in both. The genetic over-expression experiments are also quite impressive, especially the investigators' structure-function mapping in primary cells. Overall the data is quite convincing regarding the genetic requirement for MED26. The authors should be commended for demonstrating this in multiple rigorous ways.

Weaknesses:

(1) The authors state that MED26 was nominated for study based on RNA-seq analysis of a prior published dataset. They do not however display any of that RNA-seq analysis with regards to Mediator complex subunits. While they do a good job showing protein-level analysis during erythropoiesis for several subunits, the RNA-seq analysis would allow them to show the developmental expression dynamics of all subunit members.

(2) The authors use an EpoR Cre for red cell-specific MED26 deletion. However, other studies have now shown that the EpoR Cre can also lead to recombination in the macrophage lineage, which clouds some of the in vivo conclusions for erythroid specificity. That being said, the in vitro erythropoiesis experiments here are convincing that there is a major erythroid-intrinsic effect.

(3) The donor chimerism assessment of mice transplanted with MED26 knockout cells is a bit troubling. First, there are no staining controls shown and the full gating strategy is not shown. Furthermore, the authors use the CD45.1/CD45.2 system to differentiate between donor and recipient cells in erythroblasts. However, CD45 is not expressed from the CD235a+ stage of erythropoiesis onwards, so it is unclear how the authors are detecting essentially zero CD45-negative cells in the erythroblast compartment. This is quite odd and raises questions about the results. That being said, the red cell indices in the mice are the much more convincing data.

(4) The authors make heavy use of defining "erythroid gene" sets and "non-erythroid gene" sets, but it is unclear what those lists of genes actually are. This makes it hard to assess any claims made about erythroid and non-erythroid genes.

(5) Overall the data regarding condensate formation is difficult to interpret and is the weakest part of this paper. It is also unclear how studies of in vitro condensate formation or studies in 293T or K562 cells can truly relate to highly specialized erythroid biology. This does not detract from the major findings regarding genetic requirements of MED26 in erythropoiesis.

(6) For many figures, there are some panels where conclusions are drawn, but no statistical quantification of whether a difference is significant or not.

Reviewer #2 (Public review):

Summary:

The manuscript by Zhu et al describes a novel role for MED26, a subunit of the Mediator complex, in erythroid development. The authors have discovered that MED26 promotes transcriptional pausing of RNA Pol II, by recruiting pausing-related factors.

Strengths:

This is a well-executed study. The authors have employed a range of cutting-edge and appropriate techniques to generate their data, including: CUT&Tag to profile chromatin changes and mediator complex distribution; nuclear run-on sequencing (PRO-seq) to study Pol II dynamics; knockout mice to determine the phenotype of MED26 perturbation in vivo; an ex vivo erythroid differentiation system to perform additional, important, biochemical and perturbation experiments; immunoprecipitation mass spectrometry (IP-MS); and the "optoDroplet" assay to study phase-separation and molecular condensates.

This is a real highlight of the study. The authors have managed to generate a comprehensive picture by employing these multiple techniques. In doing so, they have also managed to provide greater molecular insight into the workings of the MEDIATOR complex, an important multi-protein complex that plays an important role in a range of biological contexts. The insights the authors have uncovered for different subunits in erythropoiesis will very likely have ramifications in many other settings, in both healthy biology and disease contexts.

Weaknesses:

There are almost no discernible weaknesses in the techniques used, nor the interpretation of the data. The IP-MS data was generated in HEK293 cells when it could have been performed in the human CD34+ HSPC system that they employed to generate a number of the other data. This would have been a more natural setting and would have enabled a more like-for-like comparison with the other data.

Reviewer #3 (Public review):

Summary:

The authors aim to explore whether other subunits besides MED1 exert specific functions during the process of terminal erythropoiesis with global gene repression, and finally they demonstrated that MED26-enriched condensates drive erythropoiesis through modulating transcription pausing.

Strengths:

Through both in vitro and in vivo models, the authors showed that while MED1 and MED26 co-occupy a plethora of genes important for cell survival and proliferation at the HSPC stage, MED26 preferentially marks erythroid genes and recruits pausing-related factors for cell fate specification. Gradually, MED26 becomes the dominant factor in shaping the composition of transcription condensates and transforms the chromatin towards a repressive yet permissive state, achieving global transcription repression in erythropoiesis.

Weaknesses:

In the in vitro model, the author only used CD34+ cell-derived erythropoiesis as the validation, which is relatively simple, and more in vitro erythropoiesis models need to be used to strengthen the conclusion.

Reviewer #2 (Public review):

Dipasree Hajra et al demonstrated that Salmonella was able to modulate the expression of Sirtuins (Sirt1 and Sirt3) and regulate the metabolic switch in both host and Salmonella, promoting its pathogenesis. The authors found Salmonella infection induced high levels of Sirt1 and Sirt3 in macrophages, which were skewed toward the M2 phenotype allowing Salmonella to hyper-proliferate. Mechanistically, Sirt1 and Sirt3 regulated the acetylation of HIF-1alpha and PDHA1, therefore mediating Salmonella-induced host metabolic shift in the infected macrophages. Interestingly, Sirt1 and Sirt3-driven host metabolic switch also had an effect on the metabolic profile of Salmonella. Counterintuitively, inhibition of Sirt1/3 led to increased pathogen burdens in an in vivo mouse model. Overall, this is a well-designed study.

The revised manuscript has addressed all of the previous comments. The re-analysis of flow cytometry and WB data by authors makes the results and conclusion more complete and convincing.

Reviewer #3 (Public review):

Summary:

In this paper Hajra et al have attempted to identify the role of Sirt1 and Sirt3 in regulating metabolic reprogramming and macrophage host defense. They have performed gene knock down experiments in RAW macrophage cell line to show that depletion of Sirt1 or Sirt3 enhances the ability of macrophages to eliminate Salmonella Typhimurium. However, in mice inhibition of Sirt1 resulted in dissemination of the bacteria but the bacterial burden was still reduced in macrophages. They suggest that the effect they have observed is due to increased inflammation and ROS production by macrophages. They also try to establish a weak link with metabolism. They present data to show that the switch in metabolism from glycolysis to fatty acid oxidation is regulated by acetylation of Hif1a, and PDHA1.

Strengths:

The strength of the manuscript is that the role of Sirtuins in host-pathogen interactions have not been previously explored in-depth making the study interesting. It is also interesting to see that depletion of either Sirt1 or Sirt3 result in a similar outcome.

Weaknesses:

The major weakness of the paper is the low quality of data, making it harder to substantiate the claims. Also, there are too many pathways and mechanisms being investigated. It would have been better if the authors had focussed on either Sirt1 or Sirt3 and elucidated how it reprograms metabolism to eventually modulate host response against Salmonella Typhimurium. Experimental evidences are also lacking to prove the proposed mechanisms. For instance they show correlative data that knock down of Sirt1 mediated shift in metabolism is due to HIF1a acetylation but this needs to be proven with further experiments.

Reviewer #1 (Public review):

Summary:

TMEM16, OSCA/TMEM63, and TMC belong to a large superfamily of ion channels where TMEM16 members are calcium activated lipid scramblases and chloride channels, whereas OSCA/TMEM63 and TMCs are mechanically activated ion channels. In the TMEM16 family, TMEM16F is a well characterized calcium activated lipid scramblase that play an important role in processes like blood coagulation, cell death signaling, and phagocytosis. In a previous study the group has demonstrated that lysine mutation in TM4 of TMEM16A can enable the calcium activated chloride channel to permeate phospholipids too. Based on this they hypothesize that the energy barrier for lipid scramblase in these ion channels is low, and that modification in the hydrophobic gate region by introducing a charged side chain between TM4/6 interface in TMEM16 and OSCA/TMEM63 family can allow lipid scramblase. In this manuscript, using scramblase activity via Annexin V binding to phosphatidylserine, and electrophysiology, the authors demonstrate that lysine mutation in TM4 of TMEM16F and TMEM16A can cause constitutive lipid scramblase activity. The authors then go on to show that analogous mutations in OSCA1.2 and TMEM63A can lead to scramblase activity. The revised version does a thorough characterization of residues that form the hydrophobic gate region in TM4/6 of this superfamily of channels. Their results indicated that disrupting the TM4/6 interaction can reduce energy barrier for this channels to scramblase lipids.

Strengths:

Overall, the authors introduce an interesting concept that this large superfamily can permeate ions and lipids.

Weaknesses:

none noted in the revised version.

Reviewer #2 (Public review):

This focused study by Lowry and colleagues that identifies a key molecular motif that controls ion permeation vs combined ion permeation and lipid transport in three families of channel/scramblase proteins, in TMEM16 channels, in the plant-expressed and stress-gated cation channel OSCA, and in the mammalian homolog and mechanosensitive cation channel, TMEM63. Between them, these three channels share low sequence similarity and have seemingly differing functions, as anion (TMEM16 channels), or stress-activated cation channels (OSCA/TMEM63). The study finds that in all three families, mutating a single hydrophobic residue in the ion permeation pathway of the channels confers lipid transport through the pores of the channels, indicating that TMEM16 and related OSCA and TMEM63 channels have a conserved potential for both ion and lipid permeation. The authors interpret the findings as revealing that these channel/scramblase proteins have a relatively low "energetic barrier for scramblase" activity. The experiments are done with a high level of rigor and the revised paper is very well written and addresses the previous concerns.

Reviewer #3 (Public review):

This study was focused on the conserved mechanisms across the Transmembrane Channel/Scramblase superfamily, which includes members of the TMEM16, TMEM63/OSCA, and TMC families. In previous work, the authors have studied the role of the inner activation gate of these proteins. Here, the authors show that the introduction of mutations at the TM4-TM6 interface, which are close to the inactivation gate, can disrupt gating and confer scramblase activity to non-scramblases proteins.

Overall, the confocal imaging experiments, patch clamping experiments, and data analysis are performed well and in line with standard methods. The molecular dynamics simulation work is focused but adds supportive evidence to their findings. Although there could have been more extensive molecular analysis to bolster the authors' arguments on the role of the TM4-TM6 interface (e.g. evaluate effects of size/hydrophobicity, double mutants, cross-linking, more in-depth simulation data), there is adequate evidence to conclude that certain residues at this interface is critical to ion conduction and phospholipid scramblase activity. The data presented only adds incremental depth of knowledge for each individual channel, but together, they show this to be true for conserved TM4 residues across TMEM16F, TMEM16A, OSCA1.2, and TMEM63A proteins. This breadth of data is a major strength of this paper, and provides strong evidence for a coupled pathway for ion conduction and phospholipid transport, though the underlying biophysical mechanism is still speculative and remains to be elucidated.

Reviewer #1 (Public review):

Summary:

The authors addressed the influence of DKK2 on colorectal cancer (CRC) metastasis to the liver using an orthotopic model transferring AKP-mutant organoids into the spleens of wild-type animals. They found that DKK2 expression in tumor cells led to enhanced liver metastasis and poor survival in mice. Mechanistically, they associate Dkk2-deficiency in donor AKP tumor organoids with reduced Paneth-like cell properties, particularly Lz1 and Lyz2, and defects in glycolysis. Quantitative gene expression analysis showed no significant changes in Hnf4a1 expression upon Dkk2 deletion. Ingenuity Pathway Analysis of RNA-Seq data and ATAC-seq data point to a Hnf4a1 motif as a potential target. They also show that HNF4a binds to the promoter region of Sox9, which leads to LYZ expression and upregulation of Paneth-like properties. By analyzing available scRNA data from human CRC data, the authors found higher expression of LYZ in metastatic and primary tumor samples compared to normal colonic tissue; reinforcing their proposed link, HNF4a was highly expressed in LYZ+ cancer cells compared to LYZ- cancer cells.

Strengths:

Overall, this study contributes a novel mechanistic pathway that may be related to metastatic progression in CRC.

Weaknesses:

The main concerns are related to incremental gains, missing in vivo support for several of their conclusions in murine models, and missing human data analyses.

Main comments

Novelty:<br /> The authors previously described the role of DKK2 in primary CRC, correlating increased DKK2 levels to higher Src phosphorylation and HNF4a1 degradation, which in turn enhances LGR5 expression and "stemness" of cancer cells, resulting in tumor progression (PMID: 33997693). A role for DKK2 in metastasis has also been previously described (sarcoma, PMID: 23204234)

Mouse data:<br /> (a) The authors analyzed liver mets, but the main differences between AKT and AKP/Dkk2 KO organoids could arise during the initial tumor cell egress from the intestinal tissue (which cannot be addressed in their splenic injection model), or during pre-liver stages, such as endothelial attachment. While the analysis of liver mets is interesting, given that Paneth cells play a role in the intestinal stem cell niche, it is questionable whether a study that does not involve the intestine can appropriately address this pathway in CRC metastasis.<br /> (b) The overall number of Paneth cells found in the scRNA-seq analysis of liver mets was low (17 cells, Fig.3), and assuming that these cells are driving the differences seems somewhat far-fetched.<br /> (c) Fig. 6 suggests a signaling cascade in which the absence of DKK2 leads to enhanced HNF4A expression, which in turn results in reduced Sox9 expression and hence reduced expression of Paneth cell properties. It is therefore crucial that the authors perform in vivo (splenic organoid injection) loss-of-function experiments, knockdown of Sox9 expression in AKP organoids, and Sox9 overexpression experiments in AKP/Dkk2 KO organoids to demonstrate Sox9 as the central downstream transcription factor regulating liver CRC metastasis.<br /> (d) Given the previous description of the role of DKK2 in primary CRC, it is important to define the step of liver metastasis affected by Dkk2 deficiency in the metastasis model. Does it affect extravasation, liver survival, etc.?

Human data:<br /> Can the authors address whether the expression of Dkk2 changes in human CRC and whether mutations in Dkk2 as correlated with metastatic disease or CRC stage?

Bioinformatic analysis<br /> GEO repositories remain not open (at the time of the re-review) and SRA links for raw data are still unavailable. Without access to raw data, it is not possible to verify the analyses or fully assess the results. A part of the article was made by re-analyzing public data so the authors should make even the raw available and not just the count tables

Reviewer #2 (Public review):

Summary:

The authors propose that DKK2 is necessary for the metastasis of colon cancer organoids. They then claim that DKK2 mediates this effect by permitting the generation of lysozyme-positive Paneth-like cells within the tumor microenvironmental niche. They argue that these lysozyme-positive cells have Paneth-like properties in both mouse and human contexts. They then implicate HNF4A as the causal factor responsive to DKK2 to generate lysozyme-positive cells through Sox9.

Strengths:

The use of a genetically defined organoid line is state-of-the-art. The data in Figure 1 and the dependence of DKK2 for splenic injection and liver engraftment, as well as the long-term effect on animal survival, are interesting and convincing. The rescue using DKK2 administration for some of their phenotype in vitro is good. The inclusion and analysis of human data sets help explore the role of DKK2 in human cancer and help ground the overall work in a clinical context.

Remaining Weaknesses after revision:

(1) The authors have effectively explained the regulation of HNF4A at both mRNA and protein levels. To further strengthen their findings, I recommend using CRISPR technology to generate DKK2 and HNF4A double knockout organoids. This approach would allow the authors to investigate whether the AKP liver metastasis is restored in the double knockout condition. Such an experiment would provide more direct evidence that HNF4A protein stabilization is the crucial mechanism for liver metastasis suppression following DKK2 knockout.

Reviewer #1 (Public review):

Summary:

The author developed a new device to overcome current limitations in the imaging process of 3D spheroidal structures. In particular, they created a system to follow in real-time tumour spheroid formation, fusion and cell migration without disrupting their integrity. The system has also been exploited to test the effects of a therapeutic agent (chemotherapy) and immune cells.

Comments on revised version:

The authors well addressed all my concerns. It is a wonderful design to view the 3D cell spheroids.

Reviewer #2 (Public review):

Summary:

The author developed a new device to overcome current limitations in the imaging process of 3D spheroidal structures. In particular, they created a system to follow in real-time tumour spheroid formation, fusion and cell migration without disrupting their integrity. The system has also been exploited to test the effects of a therapeutic agent (chemotherapy) and immune cells.

Strengths:

The system allows the in situ observation of the 3D structures along the 3 axes (x,y and z) without disrupting the integrity of the spheroids; in a time-lapse manner it is possible to follow the formation of the 3D structure and the spheroids fusion from multiple angles, allowing a better understanding of the cell aggregation/growth and kinetic of the cells.

Interestingly the system allows the analysis of cell migration/ escape from the 3D structure analysing not only the morphological changes in the periphery of the spheroids but also from the inner region demonstrating that the proliferating cells in the periphery of the structure are more involved in the migration and dissemination process. The application of the system in the study of the effects of doxorubicin and NK cells would give new insights in the description of the response of tumor 3D structure to killing agents.

Reviewer #2 (Public review):

This study presents valuable insight on how neurons within the central amygdala may broadly encode the valence of emotional stimuli. The evidence supporting most of the authors' conclusion is solid, although some of the claims should be treated with caution due to potential alternative interpretation of the data.

In this revised manuscript the authors have addressed the reviewers' critiques in a way that acknowledges the feedback but does not fully embrace or rigorously address the reviewers' core concerns. Here are the main observations that support this impression:

(1) The authors repeatedly acknowledge the ambiguity in defining "valence" and "salience" in the literature, but their responses don't clarify how they address these terms more rigorously. They seem to justify their operational definitions by citing previous studies but do not address how their definitions impact the clarity and robustness of their findings.

(2) The reviewers highlighted that using stimuli from different sensory modalities without scaling them or including neutral cues limits the ability to distinguish between valence and salience. The authors acknowledge this but argue that using same-modality stimuli would not produce distinct responses. This response doesn't address the reviewers' point about how these design limitations could weaken the conclusions. They seem to rely on citations of similar experimental designs instead of addressing the core critique or proposing additional experiments.

(3) In response to the low number of cue-responsive units and the call for more rigorous behavioral measures (like licking or orienting), the authors provide some data but emphasize statistical rigor over behavioral insights, which was questioned during the initial review. They don't propose any methodological adjustments or consider alternative explanations.

(4) The reviewers suggested clustering or other population-level analyses to understand functional diversity within the central amygdala. The authors argue that their statistical approach was sufficient and don't believe additional clustering analyses would add value. This response seems dismissive, as they don't consider whether population-level insights might reveal patterns that single-cell responses overlook.

Overall, while the authors have responded to each concern, their rebuttals often reference other studies to justify their choices rather than addressing the specific limitations highlighted by the reviewers.

Reviewer #3 (Public review):

Summary:

The authors have performed endoscopic calcium recordings of individual CeA neuron responses to food and shock, as well as to cues predicting food and shock. They claim that a majority of neurons encode valence, with a substantial minority encoding salience.

Strengths:

The use of endoscopic imaging is valuable, as it provides the ability to resolve signals from single cells, while also being able to track these cells across time (though the latter capability was not extensively utilized). Another strength is the use of a sophisticated circular shifting analysis to avoid statistical errors caused by correlations between neighboring image pixels.

Weaknesses:

In the first version of this manuscript, my main critique was that the authors didn't fully test whether neurons encode valence. In their rebuttal, the authors justify their use of the terms valence and salience by citing prior works from different labs:

(1) Li et al., 2019, doi: 10.7554/eLife.41223<br /> (2) Yang et al., 2023, doi: 10.1038/s41586-023-05910-2<br /> (3) Huang et al., 2024, doi: 10.1038/s41586-024-07819<br /> (4) Lin and Nicolelis, 2008, doi: 10.1016/j.neuron.2008.04.031<br /> (5) Stephenson-Jones et al., 2020, doi: 10.1016/j.neuron.2019.12.006<br /> (6) Zhu et al., 2018, doi: 10.1126/science.aat0481<br /> (7) Comoli et al., 2003, doi: 10.1038/nn1113P

Among these, items #1 and #3 primarily discuss valence, while #2, #4, #6, and #7 discuss salience, and #5 discusses both.

Upon reviewing these references, the authors' identification of valence encoding patterns is still problematic, and indeed studies cited above show several lines of evidence for valence encoding that are absent here. For example, item #3 ranked behavioral responses to five different odors in drosophila, from most attractive to most repulsive, and saw neuronal responses correlated with the degree of attraction versus repulsion across all five odors. This is robust evidence for valence encoding that is absent here. Items #1 and #5 above are the other two valence-addressing studies cited, and although those only used one rewarding and one aversive stimulus (in rodents), both also added a neutral cue, and most critically, identified substantial subsets of neurons showing a rank-order response, e.g. either aversion > neutral > reward or aversion < neutral < reward. Again, that level of demonstration of valence encoding is not shown in the current study.

Finally, two of the valence studies above tested responses to omission of reward/punishment, providing yet more evidence of valence encoding that is absent in the current study.

While there is much to like about the current study, the claims of valence encoding appear hard to justify, and should be toned down.

Reviewer #1 (Public review):

The authors present an important work where they model some of the complex interactions between immune cells, fibroblasts and cancer cells. The model takes into account the increased ECM production of cancer-associated fibroblasts. These fibres trap the cancer but also protect it from immune system cells. In this way, these fibroblasts' actions both promote and hinder cancer growth. By exploring different scenarios, the authors can model different cancer fates depending on the parameters regulating cancer cells, immune system cells and fibroblasts. In this way, the model explores non-trivial scenarios. An important weakness of this study is that, though it is inspired by NSCLC tumors, it is still far from modelling tumor lesions with morphologies similar to NSCLC tumors and does not explore the formation of ramified tumors. In this way, is a general model and it is challenging how it can be adapted to simulate more realistic tumor morphologies.

Comments on revisions:

The authors have improved the manuscript and addressed my concerns.

Reviewer #2 (Public review):

Summary:

The authors develop a computational model (and a simplified version thereof) to treat an extremely important issue regarding tumor growth. Specifically, it has been argued that fibroblasts have the ability to support tumor growth by creating physical conditions in the tumor microenvironment that prevent the relevant immune cells from entering into contact with, and ultimately killing, the cancer cells. This inhibition is referred to as immune exclusion. The computational approach follows standard procedures in the formulation of models for mixtures of different material species, adapted to the problem at hand by making a variety of assumptions as to the activity of different types of fibroblasts, namely "normal" versus "cancer-associated". The model itself is relatively complex, but the authors do a convincing job of analyzing possible behaviors and attempting to relate these to experimental observations.

Strengths:

As mentioned, the authors do an excellent job of analyzing the behavior of their model both in its full form (which includes spatial variation of the concentrations of the different cellular species) and in its simplified mean field form. The model itself is formulated based on established physical principles, although the extent to which some of these principles apply to active biological systems is perhaps debatable (see Weaknesses). The results of the model do indeed offer some significant insights into the critical factors which determine how fibroblasts might affect tumor growth; these insights could lead to new experimental ways of unraveling these complex sets of issues and enhancing immunotherapy. In this revised version, the authors have properly placed this work within the general context of other research on modeling the tumor-immune ecology.

Weaknesses:

Models of the form being studied here rely on a large number of assumptions regarding cellular behavior. One major issue is the degree to which close-to-equilibrium assumptions (such as the dynamics being driven by free energy minimization) can be taken as reliable predictors of the obviously active dynamics of biological cells. The authors have recognized this conceptual issue and have argued that these assumptions provide a reasonable first step for understanding the full complexity of dynamics in the tumor microenvironment.

The problem of T cell infiltration as well as the patterning of the extracellular matrix (ECM) by fibroblasts necessarily involve understanding cell proliferation, cell motion and cell interactions due e.g. to cell signaling. There is evidence that inherently non-equilibrium interactions between the fibroblasts and the extracellular matrix can lead to patterning of the fiber network and trapping of potentially infiltrating T-cells. it is not clear the extent to which this type of interaction can be captured by the approach being used here, although the authors propose that they can be mimicked by proper terms in their formulation. This to me is the primary concern that I had with this paper.

The authors have now addressed what used to be a separate weakness concerning the assumption that fibroblasts affect T cell behavior primarily by just making a more dense ECM. Instead, the organization of the ECM (for example, its anisotropy) could be playing a much more essential role than is given credit for here. This possibility is now discussed in some detail and the authors have suggested that the introduction of a nematic order parameter field would be a useful way to treat this effect.

Reviewer #1 (Public review):

Summary:

The authors created a transgenic mouse line to read out integrated stress responses with single-cell resolution.

Strengths:

ISR plays an important role in the development, maintenance, and degeneration of the nervous system. This mouse line represents a potentially important tool to understand ISR in situ.

Weaknesses:

The current manuscript is clearly written. However, more validation experiments should be performed to understand the exact meaning of the fluorescence intensity of GFP and RFP channels. This is important because these results will define how this tool will be used in the future and in the field.

Reviewer #2 (Public review):

Summary:

In this paper, the authors create transgenic animals with a CMV promoter driving expression of their DIO-SPOTlight construct in which uORF2 and the authentic ORF of Atf4 are replaced by GFP and tdTomato respectively, such that ISR activation is predicted to diminish GFP expression and enhance RFP expression. The major experimental finding of the paper is that cholinergic neurons have the most robust activation of the reporter, consistent with and extending upon their previous work.

Strengths:

It is very likely that the reporter does indeed read out on ISR activation at some level. It is mostly likely to be useful for screening and hypothesis testing than for gaining mechanistic insight, because, as the authors note in the present version, ATF4 itself is but one component of ISR activation. Cells might have robust eIF2a phosphorylation but have suppressed translational regulation (for instance by regulating the expression of eIF2B). The mRNA and protein half-lives of the GFP and Tomato are likely quite different from that of the equivalent components in ATF4, which means that the reporter is likely to behave differently from ATF4 itself over time.

Weaknesses:

The major element that the current manuscript lacks is a detailed comparison between how the reporter behaves and how it tracks with eIF2a phosphorylation, ATF4, and the initiation of the gene expression program downstream of ATF4. While this would be difficult to do in vivo, it would seem much more feasible to isolate primary cells (neurons, fibroblasts, hepatocytes, etc.) from the animals and thoroughly characterize the kinetics of reporter-versus-ISR activation. In that way, the reader can have a better idea of how to interpret the behavior of the reporter. As it is, the authors' attempt to account for the reporter's behavior in Figure 3F is purely speculative and not backed by experiment or modeling.

Reviewer #3 (Public review):

Summary:

The previously described reporter SPOTlight is a fluorescence-based reporter of the integrated stress response, specifically, protein synthesis initiation dynamics. In the current study from the same lab, the authors describe the creation and characterization of a transgenic mouse that expresses SPOTlight.

Strengths:

The previously described reporter has now been made into a Cre-dependent transgene in mice. The authors replicate previous findings from their lab that were acquired using viral vector-mediated delivery of their reporter.

Weaknesses:

There is not a clear advantage to having the Cre-dependent SPOTlight reporter in a transgenic mouse over using a viral vector to deliver the same Cre-dependent SPOTlight based on the experiments presented. There are potential general advantages and disadvantages to virus vs transgenic mouse but no side-by-side comparisons are performed here.

It is not clear whether overexpressing the reporter alters basal ISR/UPR function and gene expression. The CAG is a strong promoter and overexpression of fluorescent proteins (or any protein) can potentially stress protein synthesis and processing mechanisms. The use of the animal as a reporter may be misleading if the presence of the reporter is already altering ISR/UPR.

Reviewer #1 (Public review):

Summary:

In organisms with an open mitosis, nuclear envelope breakdown at mitotic entry and re-assembly of the nuclear envelope at the end of mitosis are important, highly regulated processes. One key regulator of nuclear envelope re-assembly is the BAF (Barrier-to-Autointegration) protein, which contributes to cross-linking of chromosomes to the nuclear envelope. Crucially, BAF has to be in a dephosphorylated form to carry out this function, and PP2A has been shown to be the phosphatase which dephosphorylates BAF. The Ankle2/LEM4 protein has previously been identified as an important regulator of PP2A in the dephosphorylation of BAF but its precise function is not fully understood, and Li and colleagues set out to investigate the function of Ankle2/LEM4 in both Drosophila flies and Drosophila cell lines.

Strengths:

The authors use a combination of biochemical and imaging techniques to understand the biology of Ankle2/LEM4. On the whole the experiments are well conducted and the results look convincing. A particular strength of this manuscript is that the authors are able to study both cellular phenotypes and organismal effects of their mutants by studying both Drosophila D-mel cells and whole flies.<br /> The work presented in this manuscript significantly enhances our understanding of how Ankle2/LEM4 supports BAF dephosphorylation at the end of mitosis. Particularly interesting is finding that Ankle2/LEM4 appears to be a bona fide PP2A regulatory protein in Drosophila, as well as the localisation of Ankle2/LEM4 and how this is influenced by the interaction between Ankle2 and the ER protein Vap33. It would be interesting to see, though, whether these insights are conserved in mammalian cells, e.g. does mammalian Vap33 also interact with LEM4? Is LEM4 also a part of the PP2A holoenzyme complex in mammalian cells?

Weaknesses:

This work is certainly impactful but more discussion and comparison of the Drosophila versus mammalian cell system would be helpful. Also, to attract the largest possible readership, the Ankle2 protein should be referred to as Ankle2/LEM4 throughout the paper to make it clear that this is the same molecule.

A schematic model at the end of the final figure would be very useful to summarise the findings.

Comments on revisions:

The authors have carefully revised the manuscripts and have satisfactorily addressed the issues that were raised by the reviewers.

Reviewer #2 (Public review):

The authors first identify Ankle2 as a regulatory subunit and direct interactor of PP2A, showing they interact both in vitro and in vivo to promote BAF dephosphorylation. The Ankyrin domain of Ankle2 is important for the interaction with PP2A. They then show Ankle2 also interacts with the ER protein Vap33 through FFAT motifs and they particularly co-localize during mitosis. The recruitment of Ankle2 to Vap33 is essential to ER and nuclear envelop membrane in telophase while earlier in mitosis, it relies on the C terminus but not the FFAT motifs for recruitments to the nuclear membrane and spindle envelop in early mitosis. The molecular determinants and receptors are currently not known. The authors check the function of the PP2A recruitment to Ankle2/Vap33 in the context of embryos and show this recruitment pathway is functionally important. While the Ankle2/Vap33 interaction is dispensable in adult flies -looking at wing development, the PP2A/Ankle2 interaction is essential for correct wing and fly development. Overall, this is a very complete paper that reveals the molecular mechanism of PP2A recruitment to Ankle2 and studies both the cellular and the physiological effect of this interaction in the context of fly development.

The paper is well-written and the narrative is well developed. The figures are of high quality, well-controlled, clearly labelled and easy to understand. They support the claims made by the authors.

Comments on revisions:

There are still issues with the statistics. On graphs where multiple conditions are shown, you cannot perform a T-test. You have to use other tests such as ANOVA if the data is normal, and other tests such as KS test if the data is not normally distributed.

Reviewer #3 (Public review):

The authors were interested in how Ankle2 regulates nuclear envelope reformation after cell division. They show that Ankle2 can bind in a PP2A complex without other known regulatory subunits of PP2A. The authors also identity a novel interaction with ER protein Vap33 that could be important for localization. This manuscript is a useful finding linking Ankle2 function during nuclear envelope reformation to the PP2A complex. The authors present solid data showing that Ankle2 can form a complex with PP2A-29B and Mts and generate a phosphoproteomic resource that is fundamentally important to understand Ankle2 biology. The caveat should be remembered that most experiments, including subcellular localization, are based on overexpression data. Keeping this in mind, the manuscript is a valuable resource.

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 #3 (Public review):

The manuscript by Goyal et al report substrate-bound and substrate-free structures of a tripartite ATP independent periplasmic (TRAP) transporter from a previously uncharacterized homolog, F. nucleatum. This is one of most mechanistically fascinating transporter families, by means of its QM domain (the domain reported in his manuscript) operating as a monomeric 'elevator', and its P domain functioning as a substrate-binding 'operator' that is required to deliver the substrate to the QM domain; together, this is termed an 'elevator with an operator' mechanism. Remarkably, previous structures had not demonstrated the substrate Neu5Ac bound. In addition, they confirm the previously reported Na+ binding sites, and report a new metal binding site in the transporter, which seems to be mechanistically relevant. Finally, they mutate the substrate binding site and use proteoliposomal uptake assays to show the mechanistic relevance of the proposed substrate binding residues.

Strengths:

The structures are of good quality, the presentation of the structural data has improved, the functional data is robust, the text is well-written, and the authors are appropriately careful with their interpretations. Determination of a substrate bound structure is an important achievement and fills an important gap in the 'elevator with an operator' mechanism.

Weaknesses:

Although the possibility of the third metal site is compelling, I do not feel it is appropriate to model in a publicly deposited PDB structure without directly confirming experimentally. The authors do not extensively test the binding sites due to technical limitations of producing relevant mutants; however, their model is consistent with genetic assays of previously characterized orthologs, which will be of benefit to the field.

Reviewer #1 (Public review):

Summary:

In this paper, the authors present an interesting strategy to interfere with the HBV life cycle: the preparation of geranyl and peptides' dimers that could impede the correct assembly of hepatitis B core protein HBc into viable capsids. These dimers are of different nature, depending on the HBc site the authors plan to target. A preliminary study with geranyl dimers (targeting a hydrophobic site of HBc) was first investigated. The second series deals with peptide-PEG linker-peptide dimers, targeting the tips of HBc dimer spikes.

Strengths:

This work is very well conducted, combining ITC experiments (for determination of dimers' KD), cellular effects (thanks to the grafting of previously developed dimers with polyarginine-based cell penetrating peptide) HBV infected HEK293 cells and Cryo-EM studies.<br /> The findings of these research teams unambiguously demonstrated the interest of such dimeric structures in impeding the correct HBV life cycle and thus, could bring solutions in the control of its development. Ultimately, a new class of HBV Capside Assembly Modulators could arise from this study.<br /> There is no doubt that this work could bring very interesting information for people working on VHB.

Comments on revisions:

Minor corrections have been made in this revised version of this work, according to the remarks of the reviewers.

Reviewer #2 (Public review):

Summary:

Vladimir Khayenko et al. discovered two novel binding pockets on HBc with in vitro binding and electron microscopy experiments. While the geranyl dimer targeting a central hydrophobic pocket displayed a micromolar affinity, the P1-dimer binding to the spike tip of HBc has a nanomolar affinity. In the turbidity assay and at the cellular level, an HBc aggregation from peptide crosslinking was demonstrated.

Strengths:

The study identifies two previously unexplored binding pockets on HBc capsids and develops novel binders targeting these sites with promising affinities.

Weaknesses:

While the in vitro and cellular HBc aggregation effects are demonstrated, the antiviral potential against HBV infection is not directly evaluated in this study.

Reviewer #1 (Public Review):

Summary:

In this manuscript, "PAbFold: Linear Antibody Epitope Prediction using AlphaFold2", the authors generate a python wrapper for the screening of antibody-peptide interactions using AlphaFold, and test the performance of AlphaFold on 3 antibody-peptide complexes. In line with previous observations regarding the ability of AlphaFold to predict antibody structures and antigen binding, the results are mixed. While the authors are able to use AlphaFold to identify and experimentally validate a previously characterized broad binding epitope with impressive precision, they are unable to consistently identify the proper binding registers for their control [Myc-tag, HA-tag] peptides. Further, it appears that the reproducibility and generality of these results are low, with new versions of AlphaFold negatively impacting the predictive power. However, if this reproducibility issue is solved, and the test set is greatly increased, this manuscript could contribute strongly towards our ability to predict antibody-antigen interactions.

Strengths:

Due to the high significance, but difficulty, of the prediction of antibody-antigen interactions, any attempts to break down these predictions into more tractable problems should be applauded. The authors' approach of focusing on linear epitopes (peptides) is clever, reducing some of the complexities inherent to antibody binding. Further, the ability of AlphaFold to narrow down a previously broadly identified experimental epitope is impressive. The subsequent experimental validation of this more precisely identified epitope makes for a nice data point in the assessment of AlphaFold's ability to predict antibody-antigen interactions.

Weaknesses:

Without a larger set of test antibody-peptide interactions, it is unclear whether or not AlphaFold can precisely identify the binding register of a given antibody to a given peptide antigen. Even within the small test set of 3 antibody-peptide complexes, performance is variable and depends upon the scFv scaffold used for unclear reasons. Lastly, the apparent poor reproducibility is concerning, and it is not clear why the results should rely so strongly on which multi-sequence alignment (MSA) version is used, when neither the antibody CDR loops nor the peptide are likely to strongly rely on these MSAs for contact prediction.

Major Point-by-Point Comments:

(1) The central concern for this manuscript is the apparent lack of reproducibility. The way the authors discuss the issue (lines 523-554) it sounds as though they are unable to reproduce their initial results (which are reported in the main text), even when previous versions of AlphaFold2 are used. If this is the case, it does not seem that AlphaFold can be a reliable tool for predicting antibody-peptide interactions.

(2) Aside from the fundamental issue of reproducibility, the number of validating tests is insufficient to assess the ability of AlphaFold to predict antibody-peptide interactions. Given the authors' use of AlphaFold to identify antibody binding to a linear epitope within a whole protein (in the mBG17:SARS-Cov-2 nucleocapsid protein interaction), they should expand their test set well beyond Myc- and HA-tags using antibody-antigen interactions from existing large structural databases.

(3) As discussed in lines 358-361, the authors are unsure if their primary control tests (antibody binding to Myc-tag and HA-tag) are included in the training data. Lines 324-330 suggest that even if the peptides are not included in the AlphaFold training data because they contain fewer than 10 amino acids, the antibody structures may very well be included, with an obvious "void" that would be best filled by a peptide. The authors must confirm that their tests are not included in the AlphaFold training data, or re-run the analysis with these templates removed.

(4) The ability of AlphaFold to refine the linear epitope of antibody mBG17 is quite impressive and robust to the reproducibility issues the authors have run into. However, Figure 4 seems to suggest that the target epitope adopts an alpha-helical structure. This may be why the score is so high and the prediction is so robust. It would be very useful to see along with the pLDDT by residue plots a structure prediction by residue plot. This would help to see if the high confidence pLDDT is coming more from confidence in the docking of the peptide or confidence in the structure of the peptide.

(5) Related to the above comment, pLDDT is insufficient as a metric for assessing antibody-antigen interactions. There is a chance (as is nicely shown in Figure S3C) that AlphaFold can be confident and wrong. Here we see two orange-yellow dots (fairly high confidence) that place the peptide COM far from the true binding region. While running the recommended larger validation above, the authors should also include a peptide RMSD or COM distance metric, to show that the peptide identity is confident, and the peptide placement is roughly correct. These predictions are not nearly as valuable if AlphaFold is getting the right answer for the wrong reasons (i.e. high pLDDT but peptide binding to a non-CDR loop region). Eventual users of the software will likely want to make point mutations or perturb the binding regions identified by the structural predictions (as the authors do in Figure 4).

Comments on revisions:

I have read the author's responses and the revised manuscript. The authors did not sufficiently address my comments, nor the fundamental issue with the manuscript.

By the authors' own admission, many of the results presented in the current version of the manuscript cannot be reproduced without relying on locally saved MSAs. In other words, there is almost no evidence presented that this pipeline will predict antibody-antigen interactions using currently publicly available software. This manuscript is reduced to essentially a case study (N=1) in how one might go about making such predictions coupled with pretty good experimental evidence backing up this singular prediction.

Reviewer #2 (Public Review):

Summary:

The authors showed the applicability and usefulness of a new AlphaFold2 pipeline called PabFold, which can predict linear antibody epitopes (B-cell epitopes) that can be helpful for the selection of reagents to be applied in competitive ELISA assay.

Strengths:

The authors showed the accuracy of the pipeline to identify correctly the binding epitope for three different antibody-antigen systems (Myc, HA, and Sars-Cov2 nucleocapsid protein). The design of scFvs from Fab of the three antibodies to speed up the analysis time is extremely interesting.

Weaknesses:

The article justifies correctly the findings and no great weaknesses are present. However, it could be useful for a broader audience to show in detail how pLDDT was calculated for both Simple-Max approach (per residue-pLDDT) and Consensus analysis ( average pLDDT for each peptide), with associated equations.

Comments on revisions:

I have read the author's responses to my comments and the revised paper. They addressed the minor comments and concerns. However, I agree with Reviewer #1 that these findings cannot be reproduced without local MSAs and this is a major issue.